Review of Economic Studies | Macro Paper Warehouse

A Model of Multiple Hypothesis Testing

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops an economic framework for determining when and how much multiple hypothesis testing (MHT) adjustment is warranted in research settings. The research question is: under what conditions do MHT adjustments arise as an optimal solution to incentive misalignment between a researcher and a mechanism designer (social planner)?

The model is a two-stage game. In the first stage, a benevolent social planner commits to a hypothesis testing protocol. In the second stage, a researcher decides whether to conduct a pre-specified experiment based on private costs and benefits. The planner’s utility function combines an ambiguity-averse (maximin) component—limiting harm from mistaken conclusions—with an expected-utility component capturing the generic benefits of research production. The framework focuses on multiplicity arising from testing multiple treatments or estimating effects within multiple subpopulations; multiple outcomes are treated as an economically distinct case covered in a companion paper.

The main theoretical result is that separate t-tests are uniformly globally optimal under linearity of the researcher’s payoff and welfare functions and normality of test statistics. The optimal critical value takes the explicit form: t(J, Σ) = Φ⁻¹(1 − C(J, Σ) / (b · |J|)), where |J| is the number of hypotheses, C(J, Σ) is the experiment cost, and b is the researcher’s per-rejection benefit. This formula nests two limiting cases. When costs are fully fixed (invariant to |J|), the formula delivers a Bonferroni correction. When costs scale proportionally with the number of hypotheses, no MHT adjustment is warranted—because the researcher already faces sufficient deterrent from the incremental cost of each additional test.

The key economic mechanism is as follows. In the worst states of the world (where all treatments are harmful relative to the status quo), a research study has only downside risk for society. The planner must keep the researcher’s expected payoff from false positives low enough that she chooses not to experiment. If critical values were invariant to |J|, for sufficiently many hypotheses the researcher’s expected payoff from false positives alone would exceed costs, inducing unwanted experimentation. Some upward adjustment to critical values (i.e., tighter thresholds) is therefore generically optimal. The same logic implies that critical values should also adjust for sample size, since larger samples raise costs.

The framework is calibrated to two empirical applications. For FDA clinical trial approval, using Sertkaya et al. (2016) data on approximately 31,000 U.S. pharmaceutical trials (2004–2012), fixed costs constitute approximately 46% of average total trial cost. At a benchmark significance level of 5% and benchmark sample size, the optimal level is approximately 3.2% for two tests, 2.6% for three tests, and asymptotes to approximately 1.4% as |J| → ∞. Sidak’s correction yields 2.5% and 1.7% for two and three tests respectively, and tends to zero as |J| → ∞—more conservative than the model implies. Optimal adjustments must also be less conservative for larger samples to preserve researcher incentives to bear the correspondingly larger costs.

For program evaluation in development economics, the paper uses a unique dataset of funding proposals submitted to J-PAL from 2009 to 2021. The estimated cost elasticity with respect to the number of treatment arms ranges from 0.13 to 0.22 (p < 0.05), indicating costs rise significantly but far less than proportionally. The implied optimal significance levels are slightly less conservative than Bonferroni/Sidak corrections but more conservative than unadjusted testing.

Scope conditions: the framework assumes pre-specified experiments (no p-hacking), linear payoffs, normally distributed statistics, and a researcher whose preferences are common knowledge. The analysis focuses on multiple treatments and subpopulations, not multiple outcomes. Results extend to imperfectly informed researchers and heterogeneous variances.

Q: What is the core mechanism by which MHT adjustments arise as optimal in this framework? A: The planner must deter experimentation in the worst-case states—those where all treatments are harmful. If the testing protocol did not adjust for the number of hypotheses, a researcher testing sufficiently many hypotheses could earn enough expected payoff from false positives alone to justify experimentation, even when all treatments are truly harmful. Tighter critical values (higher thresholds) reduce the probability of false positives and thus cap the researcher’s expected payoff in the null space, deterring unwanted experimentation. This is the maximin optimality condition: the researcher’s expected payoff must be non-positive over the null space.

Q: What are the two limiting cases of the optimal critical value formula, and what do they correspond to? A: The optimal level of the separate t-tests is α(J, Σ) = C(J, Σ) / (b · |J|). When C(J, Σ) = ᾱ (costs are fixed, invariant to the number of hypotheses), this reduces to ᾱ/|J|, the Bonferroni correction. When C(J, Σ) = ᾱ · |J| (costs scale proportionally with the number of hypotheses), the optimal level equals ᾱ regardless of |J|—no MHT adjustment is warranted. The intuition for the second case is that proportional costs already deter excess testing; the researcher has no undue incentive to test many hypotheses because each additional test costs the same incremental amount.

Q: Why do optimal critical values also depend on sample size, and what is the policy implication? A: Since research costs C(J, Σ) increase with sample size (Σ captures design features including sample size), the optimal test level α(J, Σ) = C(J, Σ)/(b·|J|) rises with sample size. Equivalently, larger studies warrant less conservative significance thresholds. The policy implication is that a single uniform correction (e.g., Bonferroni at the 5% level) applied without regard to sample size is suboptimal: it is too conservative for large studies, which would over-deter valuable high-powered research.

Q: What are the two optimality properties required of protocols in the paper’s main characterization? A: The paper shows (Proposition 3.1) that a protocol is uniformly globally optimal—optimal for all values of the welfare weight λ and prior π—if and only if it is both maximin optimal and unbiased. Maximin optimality (Proposition 3.2) requires two conditions: the researcher’s expected payoff must be non-positive over the null space (deterring experimentation when all treatments are harmful), and expected welfare must be non-negative when some treatments are beneficial. Unbiasedness requires that the researcher’s maximum power strictly exceeds the test size, ensuring that experimentation is motivated when treatments are genuinely beneficial.

Q: How does the paper rationalize conventional hypothesis testing asymmetry (type I vs. type II error weighting) without extreme restrictions? A: In Tetenov (2012), justifying 5%-level testing with minimax regret in a single-agent model requires the decision-maker to place 102 times more weight on type I than type II regret—an extreme restriction. In this paper, the asymmetry arises naturally from the planner’s desire to prevent harmful treatment implementation: the planner is willing to forgo some power (probability of detecting beneficial treatments) to ensure that harmful treatments are not implemented. The researcher’s private incentives and the planner’s objective diverge in a way that makes tight size control endogenously optimal.

Q: What does the FDA empirical calibration imply quantitatively about optimal versus standard adjustments? A: Using Sertkaya et al. (2016) data showing that fixed costs are 46% of average total trial cost for U.S. pharmaceutical trials, and using Pocock et al. (2002) to set J̄ = 3 (average number of subgroups), the paper calculates that at a benchmark level of ᾱ = 0.05: the optimal level is approximately 3.2% for two tests, 2.6% for three tests, and asymptotes to approximately 1.4% as |J| → ∞. By contrast, Sidak’s correction yields 2.5%, 1.7%, and zero, respectively. Both the unadjusted 5% and the Sidak/Bonferroni levels are therefore suboptimal—the unadjusted level is too permissive while standard FWER corrections are too conservative.

Q: What do the J-PAL data reveal about optimal MHT adjustment in program evaluation? A: Using the universe of J-PAL funding proposals from 2009 to 2021, the paper estimates the cost elasticity with respect to the number of treatment arms to be 0.13–0.22, which is statistically significant (p < 0.05) but far below 1 (the proportional case). This means costs rise with arms but much less than proportionally. As a result, optimal significance levels for program evaluation studies are slightly less conservative than Sidak/Bonferroni corrections (e.g., approximately 3.8–4.5% versus 2.5% at a two-arm study with ᾱ = 5%) but more conservative than unadjusted testing. The testing thresholds also vary moderately with sample size, with larger samples implying less conservative procedures.

Q: When are cross-study MHT adjustments warranted according to the framework? A: Cross-study MHT adjustments are warranted only when there are cost complementarities across those studies. If studies are conducted independently with separate cost structures, each study’s costs do not depend on the number of hypotheses tested in other studies, so no cross-study adjustment is optimal. This provides a principled resolution to the disputed question of whether researchers should correct for tests performed in other papers.

Q: When is FWER control (e.g., Bonferroni or Sidak) the appropriate form of MHT adjustment? A: Appendix B.2 shows that FWER control is appropriate when the researcher’s payoff is nonlinear—specifically when the researcher requires at least one positive finding to receive any benefit (e.g., to publish). In the baseline linear payoff model, average size control (Bonferroni) is the correct adjustment only when all costs are fixed. The broader insight is that the form of compound error control—whether average error rate or FWER—is itself determined by economic fundamentals rather than being a statistical choice made in advance.

Q: How does the paper extend to cases of heterogeneous variances across hypotheses? A: Proposition 5.2 shows that under heterogeneous variances, the optimal protocol uses separate t-tests based on sample-equalizing allocations—dividing the sample equally across treatment arms—with critical values t*(J, n(J)) = Φ⁻¹(1 − C(J, n(J))/(b·|J|)), where n(J) is the total sample size. This protocol remains maximin optimal and unbiased, preserving the main qualitative results.

Q: What does the paper contribute relative to Tetenov (2016) on single-hypothesis testing? A: Tetenov (2016) showed that in the single-hypothesis case, separate t-tests are maximin optimal and uniformly most powerful (UMP) unbiased. This paper extends that result to multiple hypotheses, but two major complications arise: first, maximin optimality in the multi-hypothesis case requires verifying that welfare is non-negative even when treatment effects have opposite signs, which requires a non-trivial argument absent in the single-hypothesis case; second, no protocol is UMP unbiased in the multi-hypothesis case, so the paper develops a weaker notion of unbiasedness (power exceeding size) that is sufficient to motivate experimentation.

Q: Why do multiple outcomes require different procedures than multiple treatments or subpopulations? A: Multiple outcomes and multiple treatments are economically distinct types of multiplicity. For multiple outcomes that are noisy proxies for a common underlying quantity, the optimal rule tests an index formed using statistical weights (as in Anderson, 2008). When outcomes capture distinct components of the planner’s utility, economic weights are appropriate. In contrast, multiple treatments or subpopulations lead to separate t-tests with cost-adjusted critical values. Conflating these two forms of multiplicity leads to incorrect inferences about what procedures are appropriate.

Maximin optimality: A hypothesis testing protocol is maximin optimal if it maximizes the planner’s worst-case welfare across all parameter values, equivalent to two conditions: deterring researcher experimentation over the null space (where all treatments are harmful), and ensuring non-negative expected welfare when some treatments are beneficial.

Unbiasedness (in the paper’s sense): A protocol is unbiased if the researcher’s maximum achievable power strictly exceeds the test size, ensuring that experimentation is motivated when treatments are genuinely beneficial. This is a weaker condition than UMP unbiasedness, which does not exist in the multi-hypothesis case.

Uniform global optimality: A protocol is uniformly globally optimal if it maximizes the planner’s objective for all values of the welfare weight λ ≥ 0 and all priors π over the parameter space, making it robust to uncertainty about the relative importance of deterrence versus research motivation.

MHT correction factor: Defined as C(J, Σ) / (C̄ · |J|), this factor captures how the cost per test varies as the number of hypotheses grows. It equals 1/|J| (Bonferroni) when all costs are fixed, and equals 1 (no correction) when costs are proportional to the number of tests; the empirically appropriate correction lies strictly between these extremes.

Cost function C(J, Σ): The private cost borne by the researcher for conducting the experiment, which depends on both the set of treatments J and the experimental design Σ (including sample size). The degree of optimal MHT adjustment is a direct function of how this cost varies with the number of hypotheses tested.

Global null space Θ₀(J): The set of parameter vectors θ for which the welfare effect of implementing any combination of treatments is strictly negative—i.e., the status quo of no treatment dominates all interventions. Maximin optimality requires deterring researcher experimentation over this set.

Cost complementarities across studies: Cost structures in which conducting multiple studies together is cheaper than conducting them separately. Cross-study MHT adjustments are warranted if and only if such complementarities exist; absent complementarities, each study’s optimal threshold is set independently of others.

A Robust Test for Weak Instruments for 2SLS with Multiple Endogenous Regressors

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a test for instrument strength based on the bias of two-stage least squares (2SLS) that: (1) generalizes the Stock-Yogo (2005) and Sanderson-Windmeijer (2016) tests to be robust to heteroskedasticity and autocorrelation (HAC), and (2) extends the Montiel Olea-Pflueger (2013) robust test from models with a single endogenous regressor to models with multiple endogenous regressors—the important remaining gap identified by Andrews et al. (2019). The test is based on a weighted quadratic loss in the asymptotic bias of 2SLS and can use either the Stock-Yogo absolute bias criterion or the 2SLS bias relative to Montiel Olea-Pflueger’s worst-case benchmark. Extensions are developed to test whether instruments are weak for individual 2SLS coefficients. In simulations, the test controls size and is powerful, and the authors provide efficient code packages. The test is applied to state-dependent fiscal multipliers (Ramey-Zubairy 2018).

In depth

Q1. What is the key gap in the existing weak instrument testing literature that this paper fills?

The key gap is the absence of a test for weak instruments that is both HAC robust and applicable to models with multiple endogenous regressors. Stock-Yogo (2005) requires conditionally homoskedastic and serially uncorrelated (CHSU) errors. Montiel Olea-Pflueger (2013) introduced a HAC-robust effective F-statistic for a single endogenous regressor but their test does not extend to multiple regressors. Sanderson-Windmeijer (2016) addressed multiple endogenous regressors but retained the CHSU assumption. This paper combines HAC robustness with multiple-regressor generality, filling the gap Andrews et al. (2019) identify as the most important remaining open problem in the literature.

Q2. What is the test statistic and what are its two bias criteria?

The test statistic is based on a weighted quadratic loss in the asymptotic bias of the 2SLS estimates when first-stage coefficients are close to zero, with two criteria: (i) the absolute bias criterion of Stock-Yogo (2005)—the 2SLS bias relative to the maximum OLS bias; and (ii) the 2SLS bias relative to Montiel Olea-Pflueger’s (2013) worst-case benchmark. The test accommodates both the Stock-Yogo setting (instruments weak because the first-stage coefficient matrix is near rank zero) and the Sanderson-Windmeijer setting (instruments weak because the first-stage coefficient matrix is near having a rank reduction of one rather than near rank zero).

Q3. What extensions are provided for individual coefficient testing?

Extensions are developed to test whether instruments are weak for individual 2SLS coefficients, by applying the test to a transformed regression that isolates the coefficient of interest, accommodating the Sanderson-Windmeijer (2016) setting in which one regressor is locally under-identified while others may not be. This is important in practice because researchers with multiple endogenous regressors often care about whether instruments are weak for each coefficient separately, not just for the system as a whole; the extension provides a formal basis for this common applied practice.

Q4. What does the empirical application show?

The paper demonstrates the testing procedures in the context of estimating state-dependent fiscal multipliers as in Ramey and Zubairy (2018), where the two endogenous regressors are lagged spending interacted with a state variable (recession/expansion indicator), illustrating both the implementation of the test and how inference differs from relying on CHSU-based critical values. In simulations, the test controls size accurately and is powerful against alternatives where instruments are strong, providing a reliable and practically useful tool with efficient code packages distributed for applied researchers.

Key concepts

weak instruments test : a test assessing whether the first-stage regression is sufficiently strong to make 2SLS inference reliable; based on the maximum bias of 2SLS relative to a benchmark; weak instruments cause 2SLS to inherit the bias of OLS. HAC robustness : robustness to heteroskedasticity and autocorrelation; absent from Stock-Yogo (2005), meaning researchers who use their critical values while allowing for HAC errors in second-stage inference apply mismatched validity assumptions. effective F-statistic : the statistic introduced by Montiel Olea and Pflueger (2013) for HAC-robust weak instruments testing with a single endogenous regressor; generalized in this paper to the multiple-regressor setting. absolute bias criterion : the criterion that the 2SLS relative bias (standardized absolute bias) is below a threshold; equivalently, the 2SLS bias as a proportion of the maximum OLS bias; defined by Stock-Yogo (2005) and generalized here to the HAC-robust multi-instrument setting.

A Temporary VAT Cut as Unconventional Fiscal Policy

Mon, 01 Jan 0001 00:00:00 +0000

The paper studies Germany’s temporary 3 percentage-point VAT cut from July 1 to December 31, 2020 (standard rate 19%→16%, reduced rate 7%→5%), combining two causal identification strategies with microdata and a HANK model to establish that intertemporal substitution drove a large spending response concentrated in durable goods.

Ex-ante approach (July 2020 BOP-HH survey, fielded immediately after the cut took effect): The survey distinguishes households informed about the January 2021 reversal (treated) from those who believed the cut was permanent (control). Treated households are approximately 10 percentage points more likely to increase durable purchases on the extensive margin. This is a lower bound on the intertemporal substitution effect because some “control” households likely learned about the reversal before the survey, attenuating the control group’s spending behavior toward that of the treated group.

Ex-post approach (January 2021 BOP-HH survey and GfK scanner data): Cross-household variation in perceived VAT pass-through identifies the spending effect. Households perceiving high pass-through — who saw prices actually fall at their usual stores — spent approximately 37 percent more on durables in 2020HY2 than those perceiving low or no pass-through (preferred OLS/IV specification, Table 3). GfK scanner data on semi-durables shows approximately 10 percent higher spending for high vs. low perceived pass-through (coefficient ≈ 0.093, Table 5). Non-durable spending shows no statistically significant response. The magnitude of the response increases with the durability of the good and increases over time toward the December 2020 cutoff, consistent with intertemporal substitution (a more durable good generates larger discounted savings from buying before the reversal; a later purchase locks in savings for longer until January).

Direct evidence of intertemporal pull-forward (Table 4): Households reporting high perceived pass-through in 2020HY2 planned to spend approximately 1,642 EUR less on durables in 2021 first-half relative to those with low pass-through in the GfK survey — a direct “spend now, buy less later” pattern confirming temporal shifting rather than a pure income effect.

Cross-sectional heterogeneity: The response is driven by young, low net-wealth households and price-sensitive “bargain hunters” who actively compare prices across stores. Critically, the response is NOT concentrated in financially literate households or those reporting long planning horizons, which distinguishes the VAT policy from forward guidance (which requires understanding and acting on future rate paths) and implies the policy reaches a broad spectrum of household types.

No COVID-19 confound: The paper finds no significant interaction between a household’s pandemic exposure (work disruption, income loss, health shock) and its durable spending response, confirming the intertemporal substitution mechanism operated independently of the concurrent COVID-19 environment.

HANK model (based on the Bayer, Born, Luetticke 2024a two-asset heterogeneous-agent New Keynesian framework, adapted with illiquid durable goods and a Calvo durable-adjustment friction):

Durable adjustment probability per semi-annual period: λ = 18% (Calvo friction calibrated to the spread of the durable spending response through 2020HY2)
Perceived-pass-through heterogeneity: 65% of households perceive high pass-through; perceived average cut among treated = 2.4pp (both calibrated to BOP-HH data)
Calibration targets: durable spending response elasticity = 0.32; X/Y = 0.08 (durable expenditure share); B/Y = 0.86 (liquid bond share); (B+qΠ)/Y = 1.90 (total liquid wealth); G/Y = 0.29; top-10% wealth share = 52%; fraction liquidity-constrained = 18%
Structural parameters: β = 0.92 (semi-annual discount factor); ξ = 2.0 (CRRA coefficient); ϑ = 0.5 (Frisch labor supply elasticity); ν = 0.80 (non-durable expenditure weight); τc = 17.5% (baseline VAT rate); τ = 31% (income tax rate); δ = 5% (semi-annual durable depreciation rate)
Impact effects: total consumption +4.3%; durable consumption +29.4%; the VAT-inclusive price level falls by approximately 1.0pp on impact (less than the 2.4pp perceived cut because of demand-driven upward pressure on prices)
Multipliers at ELB: impact consumption multiplier = 3.0; cumulative two-year consumption multiplier = 1.7
Multipliers with Taylor rule: impact = 2.2; cumulative two-year = 0.9 (lower because the central bank raises nominal rates in response to the demand boost, partly crowding out consumption)
Decomposition: the direct effect — computed holding GE equilibrium objects (wages, asset prices, aggregate demand) fixed — accounts for approximately 90% of the durable consumption response and approximately 4/5 of the non-durable response; the remaining indirect effect operates through positive Keynesian income spillovers
Comparison to interest rate cuts: the VAT cut delivers a larger aggregate consumption response per unit of fiscal cost than a comparable nominal interest rate reduction, because interest rate cuts create countervailing income effects for net savers (who lose interest income) that partially offset the stimulus for net borrowers

Scope conditions: Empirical estimates are local to Germany’s 2020 economic environment (near-zero ECB policy rate, partial COVID-19 demand suppression). The causal identification exploits cross-household variation in perceived pass-through, instrumented by bargain-hunting behavior; the exogeneity assumption requires that price-searching behavior affects spending through perceived prices rather than through other channels. The HANK quantitative results are conditional on the Calvo durable adjustment friction and the 65%/35% perceived-pass-through split; sensitivity to these calibration choices is explored but not the primary focus.

Note on working paper versions: This summary is based on NBER Working Paper 29442 (August 2024 revision), which uses a HANK framework and reports a 4.3% impact on total consumption. A Bundesbank Discussion Paper (24/2025, April 2025) describes the model as a “RANK” (representative-agent) framework with a 4.4% impact. The published RES version (June 2026) may differ from both working paper versions in its model specification; the core empirical findings (37% durable response, 10% semi-durable response, 10pp ex-ante effect) are unlikely to have changed.

In depth

Q1. What is the ex-ante identification strategy, and what does it identify?

The July 2020 BOP-HH survey ran immediately after the VAT cut took effect and identifies the causal effect of expecting a tax cut to be temporary by comparing households informed about the January 2021 reversal (treated) with those who believed the cut was permanent (control); treated households are approximately 10 percentage points more likely to report an intention to increase durable purchases. This is a lower bound on the true intertemporal substitution effect: if some “control” households learned about the reversal through other channels between the survey date and December 2020, they would have behaved more like treated households, compressing the gap. The ex-ante design also measures the extensive-margin decision (whether to increase purchases) rather than the total spending level, so the 10pp estimate is not directly comparable to the 37% ex-post level estimate.

Q2. What is the ex-post identification strategy, and how does it address endogeneity?

The January 2021 BOP-HH survey asks respondents how their 2020HY2 spending compared to a counterfactual without the VAT cut, and instruments perceived price pass-through with bargain-hunting behavior (price comparison across stores) — a variable that predicts who notices price changes but should not directly affect intertemporal allocation decisions. OLS and IV estimates are close (Table 3), suggesting limited endogeneity bias; the IV result of 37% more durable spending for high vs. low perceived pass-through is the preferred causal estimate. GfK scanner data provides an independent corroboration using objective purchase records rather than survey recall, yielding the 10% semi-durable estimate (Table 5, coefficient ≈ 0.093 in IHS-transformed spending).

Q3. Why does the response increase with the durability of the good?

A durable good yields a flow of consumption services over multiple periods; purchasing it before the January 2021 VAT reversal locks in tax savings for the entire lifetime of the good, while purchasing a non-durable before the reversal saves taxes only on a single-period consumption unit — so the present-discounted-value gain from intertemporal substitution is proportional to the good’s durability. This prediction is confirmed empirically: durables (white goods, electronics) show the largest response (37%); semi-durables (clothing, textiles in GfK) an intermediate response (~10%); non-durables no significant response. The fact that the spending response also builds toward the December cutoff — with the largest response in November and December 2020 — further supports intertemporal substitution (households delay purchases even within the cut period, maximizing the remaining time advantage).

Q4. Why was the VAT cut effective despite the concurrent COVID-19 shock?

The paper finds no statistically significant interaction between household-level COVID-19 exposure (income loss, work disruption, health shock) and the durable spending response to the VAT cut; the intertemporal price channel operated independently of pandemic-related income and uncertainty effects. This is consistent with the bargain-hunting interpretation: price-sensitive households who actively compare prices adjusted toward durables regardless of their pandemic-specific economic circumstances. The finding also implies that the simultaneous COVID-19 shock does not confound the identification, because the cross-household variation in perceived pass-through is independent of COVID-19 exposure.

Q5. Why is a HANK model appropriate, and what does durable heterogeneity add?

A HANK model is needed because the spending response is driven disproportionately by young, low net-wealth households who face binding liquidity constraints at some frequencies — in a representative-agent model all households respond immediately to the intertemporal price signal, which would predict an immediate front-loaded response; in the HANK model with Calvo durable adjustment, constrained households adjust their durable stock only when they receive an adjustment opportunity (λ=18% per semi-annual period), spreading the response through time and matching the observed gradual build-up of durable spending through 2020HY2. The illiquid-durable extension of the Bayer-Born-Luetticke framework separately tracks liquid financial assets and illiquid durables, allowing the model to capture both the temporal dynamics of the spending response and the cross-household variation in responses across the wealth distribution.

Q6. What is the impact consumption multiplier, and why is it larger at the ELB?

The impact consumption multiplier — the increase in total consumption divided by the fiscal cost of the VAT cut (measured as the VAT rate reduction times baseline consumption) — is 3.0 at the effective lower bound (ELB) and 2.2 with an active Taylor rule. At the ELB, the demand boost from the VAT cut raises inflation expectations; since the nominal rate cannot rise, the real rate falls, providing a secondary stimulus through the inter-temporal Euler equation; with an active Taylor rule, the central bank raises the nominal rate in response to higher inflation, crowding out some consumption and reducing the multiplier. The 3.0 impact multiplier exceeds the standard Keynesian multiplier because the durable sector amplifies the effect: a 2.4pp perceived price cut induces a 29.4% jump in durable purchases, whose production generates large income spillovers.

Q7. Why does the cumulative two-year multiplier fall below the impact multiplier?

The cumulative two-year multiplier is 1.7 at the ELB (vs. 3.0 on impact) because durable purchases pulled forward into 2020HY2 create a “payback effect” — households that already upgraded their durables need fewer new purchases in 2021, reducing durable consumption below the counterfactual path for several quarters after the reversal. This is directly documented in Table 4: high perceived pass-through households planned to spend approximately 1,642 EUR less on durables in 2021H1, and the GfK data confirms a spending decline in early 2021. The cumulative multiplier remains above zero and above 1.0, confirming the policy provides net stimulus over the two-year horizon even accounting for the post-cut hangover.

Q8. Why is the VAT cut more powerful than a comparable interest rate cut?

An interest rate cut stimulates borrowers but simultaneously reduces interest income for net savers, who partially offset their reduced income by consuming less; the VAT cut lowers current prices for all households without changing the interest rate, so there is no countervailing income effect for savers, and the consumption stimulus is less diluted by redistribution. In the HANK calibration, the additional dimension is that the VAT cut operates through a perceived price channel that requires only that households notice lower prices in stores — a much lower bar than the financial sophistication required to respond to forward guidance or interest rate signals — so the policy reaches a broader share of the household distribution than monetary easing.

Q9. What does the distributional evidence imply for fiscal stimulus design?

Young, low net-wealth households respond most strongly to the VAT cut, the opposite of the pattern expected if the response required financial sophistication; combined with the bargain-hunting identification, this implies the policy’s effectiveness does not depend on forward-looking planning or consumption-smoothing capacity — it is triggered simply by noticing prices are lower at the store. This finding challenges the conventional view that temporary fiscal policies are less effective than permanent ones because households do not optimize over them; instead, the price-noticing channel bypasses the forward-looking optimization entirely and generates a large spending response among households who do not match the life-cycle model assumptions. The distributional progressivity (young, low-wealth households drive the response) also contrasts with unconventional monetary policy (which benefits asset-holders through wealth effects) and improves the equity case for temporary VAT cuts as a stimulus instrument.

Key concepts

intertemporal substitution : the mechanism by which a temporary price reduction — here a VAT cut that will be reversed — induces households to shift consumption from the post-cut period to the cut period; the paper’s primary transmission channel, more powerful for durable goods because the present-value savings scale with the good’s lifetime.

perceived pass-through : the fraction of the statutory VAT rate reduction that a household perceives as an actual reduction in the prices it faces in its usual stores; the paper’s main source of cross-sectional identification in the ex-post strategy, correlated with bargain-hunting behavior.

ex-ante approach : the identification strategy using the July 2020 BOP-HH survey; identifies the causal effect of expecting a cut to be temporary by comparing informed (reversal known) vs. uninformed (thought permanent) households on their intended durable purchase behavior.

ex-post approach : the identification strategy using the January 2021 BOP-HH survey and GfK scanner data; identifies the causal effect of perceived price changes on realized spending by comparing high vs. low perceived pass-through households and instrumenting with bargain-hunting behavior.

payback effect : the reduction in durable spending in 2021H1 among households that pulled forward purchases during the 2020 cut; documented through the 1,642 EUR planned spending gap in Table 4 and GfK scanner data; makes the cumulative two-year multiplier (1.7) substantially lower than the impact multiplier (3.0).

HANK model with durable Calvo friction : the Bayer-Born-Luetticke (2024a) two-asset heterogeneous-agent New Keynesian framework adapted with illiquid durable goods and a Calvo probability of durable adjustment (λ = 18% per semi-annual period); the Calvo friction matches the gradual build-up of the durable spending response through 2020HY2 rather than an immediate front-loaded spike.

All Along the Watchtower: Military Landholders and Serfdom Consolidation in Early Modern Russia

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates the origins of serfdom in early modern Russia, arguing that the institution consolidated primarily through political economy dynamics between the crown and a landholding military class, rather than from economic fundamentals such as labor scarcity, land-labor ratios, or grain trade opportunities. The central argument is that the prolonged defense of Russia’s southern frontier against Crimean Tatar nomadic raids generated a class of military landholders who possessed both the coercive capacity and the political leverage to press the state into restricting peasant labor mobility.

The mechanism runs as follows. The Russian state, lacking the fiscal capacity to pay soldiers directly, granted frontier lands along the Tula defense line to high-ranked soldiers in exchange for military service under the pomest’e system. These lands were selected for their defensive rather than agricultural value and sat on the forest-steppe boundary roughly 180 km south of Moscow. Since soldiers could not farm while on duty and could not compete in free labor markets given the area’s low agricultural attractiveness, the arrangement was only sustainable if peasants were bound to the land. Military landholders collectively petitioned the Tsar repeatedly — with petition volumes peaking during urban uprisings (9 petitions in 1648, 13 in 1682) when the government’s political vulnerability increased the military’s bargaining power — until serfdom was codified in the Law Code of 1649.

The authors test this theory using newly digitized data from the 1678 household census, which records male population by six legally distinct peasant categories across 172 districts of Muscovy, combined with data on landholder estate counts and sizes. The primary empirical finding is that districts on the Tula defense line had approximately 40% of their population composed of serfs, compared to roughly 14% nationally — a difference of about 25 percentage points that survives the inclusion of geographic and climatic controls (grain suitability, temperature seasonality, precipitation, terrain ruggedness, river location, distance to Moscow, and regional fixed effects). Placebo tests confirm this pattern is specific to the most legally dependent peasant groups: the defense line is negatively associated with royal peasants and statistically insignificant for church peasants, free peasants, and non-Russian peasants.

To address potential endogeneity of the defense line’s location, the authors construct an instrumental variable using a novel geospatial algorithm. The algorithm computes optimal nomadic invasion routes from Crimea to Moscow via topographic cost rasters (using flow accumulation values as proxies for river-crossing barriers), then intersects these routes with the historically stable forest-steppe boundary (identified through FAO/UNESCO soil types — Podzoluvisols versus Chernozems). Districts at this intersection were 70 percentage points more likely to host the actual defense line. Two-stage least squares estimates confirm and slightly exceed the OLS magnitudes, supporting the causal interpretation.

The paper further tests two canonical alternative explanations and finds them insufficient. Domar’s (1970) labor-scarcity hypothesis predicts serfdom should be higher where population density is lower; the data show the opposite sign, contradicting this prediction. The Baltic grain trade hypothesis yields only a small, unstable positive interaction between river access to the Baltic and grain suitability, which disappears when the defense line variable is included. A horse race including all variables simultaneously shows the defense line coefficient at approximately 24 percentage points remains stable while alternative predictors become insignificant.

Mechanism tests show that defense line districts had 3.2 more estates per 100 square kilometers than the national average of 2.3, with the excess concentrated in very small (up to 5 serf households) and small (6–25 households) estates — consistent with the state’s strategy of maximizing soldier count by allocating the minimum serf labor sufficient to sustain a cavalryman. A bigram similarity analysis of collective petitions versus the 1649 Law Code yields a correlation coefficient of 0.7 for the top twenty bigrams between a 1637 petition and Chapter 11 (restricting peasant mobility), with no comparable similarity to other chapters. Persistence is documented through 1719, 1795, and 1858 censuses: defense line districts maintained the highest serf concentration through to three years before emancipation in 1861.

In depth

Q1. What is the paper’s central argument about the origins of Russian serfdom?

A: The paper argues that serfdom consolidated primarily due to political economy dynamics: the crown’s dependence on a landholding military class for frontier defense against steppe nomads gave that class sufficient political leverage to secure the legal restriction of peasant labor mobility. The military landholders’ coercive capacity and proximity to their small estates made labor coercion a viable complement to their military function. This explanation dominates alternative accounts based on labor scarcity, grain trade, or soil quality in all specifications tested.

Q2. What was the Tula defense line and why was it located where it was?

A: The Tula defense line (Great Abatis Line) was a chain of about 40 fort towns stretching over 500 km east-west, centered on Tula approximately 180 km south of Moscow, erected in the 1560s using felled trees, earth mounds, ditches, and watchtowers. Its location on the forest-steppe boundary was determined by two military-logistical constraints: it had to block the main nomadic invasion routes from Crimea, and it had to lie within the forest zone where timber was the cheapest construction material and which provided natural shelter. The paper documents that the defense line area did not differ from the rest of Muscovy in agricultural suitability, annual precipitation, seasonality, or terrain ruggedness — its distinctive feature was purely defensive.

Q3. How large is the estimated effect of defense line proximity on serf concentration?

A: In the unconditional specification, defense line districts had a 30 percentage point higher share of serfs than the rest of the country. After adding geographic controls (grain suitability, seasonality, precipitation, terrain ruggedness, river dummy, distance to Moscow, and regional fixed effects), the coefficient stabilizes at approximately 25 percentage points. Given that serfs averaged about 14% of total population nationally but about 40% in defense line districts, the estimated effect is substantial relative to the baseline.

Q4. How do the authors address endogeneity of the defense line location?

A: They construct an instrumental variable defined as the intersection of two variables: districts lying on the computed optimal nomadic invasion routes (covering 98 of 172 districts, or 57% of the sample), and districts on the forest-steppe soil boundary (38 districts, or 22% of the sample). Their interaction covers 23 districts and is the excluded instrument. In the first stage, this interaction term raises a district’s probability of hosting the actual defense line by 70 percentage points, while the linear terms become essentially zero once the interaction is included. The 2SLS second-stage estimates of the serf-share effect are slightly higher than OLS and statistically significant, confirming the direction and approximate magnitude of the OLS results.

Q5. What does the paper find about Domar’s labor-scarcity hypothesis?

A: The paper finds no support for Domar’s (1970) prediction that serfdom should be more prevalent where labor is scarcer (lower population density). Controlling for grain suitability and geographic factors, population density enters with a positive and statistically significant coefficient at the 5% level — the opposite sign from what Domar’s theory predicts. When the defense line dummy is added, population density becomes insignificant while the defense line coefficient remains at approximately 25 percentage points, consistent with the baseline.

Q6. What does the paper find about the Baltic grain trade hypothesis?

A: An exogenous measure of Baltic trade potential — a dummy for districts with river access to the Baltic, interacted with grain suitability — yields a small and marginally positive effect on serf share in Baltic districts with higher grain suitability. However, this effect disappears when the defense line dummy is included, and is also sensitive to alternative spatial clustering (becoming insignificant at the 300 km clustering radius even without the defense line dummy). The authors interpret this instability as inconsistent with grain trade being a primary driver of serfdom.

Q7. What is the evidence for the estate-size mechanism?

A: Defense line districts had on average 3.2 more estates per 100 square kilometers than the national average of 2.3 per 100 square kilometers. Among estate-size brackets, very small (up to 5 serf households) and small (6–25 serf households) estates were disproportionately concentrated in defense line districts, while the location of medium-sized and large estates was statistically independent of the defense line. This pattern is consistent with the state’s strategy of allocating minimum viable serf endowments to maximize the number of soldiers supportable along the line.

Q8. What is the textual evidence linking military petitions to the 1649 Law Code?

A: A bigram similarity analysis between a 1637 collective petition and Chapter 11 of the 1649 Law Code reveals a correlation coefficient of 0.7 for the top twenty bigrams. The five most common bigrams appear in both texts: “runaway peasants,” “commoner peasants,” “census books,” “search years,” and “tsar’s decree.” This correlation does not extend to other chapters of the Law Code that regulate non-peasant matters, establishing specificity of the legislative influence.

Q9. How does the timing of collective petitions relate to political crises?

A: Over a corpus of 96 petitions between 1608 and 1698, landholders petitioned on average once per year, but activity spiked sharply during domestic uprisings: 9 petitions in 1648 (the “Salt Riot” urban uprising) and 13 petitions in 1682 (the musketeers’ revolt). These peaks coincide with moments when the government’s political vulnerability increased the military’s bargaining power, and in both cases were followed by legislative concessions — the 1649 Law Code and new decrees in 1683–85 on harsher punishment for harboring runaways, respectively.

Q10. What do the placebo tests show?

A: Regressions of non-serf peasant shares on the defense line dummy show that the defense line is negatively associated with royal peasants and statistically insignificant for church peasants, free peasants, and non-Russian peasants. A placebo test replacing military landholders with merchants and artisans shows no significant defense line effect on the latter group, while Moscow has an 11 percentage point higher merchant/artisan share. The specificity of the defense line effect to legally dependent peasants and military landholders supports the military-political mechanism rather than a generic frontier-area effect.

Q11. How persistent was the spatial distribution of serfdom after 1649?

A: The authors estimate their baseline equation with serf share from the 1719, 1795, and 1858 censuses as dependent variables. Defense line districts maintained disproportionately higher serf densities in all three periods, including when the sample is restricted to the original Muscovite districts to exclude post-18th century territorial acquisitions. By 1858, three years before emancipation, the spatial distribution of serfs remained similar to that observed 200 years earlier at the time of serfdom’s consolidation — despite the defense line having been militarily obsolete for over a century.

Q12. What explains the persistence of serfdom beyond its original military rationale?

A: The persistence reflects a mutually beneficial exchange between the crown and former military landholders. Landholders provided local state capacity — overseeing tax collection, administering military conscription, and adjudicating peasant disputes through estate courts — in lieu of a centralized bureaucracy. In return, the crown granted successive expansions of landholder rights: Peter I equalized military landholdings with hereditary estates in 1714, and Peter III in 1762 freed landholders from military service obligations while retaining their property rights over land and serfs. This fiscal-administrative dependency is also cited as a reason for the late timing and unfavorable-to-peasants terms of the 1861 emancipation reform.

Q13. How does this paper’s explanation relate to Eastern/Western European institutional divergence?

A: The paper argues that while the military revolution in Western Europe generated fiscally capable centralized states with regular infantry armies, Russia’s peripheral nomadic threat prolonged the feudal cavalry model supported by land grants and serf labor. This delayed the formation of Weberian bureaucracy and entrenched what the authors term a “garrison state” — one whose institutions and social structure were shaped primarily by military-security considerations. The paper positions military factors alongside existing divergence explanations emphasizing land property rights, political institutions, demographic regimes, and Enlightenment ideas.

Q14. What is the methodological contribution of the optimal invasion route algorithm?

A: The algorithm uses flow accumulation rasters (proportional to river width and basin size) as a cost function to compute the lowest-cost travel paths from Crimea to Moscow, iteratively penalizing cells within 15 km of each computed route and re-running the path search to generate four distinct routes per origin point (eight total, including routes from the Don River steppe). This produces a high-resolution, geographically continuous measure of military threat exposure that the authors argue provides statistical power in contexts where terrain ruggedness or simple distance measures lack variation — particularly relevant for flat plains with a single threat origin correlated with other variables.

Pomest’e system: The institutional arrangement by which the Russian state granted frontier lands to high-ranked soldiers in exchange for military service, under the rule that “the land must not leave the service.” Unlike hereditary estates, pomest’e holdings were conditional on active service and could not be passed to heirs unless sons continued military service. This system enabled the formation of a permanent cavalry force despite the state’s low fiscal capacity, but required binding peasants to the land to make the arrangement viable for the soldier-landholders.

Serfs (bobyli and dvorovye): In the paper’s 1678 census framework, serfs are defined as the two most legally dependent subgroups of private peasants — cotters (bobyli), who owned no property and worked full-time for their landlord in exchange for payment in kind, and servants (dvorovye), who performed household and support functions on the estate. These groups constituting about 14% of total population nationally were totally dependent on their landlord and could not retain the marginal product of any part of their labor. After the 1649 Law Code, villeins (krest’yane) gradually converged to this status as well.

Collective petitions (chelobitnye): The primary institutional channel through which the military landholder class communicated collective interests and applied political pressure on the crown in 17th-century Muscovy. The paper documents 96 such petitions between 1608 and 1698, showing that their volume, timing (peaking during urban uprisings), and textual content (closely matching Chapter 11 of the 1649 Law Code) were the proximate mechanism by which landholders converted military leverage into legal codification of serfdom.

Optimal defense line (instrumental variable): The paper’s constructed instrument, defined as the intersection of computed optimal nomadic invasion routes (based on topographic cost rasters approximating river-crossing barriers) and the forest-steppe soil boundary (Podzoluvisols/Chernozems boundary from the FAO/UNESCO Soil Map). This instrument captures the geographically and militarily determined placement of defensive fortifications, purging variation in actual defense line location that might reflect agricultural or economic value.

Garrison state: Used by the authors (adapting Lasswell’s term) to describe a state whose institutions and social structure are shaped primarily by military security considerations. In the Russian context, this refers to the persistence of a feudal cavalry system, land-grant-based military compensation, and labor coercion that together delayed centralized state formation and Weberian bureaucracy relative to Western European states undergoing the military revolution toward regular infantry armies.

Labor coercion complementarity: The paper’s mechanism whereby employers with high coercive capacity (proximity to weapons, military training) can deploy that same capacity to restrict workers’ outside options and extract labor surplus. In the defense line context, soldiers’ military skills and armament made them effective at preventing serf flight and enforcing labor obligations — creating a complementarity between military capacity and serfdom that was absent among merchants or church institutions with comparable landholdings elsewhere.

Auctions with Frictions: Recruitment, Entry, and Limited Commitment

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops an auction model that jointly incorporates three frictions pervading informal price-formation processes: (1) costly recruitment by the seller, (2) costly participation by bidders, and (3) the seller’s inability to commit to a recruitment level or reserve price. The authors argue these frictions are especially prevalent in markets for idiosyncratic assets such as mergers and acquisitions, real estate, and home repair contracting, where auction houses like Christie’s and Sotheby’s command fees of 20–30% of revenues precisely because they reduce the underlying inefficiencies.

The model features a single seller who exerts recruitment effort gamma at cost gamma*s, generating a Poisson-distributed number of contacted bidders with mean gamma. Each contacted bidder independently decides whether to pay entry cost c > 0 to learn their private value and participate in a first-price auction (FPA). The seller cannot commit to gamma (which is unobservable to bidders) or to a reserve price. Two scenarios are analyzed: PO (participation-observable, where bidders observe the number of entrants before bidding) and PU (participation-unobservable).

The central tension is between the seller’s incentive to recruit more bidders to intensify competition and raise revenue, and bidders’ rational concern that excessive recruitment makes entry unprofitable. Because the seller cannot commit, this tension generates several novel inefficiency results.

In the PO scenario, the seller’s marginal revenue from recruitment Ro’(lambda) is single-peaked, meaning there is a minimum profitable participation scale lambda_o below which the seller will never recruit. Combined with a maximum participation level lambda-bar_c above which bidders will not enter (defined by U(lambda-bar_c) = c, where U is the bidder’s expected payoff), no-trade equilibrium is the unique outcome whenever lambda-bar_c < lambda_o — even for arbitrarily small recruitment cost s. This result holds because with unobservable effort, bidders correctly anticipate the seller will target participation above lambda_o, making entry unprofitable. When lambda-bar_c > lambda_o, three regimes arise: (i) no trade if s exceeds a threshold s-bar_o; (ii) an interior equilibrium with full entry (q* = 1) and lambda* = lambda_o(s) for intermediate s; and (iii) for small s, an equilibrium with lambda* = lambda-bar_c and partial entry q* = Ro’(lambda-bar_c)/s < 1. In regime (iii), total recruitment cost lambda*(s/q*) equals the constant lambda-bar_c * Ro’(lambda-bar_c) regardless of s — so even as s approaches zero, wasteful recruitment costs do not vanish, because they are determined by incentive constraints rather than by technology.

In the PU scenario, a no-trade equilibrium always exists for all parameter values, because the seller cannot credibly disclose participation, creating self-reinforcing expectations of zero competition. The seller’s recruitment incentive xi(lambda) is strictly weaker than Ro’(lambda) in the PO scenario (proven via revenue equivalence: Ro’(lambda) = xi(lambda) + a positive term reflecting how greater participation induces more aggressive bidding). This yields ranking reversals: for intermediate s and small c, the PO scenario dominates PU; but for small s or large c, the PU scenario’s weaker recruitment incentive reduces wasteful over-recruitment, making PU preferable. These comparisons translate directly to a comparison of FPA and SPA with unobservable participation: the two formats are not equivalent in the presence of recruitment and entry frictions because they generate different recruitment incentives.

A sampling-curse mechanism drives near-complete market unraveling when sellers have privately known recruitment costs drawn from a continuous uniform distribution on [0, s_o]. Because low-cost sellers recruit more, a contacted bidder believes the seller is more likely to have low costs — and hence to have recruited many other bidders — making entry unprofitable. Proposition 3 establishes a threshold c-hat such that for c in (c-hat, c-bar), as the lower bound of the cost distribution approaches zero, the fraction of seller types that remain inactive approaches one — near-complete unraveling — even though each type would be active if its cost were commonly known.

Q: What is the paper’s main modeling innovation relative to the existing literature? A: The paper’s central novelty is combining all three frictions — costly recruitment by the seller, costly participation by bidders, and limited seller commitment — in one model. The existing literature had studied entry and recruitment separately; Szech (2011) examined costly recruitment with costless entry; McAfee and McMillan (1987) and Levin and Smith (1994) studied costly entry with an exogenously given number of potential bidders; Milgrom (1987) and McAfee and Vincent (1997) studied limited commitment to a reserve price with a fixed bidder set. None combine all three.

Q: What is the “minimum profitable scale” result and why does it arise? A: Because the seller cannot commit to a reserve price, the first few bidders are complementary — they stimulate competitive bidding, causing the seller’s marginal revenue Ro’(lambda) to be initially increasing, then decreasing (single-peaked). This means the seller’s profit Pi_o(lambda, q) is maximized either at zero or at a participation level above a minimum scale lambda_o, defined by Ro’(lambda_o) = s-bar_o. The seller will never choose a participation level between 0 and lambda_o.

Q: Under what conditions does the market completely shut down in the PO scenario? A: No-trade is the unique equilibrium outcome whenever lambda-bar_c < lambda_o, where lambda-bar_c is defined by U(lambda-bar_c) = c (the participation break-even level) and lambda_o is the seller’s minimum profitable scale. This condition arises when entry costs c are large enough relative to the competitive dynamics. Importantly, no trade occurs for every recruitment cost s > 0, including arbitrarily small s — commitment failure alone can cause complete market breakdown even when recruiting bidders is nearly costless.

Q: What is the inefficiency in regime (iii) of Proposition 2 (small s, PO scenario)? A: When s < Ro’(lambda-bar_c), equilibrium has lambda* = lambda-bar_c and q* = Ro’(lambda-bar_c)/s < 1. The total recruitment cost is lambda* * (s/q*) = lambda-bar_c * Ro’(lambda-bar_c), a strictly positive constant independent of s. As s approaches zero, total recruitment effort and its cost do not vanish — they are pinned by incentive constraints. This waste could be avoided if the seller could commit to an effort level below lambda-bar_c, illustrating that commitment failure creates persistent inefficiency even when the technology of recruitment is inexpensive.

Q: Why does a no-trade equilibrium always exist in the PU scenario but not always in the PO scenario? A: In the PU scenario, if bidders expect zero participation, they bid zero conditional on being contacted; the seller then has no incentive to recruit, validating the expectation. This equilibrium is self-sustaining for all parameter values (Claim 2). In the PO scenario, the equilibrium refinement (requiring that off-path beliefs not support negative seller payoff at lambda = 0 when trade equilibria exist) rules out no-trade equilibria when lambda-bar_c > lambda_o and s is not too large; specifically, Proposition 2 shows that no-trade equilibrium is unique only when s > s-bar_o or lambda-bar_c < lambda_o.

Q: What drives the ranking reversal between PO and PU scenarios? A: The core result is Claim 3: Ro’(lambda) > xi(lambda) for all lambda > 0, meaning the marginal incentive to recruit is strictly stronger under PO than PU. This follows from revenue equivalence: Ro’(lambda) = xi(lambda) + (d/d lambda-hat) Ru(lambda, beta_{lambda-hat})|_{lambda-hat=lambda}, and the second term is strictly positive because greater expected participation induces more aggressive bidding. For intermediate s and small c, stronger PO recruitment incentives support higher participation and revenue. For small s or large c, those same stronger incentives generate wasteful over-recruitment in PO, making PU preferable.

Q: How does the paper connect its PO/PU comparison to a comparison of first- and second-price auctions? A: In any standard auction where the highest-value bidder wins, payoff and revenue equivalence imply that the bidder payoff function U(lambda) and seller revenue Ro(lambda) are identical. In particular, the dominant-strategy equilibrium of the SPA (where bidders bid their true values regardless of participation) generates the same outcomes as the PO equilibrium, because with truthful bidding the observability of participation is irrelevant. Therefore, comparing PO and PU with an FPA is equivalent to comparing the SPA and FPA with unobservable participation. The two formats are not revenue-equivalent when recruitment and entry frictions are present: their ranking depends on s and c in exactly the way described for PO vs. PU.

Q: What is the “sampling curse” and how does it cause market unraveling? A: The sampling curse arises when sellers have privately known recruitment costs. Because a lower-cost seller optimally recruits more bidders, the probability of any given bidder being contacted is higher when the seller has a lower cost. Conditional on being contacted, a bidder therefore believes the seller more likely has a low cost and thus has recruited many competitors, reducing the value of entry. In the binary-type case (Claim 8), if sL is sufficiently small relative to sH, the low-cost seller must recruit so many bidders that entry becomes unattractive; the resulting low q* makes the marginal recruitment cost sH/q* prohibitively high for the high-cost type, driving it out (lambda*_H = 0).

Q: What does Proposition 3 establish about near-complete unraveling with a continuum of seller types? A: With seller costs uniformly distributed on [s-bar, s_o], Proposition 3 establishes a threshold c-hat strictly between 0 and c-bar such that: (i) for c in (c-hat, c-bar), as s-bar approaches zero, the fraction of seller types with zero recruitment approaches one — near-complete market unraveling; (ii) for c < c-hat, all seller types remain active regardless of how small s-bar is. This is striking because for any commonly known s in (0, s_o), the PO scenario supports trade for all c < c-bar; unraveling arises purely from the interaction of private cost information and the sampling curse, not from any type’s cost being intrinsically too high.

Q: What does the welfare analysis say about equilibrium efficiency? A: The welfare-maximizing participation level lambda_w satisfies U(lambda_w) = c + s (equating the marginal bidder’s surplus to the full social cost of one more participant), with full entry q_w = 1. In equilibrium under PO, q* < 1 in some cases (wasted recruitment) and lambda* differs from lambda_w for almost all (s, c) pairs — both excessive participation (lambda* > lambda_w) and deficient participation (lambda* < lambda_w) can arise. Full efficiency requires Ro’(lambda*) = s and U(lambda*) = s + c simultaneously, but since both U and Ro’ are independent of s and c as parameters, these equalities generically fail.

Q: Does the seller benefit from being able to commit to recruitment effort? A: Claim 10 shows that with observable effort in the PO scenario, the seller commits to gamma-hat = min{lambda-bar_c, lambda_o(s)} when lambda-bar_c >= lambda_o, and to lambda-bar_c (if profitable) when lambda-bar_c < lambda_o. Commitment strictly improves the seller’s profit whenever gamma-hat = lambda-bar_c: it enables positive trade when lambda-bar_c < lambda_o and Ro(lambda-bar_c) > lambda-bar_c * s (otherwise impossible without commitment), and it saves recruitment costs when lambda-bar_c > lambda_o and Ro’(lambda-bar_c) > s. However, the commitment outcome is always welfare-inefficient: lambda-bar_c > lambda_w whenever s > 0.

Q: What anecdotal evidence do the authors cite for the model’s relevance? A: Subramanian (2010) and Boone and Mulherin (2004, 2009) show that the majority of merger and acquisition auctions are “informal” — mixtures of auctions and negotiations rather than structured processes with rules laid out in advance — and that sellers are typically unable to credibly commit to participation levels. Milgrom (2003) states from consulting experience that marketing an auction is often more critical than clever mechanism design. Fees of 20–30% of revenues paid to intermediaries like Christie’s and Sotheby’s are offered as quantitative evidence of the magnitude of the inefficiencies that such intermediaries reduce. Home repair contracting is cited as a familiar informal-auction setting where both recruitment and entry costs are material.

Recruitment effort (gamma): The seller’s costly action of contacting potential bidders, modeled as a Poisson process with mean gamma at cost gamma*s; unobservable to bidders in the baseline model.

Participation-observable (PO) vs. participation-unobservable (PU) scenarios: The two variants of the model; in PO, bidders observe the total number of entrants n before bidding; in PU, they do not observe n and the seller cannot credibly disclose it.

Minimum profitable scale (lambda_o): The smallest positive participation level the seller will ever choose in equilibrium, defined as the value where Ro’(lambda_o) equals the peak of the average revenue curve s-bar_o. The seller always recruits either zero bidders or at least lambda_o, due to the initial complementarity of bidders (they stimulate each other’s bids) under no-commitment-to-reserve-price.

Break-even participation level (lambda-bar_c): The maximum participation level at which a bidder’s expected gross payoff U(lambda) equals the entry cost c; bidders will not enter if they expect participation above lambda-bar_c.

Sampling curse: The adverse-selection mechanism arising when sellers have privately known recruitment costs: because low-cost sellers recruit more, a contacted bidder infers the seller is more likely to have a low cost and thus to have recruited many competitors, making entry less attractive and potentially driving higher-cost seller types out of the market.

xi(lambda): The seller’s marginal revenue with respect to recruitment in the PU scenario, defined as the total derivative of Ru(lambda, beta_{lambda-hat}) evaluated where actual and expected participation coincide (lambda-hat = lambda). Strictly less than Ro’(lambda) for all lambda > 0, reflecting that in PU the seller loses the ability to leverage bidder aggression via observable competition.

Wasteful recruitment: The equilibrium phenomenon in which total recruitment cost lambda*(s/q*) remains at the positive constant lambda-bar_c * Ro’(lambda-bar_c) even as s approaches zero, because incentive constraints — not technology — pin the equilibrium effort level.

Bank Information Production Over the Business Cycle

Mon, 01 Jan 0001 00:00:00 +0000

Bank Information Production Over the Business Cycle

Research Question

Banks produce private information about borrowers that is inherently unobservable to outside researchers. Howes and Weitzner ask whether the quality of this private information is countercyclical — that is, whether banks invest more in learning about borrowers when local economic conditions deteriorate — and whether any such cyclicality reflects endogenous information production incentives rather than exogenous changes in the information environment.

Data and Methodology

The paper uses the Federal Reserve’s Y-14Q Schedule H.1 confidential regulatory data, which covers commercial and industrial (C&I) loans exceeding $1 million originated by bank holding companies with $50 billion or more in total assets. This universe covers 85.9% of all banking sector assets and approximately 70% of all C&I loan volume (as documented by Bidder, Krainer, and Shapiro (2020)). A distinctive feature is that qualifying banks must report their internal probability of default (PD) estimates for each loan to the Federal Reserve. The sample is restricted to newly originated loans from 2014Q4 through 2019Q1 — the window over which PD data are well populated — with at least one year of subsequent observation to allow defaults to materialize. The outcome variable is a binary default indicator equal to one if the borrower defaults within two years of origination (0.41% of firms in the sample).

The measure of information quality is defined as the OLS coefficient on PD when regressing realized default on the bank’s internal PD estimate. A larger coefficient indicates that the bank’s private risk assessment carries more predictive content for realized default outcomes, above and beyond observable firm and loan characteristics. The authors identify cyclical effects by exploiting cross-sectional variation in county-level unemployment rates across the US at each point in time, controlling for bank-by-quarter fixed effects (to absorb supply-side bank-level factors), industry-by-quarter fixed effects, and bank-by-county fixed effects. The key interaction is between PD and the local unemployment rate.

Main Findings

The paper establishes three main results:

Banks’ PDs predict default and contain private information. Even after controlling for firm size, leverage, profitability, tangibility, log loan size, loan maturity, loss given default (LGD), loan type fixed effects, bank-quarter fixed effects, and industry-quarter fixed effects, PD remains a statistically and economically significant predictor of realized default. A one-percentage-point increase in PD increases the probability of default by approximately 25 basis points (coefficient of 0.245).
Information quality is countercyclical. A one-percentage-point increase in the local county unemployment rate increases the sensitivity of realized default to PD by approximately 8 basis points — roughly one-third of the average unconditional PD coefficient. When the unemployment rate is above a county’s median, the PD coefficient is approximately three times as large as during low-unemployment periods. Correspondingly, during high-unemployment periods, the total R-squared of a regression predicting default from observable firm and loan characteristics falls (from 0.311 to 0.264 — an 18% decline), while the marginal contribution of PD to the R-squared increases. This pattern is consistent with observable characteristics doing a worse job at predicting default in bad times, which in turn incentivizes banks to invest more in their internal risk assessments.
The cyclicality is driven by newly originated loans and more information-sensitive loans. The triple interaction between PD, the new-loan indicator, and the unemployment rate is positive and statistically significant across all specifications; the interaction between PD and unemployment for previously issued (non-new) loans is consistently less than half the size of the triple interaction term. The cyclical sensitivity also decreases by more than 0.1 (against a base of 0.08) in the year after origination and continues to fall over the loan’s life. Additionally, a one-standard-deviation increase in log loan size (approximately 1.29) increases the sensitivity of realized default to PD by about 0.085 — roughly one-quarter of the unconditional effect — and a one-standard-deviation increase in LGD (0.158) increases the PD coefficient by 0.098, or about one-third of the unconditional effect. Both the loan-size and LGD interactions are amplified when the local unemployment rate is high, consistent with Dang, Gorton, and Holmstrom (2012). The cyclical sensitivity of information quality is statistically significant only for firms in nontradeable industries (e.g., utilities, construction, retail, professional services), not for tradeable-sector firms.

Scope Conditions

Results are conditional on: large US bank holding companies ($50bn+ in assets) lending to non-financial, non-public domestic corporate borrowers with at least $100k in reported assets; a sample period from 2014Q4 to 2019Q1, covering a predominantly expansionary phase of the US business cycle; and county-level rather than aggregate time-series variation in economic conditions.

Policy Implications

Countercyclical information production implies that bank lending stimulus policies — including interest rate cuts, liquidity facilities, and asset purchase programs — may be less effective in recessions because banks simultaneously increase screening intensity. The marginal borrowers who gain access to credit from stimulus will differ across states of the cycle: in downturns, banks grant credit to fewer but higher-quality firms, so the incremental impact of expanding the credit supply on the number and type of firms funded may be attenuated. The authors connect this mechanism to prior empirical evidence that monetary policy is less effective in recessions (Tenreyro and Thwaites (2016)) and to LTRO and QE program evidence showing no increase in lending to riskier firms.

In depth

Q1. What is the precise definition of “bank information quality” used in this paper, and why is this measure preferred over alternatives?

Information quality is defined as the OLS coefficient β on the bank’s internal PD estimate when predicting realized two-year default in a regression that also includes firm and loan characteristics and a rich set of fixed effects. A higher coefficient indicates that the bank’s private risk assessment contains more predictive content for actual default beyond what is captured by observable firm and loan characteristics. This approach is preferred because it directly quantifies the marginal information content of the bank’s private assessment and can be estimated at the loan level using the cross-sectional variation in county-level economic conditions, rather than relying on aggregate time-series variation that would confound bank supply-side factors.

Q2. How do the authors establish that the PD estimates contain genuine private information rather than merely reflecting publicly observable characteristics?

Column (1) of Table 3 shows a PD coefficient of 0.245 in a regression predicting default without controls. Columns (2) and (3) add firm and loan characteristics (size, leverage, profitability, tangibility, log loan size, maturity, LGD, and loan type fixed effects) plus bank-quarter, industry-quarter, and bank-county fixed effects, and also add the interest rate as an additional control; the PD coefficient remains statistically and economically significant across all specifications. This demonstrates that PD retains predictive power for realized default even after absorbing all variation captured by observable firm-level fundamentals and pricing signals, implying the PD estimate contains private information not contained in observables.

Q3. What is the baseline magnitude of the cyclicality finding, and how is it identified?

A one-percentage-point increase in the county-level unemployment rate increases the PD coefficient by approximately 8 basis points (Table 5, Column 1). This represents about one-third of the average unconditional PD coefficient estimated in Section 3.1. Identification uses bank-by-quarter fixed effects so that the effect is estimated by comparing two loans made by the same bank at the same time to borrowers in counties with different unemployment rates, ruling out bank-level supply-side confounders such as changes in a bank’s cost of capital or risk appetite.

Q4. How does the split-sample analysis (above/below county-median unemployment) further characterize the cyclicality?

Columns (3) and (4) of Table 4 show that, when predicting default with PD alone (no controls), the PD coefficient is approximately three times as large during high-unemployment periods as during low-unemployment periods, and the R-squared is substantially higher for high-unemployment observations. The R-squared from a regression of default on observable controls alone is 17.8% higher when unemployment is low (0.311 versus 0.264), while the marginal contribution of PD to the R-squared is higher when unemployment is high (going from 0.264 to 0.267, versus 0.311 to 0.313). This pattern — observables explain less but PD explains more in bad times — is consistent with information frictions being more severe in downturns, which in turn raises banks’ incentives to invest in private information production.

Q5. How do the authors distinguish endogenous information production from a purely exogenous improvement in information quality during downturns?

Three tests are designed to be difficult to rationalize under a purely exogenous information channel. First, the cyclicality is concentrated in newly originated loans: the triple interaction term (PD × unemployment × new-loan indicator) is positive and statistically significant, while the PD × unemployment interaction for previously originated loans is less than half the size of the triple interaction. If information quality improved exogenously during downturns, there is no clear reason why this improvement would be far larger for loans where the bank is making a new capital commitment. Second, the cyclicality declines by more than 0.1 (relative to a base of 0.08) in the year after origination and continues to fall — simultaneously, the unconditional predictive power of PD increases over the loan life. This divergence is inconsistent with a purely exogenous mechanism. Third, the cyclical sensitivity is concentrated in loans that theory (Dang, Gorton, and Holmstrom (2012)) predicts to have higher information production incentives: larger loans, higher-LGD loans, and loans to nontradeable-sector borrowers.

Q6. How do loan characteristics (size and LGD) relate to information quality, and how does this relationship evolve over the business cycle?

Table 7 shows that a one-standard-deviation increase in log loan size (approximately 1.29) increases the sensitivity of realized default to PD by about 0.085, or roughly one-quarter of the unconditional PD coefficient. A one-standard-deviation increase in LGD (0.158) increases the PD coefficient by 0.098, or about one-third of the unconditional effect. Table 8 shows that both of these interaction coefficients have the same sign and are amplified during periods of high unemployment, consistent with Dang, Gorton, and Holmstrom (2012)’s prediction that information production decisions become more sensitive to loan features following negative aggregate shocks.

Q7. What does the tradeable versus nontradeable industry test contribute?

Because nontradeable-sector firms (utilities, construction, retail, transportation, accommodation, food services, information and communication, professional services) are more likely to depend on local demand, the same change in the county-level unemployment rate will have a larger impact on their default probability. Table 9 shows that the cyclical sensitivity of PD’s predictive power — the PD × unemployment interaction — is statistically significant only for nontradeable-sector firms, not for firms in tradeable industries. This provides additional evidence that the mechanism operates through local economic conditions affecting borrower riskiness in a way that raises information production incentives, rather than through some aggregate or bank-level mechanism.

Q8. Do composition effects (changes in the pool of borrowers) account for the main findings?

Table 11 shows that observable loan characteristics — average loan size, interest rate, LGD, and maturity — do not vary meaningfully with the local unemployment rate. Realized default rates increase slightly with unemployment but the effect is not statistically significant. The PD itself increases by only about 3 basis points for a one-percentage-point increase in unemployment (significant only at the 10% level). Loan volume declines: a one-standard-deviation increase in the unemployment rate (1.3 percentage points) leads to a 1.6% decrease in loan volume and a 5.46% decrease in the number of loans. The minimal variation in the risk profile of loans actually granted suggests that composition effects in the pool of approved borrowers are unlikely to explain the main result.

Q9. What are the implications of countercyclical information production for monetary policy transmission?

When unemployment is high, banks screen potential borrowers more intensively, which changes the composition of firms that gain access to credit. Policies designed to expand credit supply — interest rate cuts, liquidity facilities, asset purchase programs — face a more heavily screened pool of potential recipients during downturns. This means the marginal firms that receive additional credit following a stimulus in a recession will be of higher quality than the marginal recipients in an expansion, implying the credit transmission of monetary policy reaches a different — and potentially smaller — set of firms in recessions. The authors connect this to Tenreyro and Thwaites (2016)’s finding that monetary policy is less effective in recessions, and to evidence from the Eurosystem’s LTRO program that aggregate lending rose but lending to riskier firms did not, and to UK QE evidence finding no stimulation of bank lending.

Becker, Bos, and Roszbach (2020) also find that bank credit ratings predict default better in bad economic times, using data from a single Swedish bank and relying on aggregate time-series variation. The present paper differs in three ways. First, it uses cross-sectional variation across US counties within each time period, exploiting bank-by-quarter fixed effects to rule out bank supply-side confounders. Second, it uses loan-level rather than firm-level data, enabling the analysis of how loan characteristics (size and LGD) interact with information quality and cyclicality. Third, Becker, Bos, and Roszbach interpret the cyclicality as exogenous; Howes and Weitzner provide evidence against this interpretation — specifically, the concentration in newly originated loans and in loans with characteristics that theoretical models predict should generate higher endogenous information production.

Key Concepts

Bank Information Quality (as used in this paper) The size of the OLS coefficient on a bank’s internal probability of default (PD) estimate in a regression predicting realized loan default. A larger coefficient means the bank’s private risk assessment carries more predictive content for actual default beyond observable firm and loan characteristics. It is a measure of how much private information the PD encodes about borrower risk, not a measure of accuracy in an absolute sense.

Probability of Default (PD) — Y-14Q Internal Estimate Banks’ own model-based estimate of each corporate borrower’s likelihood of defaulting, reported confidentially to the Federal Reserve under Y-14Q Schedule H.1 filings. In the paper, PD is used as the observable proxy for the bank’s private risk assessment; its predictive power for realized default is the object being studied, not the PD level itself.

Countercyclical Information Production The property that banks’ incentives to invest in learning about borrower quality increase as economic conditions deteriorate. In the theoretical literature the paper tests empirically, the returns to distinguishing between borrower types rise in downturns (because the distribution of borrower quality widens and the consequences of adverse selection increase), inducing banks to produce more private information at loan origination. The paper uses “information quality is countercyclical” to mean that the predictive content of PD for realized default is higher when the local unemployment rate is higher.

Information Sensitivity (of a loan) The degree to which the value of a loan depends on information that is privately held by potential borrowers. Following Dang, Gorton, and Holmstrom (2012), loans are more information-sensitive when they are larger (larger potential loss from adverse selection) or when they have higher loss given default (lower expected recovery value). The paper uses loan size and LGD as proxies for information sensitivity and tests whether banks invest more in information about higher-information-sensitivity loans.

Loss Given Default (LGD) The bank’s estimate of the fraction of the loan’s value that would be lost if the borrower defaults, reflecting the expected recovery value of collateral and other loan features. In the paper, higher LGD (lower recovery) is a proxy for higher information sensitivity, since the consequences of lending to a bad borrower are larger when recovery is low.

Bank-by-Quarter Fixed Effects A set of fixed effects that absorbs all variation in outcomes attributable to a particular bank at a particular point in time. In the context of this paper, including bank-by-quarter fixed effects means the cyclicality results are identified from variation across counties for loans made by the same bank in the same quarter, ruling out supply-side explanations such as changes in a bank’s cost of capital, risk appetite, or credit standards that affect all of its loans uniformly.

Endogenous versus Exogenous Information Quality A core distinction in the paper. Exogenous information quality would mean banks passively receive more precise signals about borrowers during downturns regardless of their investment in screening. Endogenous information quality means banks actively choose to invest more in information production during downturns because the returns to distinguishing borrower types are higher. The paper argues its results — especially the concentration of cyclical effects in newly originated loans and in loans with characteristics that theory predicts should generate higher screening incentives — are consistent with the endogenous channel and are difficult to rationalize under a purely exogenous mechanism.

Bridges

Mon, 01 Jan 0001 00:00:00 +0000

This paper measures the causal effects of land transport infrastructure on economic activity, exploiting quasi-experimental variation in bridge construction over the Mississippi and Ohio Rivers in the United States. The central empirical puzzle motivating the study is a hump-shaped relationship between per capita income and distance to major land transport routes in contemporary U.S. data: income peaks around 5 km from a transport route, with an elasticity of 0.072 closer than 4.1 km and -0.096 at greater distances, so that 85% of Americans live where local income increases with distance to transport routes rather than decreasing. The question is whether this pattern reflects causal effects of infrastructure, selection, or sorting.

The paper develops two complementary identification strategies. The first exploits tributary confluences — where smaller rivers join larger rivers, sharply raising downstream flow rates and bridge construction costs — to generate quasi-random variation in bridge location. Because bridge construction costs increase convexly with river flow (maximum bending moment scales with span length squared), bridges are disproportionately built just upstream of confluences. The median upstream census tract lies 0.7 km from a bridge versus 2.3 km for the median downstream tract, making upstream tracts on average 60% closer to bridges and 27% closer to the nearest major land transport route. This asymmetry dates to at least 1880 and persists to 2010. Despite this persistent connectivity advantage, by 2010 upstream tracts have 13% lower per capita incomes and 63% higher population densities than downstream neighbours. The implied elasticity of per capita income with respect to distance to land transport, scaling the income effect by the distance-to-transport effect, is approximately 0.44. Income density (income per unit area) is higher upstream, though the difference is not statistically significant. Historical placebo tests using pre-bridge-construction data show no asymmetry in land values or population upstream versus downstream, supporting the identification assumption.

The second strategy exploits variation in the timing of bridge construction. Because major bridge projects involve decades of planning, financing, design, and construction — the Wheeling Suspension Bridge was chartered in 1816 but opened in 1849 — the precise opening date is argued to be exogenous to short-run deviations from local growth trends. Using a county-level panel from 1860 to 2010 (432 counties, 14–19 states), the paper estimates event-study regressions around the first time a county experiences a 50% reduction in distance to a bridge. After such a reduction, farm land values (the best available consistent proxy for total economic activity in historical data) rise immediately and cumulatively by approximately 9% over 30 years. Population rises by approximately 5% over the same period. The proportionally larger rise in land values than population implies higher per capita economic activity in better-connected counties after 30 years.

These two sets of results are reconciled through a narrative account of development. Better bridge access drives industrialization — manufacturing employment shares rise in counties experiencing improved connectivity — and urbanization. Cities form around historical transport routes and expand. Richer households then sort away from historical city centres into lower-density suburban areas, while lower-income households remain near or selectively migrate to the historical transport corridors. This within-city sorting produces the observed cross-sectional gradient: areas nearest transport routes end up with higher population density but lower per capita incomes. The negative local income effect of proximity to transport routes is larger in more urbanized areas and areas with higher income inequality, and is concentrated among non-white and low-education populations.

The paper also contributes a new dataset covering every road and rail bridge (237 total) ever constructed over the Mississippi and Ohio Rivers from 1849 to 2010, assembled from the National Bridge Inventory and extensively cross-checked with satellite imagery and historical sources.

Q: What is the motivating empirical puzzle about transport infrastructure and income?

A: In contemporary U.S. census data, per capita income does not monotonically increase with proximity to land transport routes. Instead, the relationship is hump-shaped: income peaks around 5 km from a major transport route, with a positive elasticity of 0.072 within 4.1 km and a negative elasticity of -0.096 beyond that distance. Population density, by contrast, falls monotonically with distance to transport routes. As a result, 85% of Americans live in places where local mean income increases with distance to transport infrastructure rather than decreasing.

Q: How does the tributary confluence identification strategy work?

A: Tributary confluences — where smaller rivers join the main river — cause sharp, localized increases in river flow rates and thus in bridge construction costs, because cost scales convexly with required span length. This makes bridges systematically more likely to be built just upstream of confluences than just downstream. The strategy compares census tracts located upstream versus downstream of the 27 major tributary confluences identified on the Mississippi and Ohio Rivers, controlling for nearest-tributary fixed effects and distance to the confluence.

Q: What is the magnitude of the connectivity difference between upstream and downstream census tracts?

A: Upstream census tracts are approximately 60% closer to a bridge than downstream tracts (coefficient of 0.91 in log distance to bridge, p < 0.01), and consequently 27% closer to the nearest major land transport route (coefficient of 0.32, p < 0.10). This asymmetry is established by 1880 and persists through 2010. The advantage arises approximately equally from proximity to railroads and primary roads.

Q: What are the causal effects of this connectivity advantage on per capita income and population density?

A: Despite being better connected, upstream census tracts have 13% lower per capita incomes (coefficient 0.14 on the downstream indicator in log per capita income, p < 0.05) and 63% higher population densities (coefficient -0.49 on the downstream indicator in log population density, p < 0.05) in 2010. Income density is higher upstream, but the difference is not statistically distinguishable from zero. Scaling the income effect by the effect on distance to land transport implies an elasticity of approximately 0.44.

Q: What pre-bridge-era placebo tests support the identifying assumption for the tributary confluence strategy?

A: Matching modern census tracts to county-level historical data from 1840 and 1850 (before substantive bridge construction began), the paper finds no statistically significant asymmetry in land values or population density upstream versus downstream of tributary confluences. Asymmetric patterns emerge only after bridge construction begins. Ferry crossing locations, traced through place names in the USGS Geographic Names database, also appear equally frequently upstream and downstream, suggesting ferries did not differentially locate upstream.

Q: How does the timing-based identification strategy work, and what is its key assumption?

A: The strategy uses a county-level panel from 1860 to 2010 and estimates event-study regressions around the first time a county experiences a 50% reduction in distance to a bridge. County fixed effects and county-specific quadratic time trends absorb all fixed differences across counties and average changes in trends. The key assumption is that the exact opening date of a bridge is exogenous to short-run deviations from local long-run growth trends — supported by the argument that major bridges involve decades-long planning processes that evolve independently of local economic fluctuations. Pre-trend tests show no significant differences in outcomes before the event.

Q: What are the quantitative effects of a major improvement in bridge access on land values and population?

A: After a county first experiences a 50% reduction in distance to a bridge, farm land values rise immediately and cumulatively by approximately 9% (cumulative effect on log land values of about 0.09) over 30 years, relative to counties with no such change. Population rises by approximately 5% (cumulative log effect of about 0.05) over the same period. The proportionally larger effect on land values than on population implies that per capita economic activity is higher in better-connected counties 30 years after the event. The divergence between land value and population effects grows over time, suggesting productivity advantages accumulate.

Q: Why does the paper use farm land values rather than other income measures in the historical panel?

A: Farm land values — the total value of farm land and buildings — are the best consistently measured proxy for total economic activity available throughout the 1860–2010 census panel. The paper notes explicitly that as the economy industrializes and urbanizes, farm land values increasingly miss urban land values, implying that the estimated effects on farm land values are likely lower bounds on the true effects on total economic activity.

Q: How does the paper address the concern that bridge timing might reflect anticipated local growth?

A: The paper shows that results hold when restricting to counties whose distance to a bridge is only affected by bridges constructed in other counties, addressing the concern that local planners might time construction in anticipation of local growth. The results are also insensitive to controlling for pre-period trends, and outcomes of interest are uncorrelated with future changes in distance to a bridge in preferred specifications.

Q: How does the paper reconcile the negative local income effect (tributary confluence strategy) with the positive aggregate effect (timing strategy)?

A: The reconciliation proceeds through a narrative account combining industrialization, urbanization, and within-city sorting. Better bridge access drives a shift toward manufacturing employment and attracts population, consistent with a productivity advantage enabling exploitation of economies of scale. Cities form around historical transport routes. As cities mature and expand, richer households sort into lower-density suburban areas further from the historical transport corridor, while lower-income households remain near or migrate to the city centre. This within-city sorting produces lower per capita incomes near transport routes even as aggregate economic activity is higher in better-connected areas.

Q: What evidence supports the within-city sorting mechanism specifically?

A: The negative income effect of proximity to transport routes is larger in more urbanized areas and in areas with higher income inequality. The effect is concentrated in areas that were more rapidly urbanizing in the 19th century, and it is stronger for non-white and low-education populations. Upstream census tracts simultaneously show higher manufacturing employment shares and higher population densities, consistent with cities having formed around transport routes, followed by residential sorting away from the core.

Q: What are the two novel identification strategies and their broader applicability?

A: The tributary confluence strategy exploits discontinuities in bridge construction costs generated by sharp increases in river flow rates at confluences; it requires only that bridges are more likely built upstream of confluences than downstream, an asymmetry the paper shows is detectable elsewhere in the world from satellite imagery. The timing strategy exploits the multi-decade planning and construction process for major bridges as a source of near-exogenous variation in opening dates. Both strategies can be applied in other settings where major rivers form substantial barriers to land transport networks.

Q: What does the paper contribute to the debate about whether early U.S. transport infrastructure followed or led economic development?

A: The results support the view that early investments in land transport infrastructure led to meaningful changes in economic geography rather than merely following pre-existing growth patterns. However, the paper finds a moderate level of responsiveness — population density responds to bridge access over several decades, not immediately — consistent with a broader literature documenting sluggish population responses to changes in economic conditions.

Tributary confluence: A location where a smaller river (tributary) joins a larger river, causing a sharp, localized increase in downstream flow rates and therefore a discontinuous increase in bridge construction costs, generating the quasi-experimental variation in bridge location exploited in the paper.

Within-city sorting: The process by which, as cities expand around historical transport routes, richer households differentially relocate to lower-density suburban areas further from the transport corridor while lower-income households remain near or migrate to the historical city centre, reversing the income gradient at small spatial scales.

Income density: The product of population density and per capita income, corresponding to total economic activity per unit area; the paper finds income density is higher in better-connected upstream census tracts even when per capita income is lower, reflecting the dominant effect of higher population density.

Farm land values: The total value of farm land and buildings, used as the best consistently available proxy for total economic activity in the 1860–2010 historical county panel; the paper treats estimated effects on farm land values as lower bounds on effects on total economic activity because farm values increasingly miss urban land as the economy industrializes.

Structural transformation: The shift in the composition of employment away from agriculture and toward manufacturing, which the paper documents occurring in counties that experience improved bridge access, interpreted as evidence that transport infrastructure provides a productivity advantage attracting industrial activity.

Distance to a bridge (as proxy for land transport access): In the study area along the Mississippi and Ohio Rivers, where all land has comparable water access, distance to the nearest bridge strongly predicts distance to the nearest major land transport route (rail or primary road), allowing bridge distance to serve as a consistent measure of transport connectivity throughout the entire study period.

Market access: A measure of economic connectivity that captures both the state of the transport network and the size of accessible markets; the paper notes that log distance to a bridge explains 46% of the variation in market access in 1890 (from Donaldson and Hornbeck’s data) with an elasticity of approximately 0.1, and that halving distance to a bridge increases market access by approximately 7%.

Catastrophes, Delays, and Learning

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a general model of experimentation under catastrophe risk in which the catastrophe is triggered when a stock variable exceeds an unknown threshold, but occurs only after a stochastic delay. The central contribution is the concept of the “legacy of the past”: at any planning date, past experiments may have already triggered a catastrophe that has not yet materialized, and the planner cannot observe whether triggering has occurred. The legacy is formally defined as the probability, conditional on survival, that a catastrophe was triggered in the past.

The model unifies two canonical but previously incompatible approaches in the literature. In the hazard-rate approach, the catastrophe is bound to happen and the planner manages its timing and severity. In the unknown-threshold approach, learning is instantaneous and the catastrophe is certainly avoided if the stock has not yet exceeded the threshold. Neither approach captures the intermediate case where the planner remains uncertain about whether the catastrophe is already underway. By introducing a delay governed by an exponential distribution with parameter α, the authors show that both approaches are limiting special cases: as α → ∞ (no delay), the legacy vanishes and the unknown-threshold approach is recovered; when the legacy is set permanently to one (catastrophe triggered with certainty), the hazard-rate approach is recovered.

Three benchmark stock levels anchor the analysis. QN is the long-run target absent any catastrophe risk. QD (“Damages”) is the optimal stabilization target when the planner knows a catastrophe was triggered in the past — it lies weakly below QN because the planner trades off current gains against the discounted marginal damage from raising the stock at the moment of eventual catastrophe occurrence. QE (“Experimentation”) is the stock level below which stabilization is suboptimal when the planner is certain no triggering has occurred — it also lies weakly below QN.

The paper’s two main theorems are distinguished by the ranking of QD and QE, which reflects whether mitigation strategies are effective.

Theorem 1 (QE < QD): When damage is not highly sensitive to the stock level at catastrophe time — so mitigation is relatively ineffective — optimal paths are monotonically increasing and converge to a long-run stock level Q∞ ∈ [QE, QD]. The stopping condition equates the marginal benefit of experimentation to a weighted average of the expected cost under the unknown-threshold approach (weight 1 − π) and the marginal damage under the hazard-rate approach (weight π), where π is the legacy at stopping time. A higher legacy at the stopping time is associated with a higher long-run stock level. A higher initial legacy induces fatalism: since the catastrophe is more likely already triggered, the planner shifts priority toward current consumption rather than caution, leading to more total experimentation.

Theorem 2 (QD < QE): When damage is highly sensitive to the stock level — so mitigation is valuable — the long-run target is uniquely QE regardless of the initial legacy. However, the short-run path is non-monotonic: for a sufficiently high initial legacy, the planner first reduces the stock sharply (lockdown, emissions cut) to mitigate pending catastrophe damages, then, as the legacy declines because no catastrophe occurs, gradually allows the stock to rise back toward QE. The direction of caution reverses relative to Theorem 1: a higher legacy now induces more caution, not less.

Applications include pandemic management (stock = infected population, catastrophe = health system collapse) and climate change (stock = cumulative CO2 emissions or atmospheric pollution stock). In the disease control application, whether a planner prioritizes economic production or mortality reduction determines which theorem governs, with the key ratio being production losses relative to mortality increases. For pandemic policy, Theorem 2 produces a formal learning-based rationale for non-monotonic “hammer-and-dance” policies (strict early lockdown followed by relaxation) that differs from prior explanations in the literature. In the carbon budget application, Proposition 5 formally proves that higher initial legacy raises the optimal carbon budget under Theorem 1 conditions, and can imply unbounded consumption (certainty of catastrophe) above a critical legacy threshold π*. Under Theorem 2 conditions (Proposition 6), the optimal policy can involve first reducing then expanding the stock before stabilizing, with both transition dates increasing in the initial legacy.

Q: What is the “legacy of the past” and how is it computed? A: The legacy πt is defined as the probability, conditional on survival to date t, that a catastrophe was already triggered by past experiments. Formally, πt = 1 − [1 − F(Qt)] / pt, where Qt is the highest stock level ever reached, F is the prior distribution over the threshold, and pt is the survival probability. A past experiment at time t’ contributes to the current legacy with weight exp[−α(t − t’)], so recent experiments matter more than distant ones. As time passes without catastrophe, the legacy of any fixed past experiment declines geometrically at rate α.

Q: How do the three benchmark stock levels QN, QD, and QE relate to each other? A: QN is the optimal long-run stock without any catastrophe. QD is defined by the condition where the marginal net benefit of increasing the stock — ν(Q) − [α/(α+δ)]D’(Q) — equals zero, and satisfies QD ≤ QN. QE is defined by ν(Q) − [α/(α+δ)]ρ(Q)D(Q) = zero, and also satisfies QE ≤ QN. The ranking between QD and QE depends on whether damage is more sensitive to the marginal increase in stock at catastrophe time (which pushes QD below QE) or to the level of the stock at triggering (which pulls QD above QE).

Q: What is the key optimality condition in Theorem 1 and how does it unify prior approaches? A: The stopping condition (equation 15) states: ν(QT) = [α/(α+δ)] × [(1 − πT)ρ(QT)D(QT) + πT D’(QT)]. When πT = 0 (no legacy, unknown-threshold limit), this reduces to the experimentation stopping condition of Tsur and Zemel, governed by the hazard rate ρ(QT) times expected loss D(QT). When πT = 1 (full legacy, hazard-rate limit), it reduces to the damage-mitigation condition governed by marginal damage D’(QT). The legacy at stopping time thus serves as the mixing weight between the two canonical approaches, embedding both as special cases.

Q: How does the initial legacy affect total experimentation under Theorem 1 versus Theorem 2? A: Under Theorem 1 (QE < QD), a higher initial legacy π0 leads to more total experimentation (higher Q∞), because the planner becomes fatalistic — since the catastrophe is more likely already triggered and mitigation is relatively ineffective, current consumption is prioritized. Proposition 5 formally proves this for the carbon budget application: the optimal stopping date T and optimal budget QT are nondecreasing in π0. Under Theorem 2 (QD < QE), a higher legacy triggers more caution in the short run (larger reduction in the stock during the mitigation phase), but the long-run target QE remains the same regardless of π0.

Q: What generates non-monotonic policies in Theorem 2, and what does this look like in the pandemic application? A: Non-monotonicity arises because the optimal response to a high legacy is first to reduce the stock sharply to limit catastrophe damages (since damage is sensitive to the stock level), and then, as time passes without catastrophe and the legacy declines, to allow the stock to recover. In the disease control application with high mortality weight, a complete lockdown is optimal in the first phase whenever the legacy is strictly positive. As the legacy declines, the lockdown is gradually relaxed, and eventually the infection level returns to its pre-lockdown level. Figures 3 and 4 show that a higher initial legacy (π0 = 0.1, 0.5, or 0.9) leads to a longer lockdown and slower recovery, though all paths converge to the same long-run infection level.

Q: How does the model’s disease control application determine which theorem governs? A: Lemma 2 states that if 1 / [1 + (Y(r+d) − Y*) / (wµdI^D)] < ρ(I^D), then I^E < I^D and Theorem 1 applies; otherwise I^E > I^D and Theorem 2 applies. The key ratio is (Y(r+d) − Y) / (wµ*d), the production loss relative to mortality increase. A planner who weights economic activity heavily (large production loss ratio) falls under Theorem 1 and tolerates rising infections; a planner who weights mortality heavily falls under Theorem 2 and imposes an initial lockdown.

Q: What is the carbon budget result under Theorem 1 (Proposition 5)? A: Under the condition u1 > [α/(α+δ)]v0 (marginal consumption value exceeds discounted marginal damage), Theorem 1 applies and there exists a critical legacy threshold π* such that: below π*, the planner consumes maximally (qt = q-bar) until a finite date T and then stops, with QE < QT < QD; above π*, the planner consumes maximally forever, triggering the catastrophe with certainty. The stopping date T and the optimal budget QT are nondecreasing functions of initial legacy π0, formally proving that higher past emissions (captured through legacy) justify higher future carbon budgets in this model.

Q: What is the carbon budget result under Theorem 2 (Proposition 6)? A: Under condition u1 < [α/(α+δ)]v0, QD < QE and Theorem 2 applies. Starting from Q0 above QE, if π0 is small enough (specifically u1 > π0[α/(α+δ)]v0), the optimal policy is to stabilize the stock forever at Q0. Otherwise, there exist two finite dates t1 < t2, both increasing in π0, such that the planner first reduces the stock at maximum rate (qt = q-bar-negative) for t < t1, then expands at maximum rate for t1 < t < t2, then stabilizes at Q0 forever. The optimal carbon budget is Q0 in all cases, showing that the long-run target is independent of legacy under Theorem 2.

Q: How does the model relate to the hazard-rate literature formally? A: Papers such as Nordhaus and others that use an exogenous hazard rate h(Qt) for catastrophe — yielding survival probability pt = p0 exp(−∫h(Qτ)dτ) — are shown to be equivalent to the special case where the catastrophe was triggered in the past (legacy = 1 permanently). Their formulation corresponds to assuming α is constant and the legacy is identically one, which reduces the law of motion for pt to pt = p0 exp(−αt). The key difference is that in the hazard-rate approach the planner can reduce the arrival rate by lowering the stock (h is increasing in Q), whereas in the authors’ model the delay parameter α is constant and policy affects only damages.

Q: What is the role of the exponential delay distribution assumption? A: The assumption that the delay τ follows an exponential distribution with parameter α is made for tractability. Under this assumption, the entire past trajectory of the stock (Qt)t≤0 can be summarized by just two state variables — the highest stock on record Q0-bar and the initial legacy π0 — because the exponential “memoryless” property means that the additional expected waiting time until catastrophe occurrence does not depend on how long the triggering has already been in effect. Without this assumption, the full chronicle of past experiments would be required as a state variable, making the problem intractable.

Q: What happens when the delay parameter α approaches zero or infinity? A: When α → ∞ (instantaneous catastrophe upon triggering), pt = 1 − F(Qt) and the legacy is identically zero, recovering the Tsur-Zemel unknown-threshold approach (Proposition 3). The optimal path converges to QE0 from below or stabilizes if already above QE0. When α → 0 (infinite delay, effectively no catastrophe), QE = QD = QN and the problem reduces to the simple stock-flow problem (Proposition 1), with the optimal path converging monotonically to QN.

Q: Does the model allow for damage mitigation after triggering but before occurrence? A: Yes, this is a key feature. The continuation payoff after catastrophe occurrence is V(QT) where QT is the stock level at the time of occurrence T, not at triggering time T(S). This means the planner can reduce the stock after triggering to lower damages — analogous to a skater turning back toward shore after the ice first cracks. The assumption that V depends on the stock at occurrence rather than at triggering or at the maximum historical level is what allows this mitigation channel and is explicitly noted as a modeling choice.

Legacy of the past (πt): The probability, conditional on survival to date t, that past experiments have already triggered a catastrophe. Formally πt = 1 − [1 − F(Qt)] / pt. Recent experiments contribute more to the legacy than distant ones, with contribution decaying at rate α. The legacy is zero when α → ∞ and is the central state variable bridging the paper’s two canonical extremes.

QE (“Experimentation” threshold): The stock level at which the net marginal gain from further experimentation, defined as ν(Q) − [α/(α+δ)]ρ(Q)D(Q), equals zero, under the assumption that no catastrophe has been triggered. Below QE, stabilization is suboptimal; above QE, the planner does not experiment further when the legacy is zero.

QD (“Damages” threshold): The stock level at which the net marginal benefit from holding the stock, defined as ν(Q) − [α/(α+δ)]D’(Q), equals zero, under the assumption that the catastrophe is known to have been triggered. QD ≤ QN and represents the optimal long-run target when the hazard-rate approach applies.

Marginal payoff ν(Q): Defined as uq(0, Q) + (1/δ)uQ(0, Q), it measures the net gain from marginally increasing the flow when the stock is stabilized at Q. It is strictly decreasing in Q under Assumption 1 and equals zero at QN.

Damage function D(Q): Defined as (1/δ)u(0, Q) − V(Q), it measures the welfare loss from catastrophe occurrence when the stock is Q at occurrence time, relative to permanent stabilization at Q. Assumed weakly positive and weakly increasing in Q.

Survival probability (pt): The probability, computed from prior beliefs F at the beginning of times, that the catastrophe has not yet occurred by date t. Its law of motion is ṗt = α[1 − F(Qt) − pt], driven solely by the catastrophe parameter α and the current maximum stock Qt.

Fatalism (under Theorem 1): The policy implication that a higher legacy — meaning a higher probability the catastrophe is already triggered — leads the planner to increase the stock further and accept more experimentation, because mitigation is relatively ineffective (QE < QD) and current consumption must be enjoyed before the catastrophe arrives.

Choice and Opportunity Costs

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

This paper develops a unified choice-theoretic framework in which agents evaluate alternatives not in isolation but relative to their opportunity costs — the alternatives they forgo. The central departure from classical theory is the relaxation of additive separability between benefits and costs. In the standard additive model, accounting for opportunity costs is behaviourally equivalent to simple utility maximisation: a decision maker who correctly perceives the feasible set and maximises an additively separable utility will make identical choices whether or not opportunity costs are explicitly considered (the paper calls this the irrelevance of opportunity costs under additivity, formally establishing it as a general result). Once additive separability is relaxed, however, opportunity costs become non-trivial and generate a genuinely distinct theory of choice.

The primitive of the model is a net preference — an asymmetric binary relation on pairs (x, y) of distinct alternatives, where (x, y) ≻ (w, z) means the agent strictly prefers obtaining x while forgoing y over obtaining w while forgoing z. Because the opportunity cost of a chosen alternative depends on what else the agent would choose, and vice versa, choice emerges from an intrapersonal equilibrium rather than from direct maximisation.

The paper defines and axiomatically characterises two nested models. The Recursive Opportunity Model (ROM) adopts a behavioural definition of opportunity costs: the cost of the chosen alternative x in menu A is c(A \ x), the alternative that would actually be chosen were x unavailable; the cost of every unchosen alternative is x itself. This recursive structure is completely characterised by a single observable condition — Weak Path Independence (WPI): if x is chosen when added to a menu A, then x must also be chosen in a pairwise comparison against c(A). WPI is shown to imply Always Chosen (AC) — that a Condorcet winner is always selected — but it permits pairwise cycles of choice (failures of No Binary Cycles). Rationality within the ROM requires additionally that the net preference be a strict order satisfying Congruence, an acyclicity condition on the gross preference induced by the net preference. Even then, the utility function being maximised need not coincide with the gross preference naturally implied by the underlying psychological net preference, raising a welfare identification problem.

The Opportunity Model (OM) generalises the ROM by allowing the opportunity cost of the chosen alternative to be any unchosen alternative rather than the recursively determined one. This relaxation permits both pairwise cycles and menu effects (Condorcet violations). The OM is completely characterised by Never Chosen (NC): an alternative that loses every pairwise comparison within a menu (a Condorcet loser) cannot be chosen. Imposing a strict order and Congruence on the net preference of an OM rules out only pairwise cycles, leaving menu effects intact. Full rationality within the OM is restored only with the additional assumption that opportunity costs are non-decreasing in the induced gross preference as the feasible set expands (the Increasing Opportunity Model).

Extensions characterise multivalued versions of both models (M-ROM and M-OM) via adapted axioms on choice correspondences, and show that several known behavioural models in the literature — including list-rationalizable choice and game-tree rationalizable choice — satisfy WPI and thus are instances of ROM. Applications demonstrate that OMs can represent the attraction effect and the multiple decoy effect, providing a preference-maximisation account without appealing to bounded cognition, and that ROMs can represent intransitive pairwise choices via smooth parametric net preferences, avoiding the discontinuities of lexicographic semiorder models.

Q: What is the paper’s foundational definition of opportunity cost, and how does it differ from the standard textbook definition? A: The paper defines the opportunity cost of the chosen alternative x in menu A as the alternative that would actually be chosen from A \ {x} — that is, c(A \ {x}). The opportunity cost of any unchosen alternative y is the actual choice x. The standard textbook definition — “the next-best feasible alternative” — presupposes context-independent, additively separable preferences, precisely the assumption the paper relaxes. The behavioural definition is grounded directly in the agent’s own choice function, making it consistent with non-separable evaluations.

Q: Under what conditions do opportunity costs become irrelevant, and why? A: If preferences admit an additively separable utility representation u, then for any finite menu A and any two alternatives x and y, u(x) ≥ u(y) if and only if u(x) − max_{a ∈ A{x}} u(a) ≥ u(y) − max_{a ∈ A{y}} u(a). Net utility maximisation and gross utility maximisation rank alternatives identically. Opportunity costs become non-trivial only when additive separability is relaxed — at that point, the agent’s comparative evaluation of (alternative, cost) pairs can produce choices that no gross utility function rationalises.

Q: What is the Recursive Opportunity Model (ROM) and what single axiom characterises it? A: A choice function c is a ROM if there exists a net preference ≻ such that for every menu A and every unchosen alternative x, the chosen alternative evaluated at its opportunity cost is preferred to x evaluated at c(A). This is equivalent to the choice function satisfying Weak Path Independence (WPI): if x ∉ A and x = c(A ∪ {x}), then x = c({x, c(A)}). WPI is necessary and sufficient for a ROM (Theorem 1). It is not sufficient for full rationality, as it permits pairwise cycles while ruling out menu effects.

Q: What kinds of irrationality can a ROM exhibit, and what kinds does it preclude? A: The paper establishes (Corollary 1) that WPI implies Always Chosen — a ROM always selects the Condorcet winner when one exists. Therefore, the only admissible form of irrational behaviour in a ROM is pairwise cycles (failures of No Binary Cycles). Condorcet violations (menu effects) are precluded. A ROM becomes fully rational if and only if it additionally satisfies No Binary Cycles.

Q: What additional condition on the net preference guarantees that a ROM is rational? A: Theorem 2 establishes that a choice function is rational if and only if it is a ROM generated by a net preference that is a strict order (complete, asymmetric, transitive) satisfying Congruence. Congruence requires that the induced binary relation P≻ on alternatives — defined by xP≻y whenever there exists z such that (x, z) ≻ (y, z) or (z, y) ≻ (z, x) — is acyclic. For a (u, v)-additive net preference, Congruence holds if and only if u and v are ordinally equivalent.

Q: Can rational behaviour generated by a ROM be welfare-analysed using revealed preference in the standard sense? A: No — and this is a key warning in the paper. Even when a ROM with a strict order and Congruence produces fully rational behaviour, the utility function being maximised need not coincide with the gross preference P≻ naturally induced by the underlying net preference. The paper provides an explicit example (Remark 1, equation 10) in which the choice-rationalising order P is xPyPz while the induced preference is xP≻zP≻y. The utility “revealed” by choice may diverge from the psychological primitive driving that choice, undermining the normative authority of standard revealed preference welfare analysis.

Q: What is the Opportunity Model (OM) and how does it extend the ROM? A: The OM relaxes the recursive assumption by allowing the opportunity cost of the chosen alternative to be any unchosen element of the menu rather than specifically c(A \ c(A)). This breaks the recursive structure while preserving the intrapersonal equilibrium character (the choice still affects the net value of alternatives). The OM is completely characterised by Never Chosen (NC): no Condorcet loser can be chosen (Theorem 3). Unlike the ROM, an OM may fail to select the Condorcet winner, permitting both pairwise cycles and Condorcet violations.

Q: What is the Increasing Opportunity Model and when does it restore full rationality? A: An IOM is an OM in which the opportunity function o is monotone in the sense that if A ⊃ B and o(A) ≠ o(B), then o(A) is ranked higher than o(B) in the induced gross preference P≻. Intuitively, opportunity costs do not decrease as the feasible set expands. Theorem 5 establishes that a choice function is rational if and only if it is an IOM generated by a net preference that is a strict order satisfying Congruence. Full rationality within the OM thus requires both the internal consistency of the net preference (strict order, Congruence) and this monotonicity of opportunity costs.

Q: How does the paper explain the attraction effect using the OM? A: In the canonical formulation, c({x,y}) = x, c({y,d}) = y, c({x,d}) = x, and c({x,y,d}) = y, where d is a decoy. This pattern is incompatible with gross preference maximisation. The paper represents it as an OM with opportunity function o({x,y,d}) = d and a strict net preference order yd ≻ xy ≻ yx ≻ xd ≻ dx ≻ dy. The psychological interpretation is that the introduction of the decoy shifts the comparator for y from x to d; y looks more favourably comparable to d than x does, so the equilibrium where y is chosen is selected. No bounded cognition or imperfect attention is assumed.

Q: How does the framework account for multiple decoys? A: With decoys dx and dy specific to x and y respectively, the observed pattern c({x,y}) = x and c({x,y,dy}) = y and c({x,y,dx,dy}) = y can be represented as an OM with a transitive net preference satisfying xdx ≻ ydy ≻ xy ≻ yx ≻ dyy ≻ dxx and opportunity function o({x,y,dx,dy}) = dx, o({x,y,dy}) = dy. The paper notes this net preference can be extended to a strict order while preserving the choice pattern. This accommodates a phenomenon that poses a challenge to standard theoretical choice literature (per Masatlioglu, Nakajima and Ozbay [25]).

Q: How does the ROM explain intransitive choices more smoothly than lexicographic semiorder models? A: The paper shows that the Tversky (1969) cyclical pattern c({x,y}) = x, c({y,z}) = y, c({x,z}) = z with x=(115,7), y=(117,3), z=(120,0) can be generated by net preferences that admit smooth parametric representations. Specifically, for any two alternatives w=(a,b) and z=(c,d), the paper proposes (w,z) ≻ (z,w) iff (max{a−c, b−d})² > k(min{a−c, b−d})², where k is a relative sensitivity parameter. For k=1/2 this yields the required cycle. Lexicographic models require sharp discontinuities in preference and systematic avoidance of trade-offs, which are often viewed as implausible within the standard economic paradigm; the smooth parametric form avoids these features.

Q: What is the relationship between ROMs and previously studied choice models in the literature? A: Several known models satisfy WPI and are therefore, by Theorem 1, instances of ROMs: specifically, Rationalizability by Game Trees (Xu and Zhou) and List-Rationalizable Choice (Yildiz) are shown to satisfy WPI. The two-stage choice model of Bajraj and Ulku satisfies NC but not WPI, making it an OM but not a ROM. The net preference being maximised in each case can in principle be recovered using the explicit construction in the proof of Theorem 1.

Q: How does the ROM relate to Koszegi-Rabin personal equilibrium? A: Both models involve preferences that depend on a variable determined endogenously by choice, requiring an intrapersonal equilibrium concept in which the agent’s conjectures about their own behaviour must be internally consistent. The key difference is that in Koszegi-Rabin the psychological primitive is a set of reference-dependent preferences ≻r on alternatives in X (where r is the reference point), and equilibrium requires c(A) ≻{c(A)} y for all y ∈ A \ c(A). In the ROM, the primitive is a preference on pairs of distinct alternatives, and the opportunity cost differs for each alternative being compared (the chosen alternative has one opportunity cost, each unchosen alternative has a different one, namely c(A) itself).

Net preference: An asymmetric binary relation on pairs (x, y) of distinct alternatives, where (x, y) ≻ (w, z) means the agent strictly prefers to be in a situation where they choose x while forgoing y over a situation where they choose w while forgoing z. The primitive is defined on X = {(x, y) ∈ X × X : x ≠ y}, without imposing additive separability.

Recursive Opportunity Model (ROM): A choice function c is a ROM if there exists a net preference ≻ such that for every menu A and every unchosen x, the pair (c(A), c(A \ c(A))) ≻ (x, c(A)). The opportunity cost of the chosen alternative is defined recursively as c(A \ c(A)); choice results from intrapersonal equilibrium rather than simple maximisation.

Opportunity Model (OM): A generalisation of the ROM in which the opportunity cost of the chosen alternative can be any unchosen alternative in the menu (not necessarily the recursively determined one). Characterised by Never Chosen: no Condorcet loser can be chosen. Permits both pairwise cycles and Condorcet violations.

Weak Path Independence (WPI): The axiom characterising ROMs: if x ∉ A and x = c(A ∪ {x}), then x = c({x, c(A)}). Equivalently, if an alternative is chosen upon being added to a menu, it must also win in a pairwise comparison with what was previously chosen from the original menu.

Congruence: A consistency condition on net preferences requiring that the induced binary relation P≻ — defined by xP≻y whenever there exists z such that (x,z) ≻ (y,z) or (z,y) ≻ (z,x) — is acyclic. For a (u,v)-additive net preference, Congruence holds if and only if u and v are ordinally equivalent. Together with a strict net preference order, Congruence in a ROM is equivalent to rational choice.

Intrapersonal equilibrium: The concept underlying both models: an agent is in equilibrium when selecting x from A if they correctly anticipate their own contingent behaviour across hypothetical scenarios (i.e., they use the actual choice function c to evaluate what they would choose from A \ {x}), and the chosen alternative is net-preference-maximal given those consistent conjectures.

Never Chosen (NC): The axiom characterising OMs: an alternative that is a Condorcet loser — losing in every pairwise comparison within a menu — cannot be chosen from that menu. NC is weaker than WPI (which implies both Always Chosen and Never Chosen) and is the precise behavioural content of the OM.

Closing Gender Gaps Through Workplace Diversity: The Intergenerational Effects of World War I

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether exposure to greater female representation in the workplace can persistently reduce intergenerational gender gaps in labor market outcomes. The authors exploit the sudden, city-by-department variation in female employment within the U.S. federal government triggered by World War I mobilization. Using the Official Registers of the United States — biennial personnel rosters covering the near-universe of federal employees from 1913 to 1921 — linked to full-count decennial censuses (1900–1940), they construct a granular measure of each office’s (city × department) change in female share between 1915 and 1919, then trace labor force outcomes for the children of incumbent civil servants in the 1940 Census.

WWI caused the female share of the federal civilian workforce to jump by 13 percentage points — a doubling within two years (1917–1919). These wartime female entrants were younger, more likely to be single, more educated, more geographically mobile, and less likely to have been previously employed than their male counterparts, suggesting the war mobilized a previously untapped labor pool. The increase was driven almost entirely by clerical positions: the female share of the federal clerical workforce rose from roughly 30% to nearly 70% within two years.

The main finding is that a one standard deviation (SD) increase in parental exposure to female co-workers reduces the gender gap in labor force participation (LFP) among children of incumbent civil servants by 4.1–4.6 percentage points in the within-city, within-department specification — a decline in the mean gender LFP gap of approximately 8.6–9.6% by 1940. This effect is entirely driven by a higher propensity of daughters to work; sons’ LFP is unaffected. The intergenerational effect operates primarily through exposed fathers, including fathers without working wives, identifying a channel beyond the mother-to-daughter vertical transmission emphasized in prior literature. Children who were teenagers at the time of parental exposure show the largest effects, consistent with formative-years malleability. A placebo test using civil servants who left the same offices before the wartime shock shows no comparable effect, ruling out time-invariant office-level selection.

Parental exposure extends beyond the public sector: the private sector LFP effect is comparable in magnitude to the public sector effect. The gender earnings gap among children of exposed civil servants narrows by 12%, driven by daughters moving into higher-paying, previously male-dominated positions rather than by differences in hours or weeks worked. Marriage, fertility, and schooling differences only partially mediate the LFP effect, with a residual exposure effect remaining after controlling for these proximate determinants.

At the aggregate level, a 1 SD increase in city-level exposure to female federal workers raises overall female LFP by 0.9–1.0 percentage points, with no effect on male LFP, and the effect persists through 1940. A back-of-envelope calculation implies each additional female wartime civil service entrant generated approximately 2.4 additional women entering the workforce — a multiplier effect. Neighborhood-level analysis shows LFP gains are concentrated in enumeration districts where wartime female civil servants resided, and cities with greater female federal employment exposure also saw faster women’s club membership growth after WWI.

The scope conditions are important: the sample covers 70 cities and 8 federal departments with meaningful pre-war staffing; children must have been born by 1917; and the 1940 outcomes reflect adulthood labor decisions in a labor market shaped by subsequent decades of change. The design relies on within-city and within-department residual variation in female share change being conditionally exogenous, supported by lack of correlation with pre-war office characteristics.

Q: What was the scale of the WWI shock to female federal employment? A: The U.S. entry into WWI in April 1917 triggered a near-doubling of total federal civilian employment from roughly 150,000 to over 300,000 workers by 1919. Within this expansion, the share of female civil servants increased by 13 percentage points — a doubling of the female share within two years. The increase was driven almost entirely by clerical positions, where the female share rose from around 30% to nearly 70%.

Q: How do the authors measure parental exposure to female co-workers? A: Exposure is measured as the change in the share of female civil servants at the city-by-department (“office”) level between 1915 and 1919. The sample is restricted to offices with at least 20 civil servants in 1915 and cities with at least two federal departments, yielding 70 cities and 8 departments. The interquartile range of exposure across offices is approximately 10 percentage points, and cross-city and cross-department variation explains 58% of the overall variation, leaving substantial residual office-level variation for identification.

Q: What is the main intergenerational finding and its magnitude? A: A 1 SD increase in parental exposure to female co-workers increases the relative likelihood that a daughter works (compared to a son) by 2 percentage points in the baseline specification, and by 4.1–4.6 percentage points in the preferred within-city and within-department specification. Since daughters of civil servants are on average 48 percentage points less likely than sons to be in the labor force in 1940, this corresponds to closing the mean gender LFP gap by approximately 8.6–9.6%.

Q: Does the effect operate through daughters or sons? A: The effect is entirely driven by daughters. Parental exposure to female co-workers has no statistically discernible impact on the labor force participation of sons. The decline in the gender LFP gap is thus attributable to a higher propensity of daughters of exposed civil servants to work.

Q: What is the key placebo test, and what does it show? A: The authors exploit high-frequency personnel records to identify civil servants who selected into the same offices that would later be exposed but who left before the wartime shock occurred. These pre-departure leavers show no intergenerational exposure effects on their children’s LFP, ruling out the interpretation that time-invariant selection into particular offices drives the results.

Q: Which parent serves as the primary channel of transmission? A: Exposed fathers are the primary conduit. The effect for daughters is precise and sizable even when restricting the sample to fathers without working wives, suggesting the channel does not depend on children observing maternal employment. While the estimated effect through mothers is positive, it is imprecise — likely due to the small sample of female incumbent civil servants. This identifies fathers as a new channel of vertical intergenerational norm transmission, beyond the mother-to-daughter pathway emphasized in prior literature.

Q: How does children’s age at the time of parental exposure moderate the effect? A: The exposure effects are concentrated among children who were teenagers at the time of parental exposure during WWI. Children who were older and more likely to have already left the household or formed fixed beliefs show little to no detectable effect. This pattern is consistent with the formative-years hypothesis that experiences during adolescence shape lifetime economic behavior.

Q: Does the intergenerational effect extend beyond the public sector? A: Yes. The private sector LFP effect for daughters is comparable in magnitude to the public sector effect, with a 1 SD increase in parental exposure having approximately equal effects on LFP within public and private employment. There is also no measurable shift toward clerical occupations specifically, suggesting the channel is a broader change in attitudes toward women working, not transmission of information about specific government or clerical jobs.

Q: What is the effect on the gender earnings gap? A: A 1 SD increase in parental exposure to female co-workers closes the gender earnings gap among children of civil servants by 12%. This is not driven by differences in weeks or hours worked, but rather by daughters of exposed parents selecting into higher-paying and previously male-dominated occupations.

Q: How do the authors address the possibility that the results reflect local labor market conditions rather than parental exposure per se? A: By 1940, 67% of civil servant children lived in a city different from their parent’s WWI-era city. Even among children who moved to the same destination city — and thus face identical labor market conditions — variation in parental exposure at the origin city-by-department remains highly predictive of daughters’ LFP. Comparing children moving from the same origin city to the same destination city, those with parents in higher-exposure departments still show higher LFP, pointing to cultural transmission rather than local labor market demand.

Q: What do the marriage and fertility results indicate about mechanisms? A: Daughters of more exposed civil servants are less likely to be married (a 1 SD increase in parental exposure reduces the relative likelihood of daughters being married by 3.7 percentage points) and tend to have fewer children by 1940. A mediation exercise shows these observable differences in marriage, fertility, and education only partially explain the LFP increase; a statistically significant and economically large residual exposure effect remains, consistent with parental exposure shifting broader gender norms rather than only proximate determinants of labor supply.

Q: What does the spousal work decision evidence contribute? A: A 1 SD increase in male civil servants’ exposure to female co-workers increases the propensity of their subsequent wife to work by 0.5 percentage points after WWI. The effect is driven by marriages formed after the exposure and is not mechanically explained by men marrying their female co-workers. This revealed preference measure supports the interpretation that exposure changed men’s attitudes toward women’s work.

Q: What do naming patterns suggest about changing attitudes? A: Exposed parents are more likely to give daughters names that are less feminine — specifically, names with a lower share of vowels or less likely to end with a vowel — for daughters born after WWI. No comparable effect is observed for sons’ names. This provides supplementary evidence of a shift in paternal attitudes following workplace exposure to female co-workers.

Q: What are the aggregate city-level effects on female LFP? A: In a difference-in-differences design using cross-city variation in female federal worker exposure before and after WWI, a 1 SD increase in city-level exposure raises aggregate female LFP by 0.9–1.0 percentage points, with no effect on male LFP. The effect is persistent through 1940 and city-level exposure is uncorrelated with female LFP prior to WWI. A back-of-envelope calculation implies each additional female wartime entrant generated approximately 2.4 additional women entering the broader workforce — a social multiplier.

Q: Is there evidence of horizontal (non-family) transmission? A: Yes. The aggregate LFP gains are concentrated almost entirely in census enumeration districts where female wartime civil servants resided; neighboring districts without female entrants do not see comparable gains. Cities with greater increases in female federal employees also experienced faster growth in women’s club memberships, with this pattern appearing only after WWI and coinciding with the rise in female LFP. Both findings are consistent with social learning operating through residential proximity and community networks.

Q: How robust are the results to potential selection bias from imperfect census linking? A: The propensity of a civil servant’s child to be linked to the 1940 Census is — conditional on city and department fixed effects — uncorrelated with the parental exposure measure. The authors apply inverse probability weighting (IPW) to ensure the matched sample is balanced on baseline characteristics, and results remain virtually identical. Estimates are also stable across different linking strategies individually.

Q: What instrumental variable strategy is used and what does it find? A: The authors instrument for office-level female share change using the interaction of the 1915 clerical workforce share and an indicator for war-related departments — a pre-determined source of variation in the capacity and demand for female clerical workers. The IV estimates are consistent with the OLS main specification: parental exposure to female co-workers closes the children’s gender LFP gap.

Q: What is the policy implication regarding public sector hiring? A: The paper suggests that increasing gender representation within public sector employment can have labor market implications that extend well beyond the organization itself — across generations through vertical intergenerational transmission and across the broader community through horizontal social spillovers. The findings imply that public sector diversity policies can serve as a lever for broader, persistent reductions in gender gaps in the private labor market.

Office-level exposure: The city-by-department measure of the change in female share of civil servants between 1915 and 1919, capturing the granular intensity of each workplace unit’s contact with wartime female entrants; the interquartile range across offices is approximately 10 percentage points.

Intergenerational gender gap in LFP: The difference in labor force participation rates between daughters and sons of incumbent civil servants measured in 1940 adulthood, used as the primary outcome to capture whether parental workplace exposure transmits to children’s labor supply decisions.

Vertical transmission: The intergenerational channel through which exposed parents — identified here primarily as fathers, including those without working wives — convey changed attitudes or information about female work to their children, closing the gender LFP gap.

Horizontal transmission: The community-level channel through which the increased presence of female civil servants in a city spreads changed norms or information about women’s work to women who are not daughters of exposed co-workers, operating through residential proximity and social networks such as women’s clubs.

Social multiplier: The amplification of the direct effect of hiring female workers through behavioral spillovers; the authors’ back-of-envelope calculation estimates that each additional female wartime civil service entrant generated approximately 2.4 additional women entering the workforce.

Formative years: The period of adolescence during which children are argued to be most malleable in forming preferences and beliefs; exposure effects in this paper are concentrated among children who were teenagers at the time of parental exposure, with older children showing little effect.

Source text origin: The authors’ classification of whether a summary is based on full working paper text (pdf or oa-html) vs. abstract only; in this workflow, abstract-only is a hard block for summary generation.

Coarse Bayesian Updating

Mon, 01 Jan 0001 00:00:00 +0000

This paper introduces and axiomatically characterizes Coarse Bayesian updating, a generalization of Bayes’ rule designed to accommodate the wide empirical evidence that individuals systematically deviate from standard Bayesian belief revision. The research question is: what is the minimal, tractable, axiomatically grounded generalization of Bayes’ rule that can accommodate heterogeneous non-Bayesian behaviors — including under-reaction, over-reaction, asymmetric updating, limited perception, and motivated reasoning — while remaining portable to standard economic settings?

The paper takes as primitive a finite state space Omega = {1, …, N} and an updating rule mu: S -> Delta assigning posterior beliefs to signals, where signals represent likelihood profiles from stochastic information structures. No data are used; the methodology is axiomatic decision theory combined with analysis of the model’s implications in static, dynamic, and decision-theoretic settings.

A Coarse Bayesian agent is characterized by (i) a partition of the probability simplex Delta into convex cells, and (ii) a representative distribution for each cell, one of which is the prior. Upon observing a signal, the agent determines which cell contains the Bayesian posterior and adopts the representative of that cell as his posterior belief. The agent need not point-identify the Bayesian posterior; he merely approximates it by identifying which cell it belongs to.

The central characterization result (Theorem 1) establishes that an updating rule has a Coarse Bayesian representation if and only if it satisfies three axioms: Homogeneity (beliefs depend only on likelihood ratios of the signal, not its scale), Cognizance (if two signals induce the same belief, then a garbled signal indicating one of them was generated also induces that belief), and Confirmation (if a signal is perfect evidence of some feasible belief, the agent adopts that belief). The representation — partition, representative points, and prior — is unique.

Proposition 1 shows that, under mild regularity conditions, strengthening any of the three axioms to an if-and-only-if form forces the agent to be perfectly Bayesian. This identifies the Coarse Bayesian framework as a qualitatively small but substantively rich departure from Bayes’ rule. The converse statements identify three necessary non-Bayesian behaviors exhibited by any proper Coarse Bayesian: (i) treating some signals as equivalent when a Bayesian would not; (ii) collapsing to a default belief when uncertain between two signals the agent would otherwise distinguish; (iii) false extrapolation — arriving at a belief via signals that are not perfect evidence of it.

In dynamic settings, Pooled Coarse Bayesian rules (which apply the full signal history at each period) are invariant to signal ordering and pooling and converge whenever Bayesian beliefs do, though to the representative point of the cell containing the true state rather than the true state itself. Sequential Signal Distortion rules are invariant to signal ordering but not pooling, and beliefs converge almost surely — but not necessarily to the true state (Example 1 illustrates convergence to the wrong state in a two-state setting). Sequential Coarse Bayesian rules need not satisfy either form of path-independence and need not converge at all.

In the decision-theoretic application (Section 4), a Coarse Bayesian’s value of information is posterior-separable and generally violates the Blackwell (1951) information ordering — more informative experiments need not be valued more highly. Two Coarse Bayesians are shown to be identical (same cells and representative points) if and only if they benefit from the same Blackwell improvements, providing a behavioral identification result. Agents with finer partitions are more sophisticated (higher ex-ante value of information), while agents with larger distortions from Bayesian posteriors are more biased (larger worst-case losses relative to a Bayesian). Neither greater sophistication nor lower bias implies being better off at all menus or signal realizations.

Q: What are the three axioms that characterize Coarse Bayesian updating, and what property of Bayes’ rule does each capture? A: Homogeneity requires that beliefs depend only on likelihood ratios of the signal — if two signals are proportional (s ~ t), they induce the same posterior. Cognizance requires that if two signals induce the same belief, then a garbled signal indicating that one of them was generated also induces that belief (mu_{s+t} = mu_s when mu_s = mu_t). Confirmation requires that if a signal is perfect evidence of some feasible belief — i.e., the Bayesian posterior at that signal equals a candidate belief — then the agent adopts that belief. Each axiom is satisfied by standard Bayesian updating.

Q: In what sense is Coarse Bayesian updating a “small” departure from Bayes’ rule? A: Proposition 1 establishes that strengthening any one of the three axioms to an if-and-only-if form forces the agent to be perfectly Bayesian. The converses are: (i) different likelihood ratios lead to different posteriors; (ii) if a garbled signal does not change beliefs, then the two signals must induce the same belief individually; (iii) if a signal induces the same posterior as another, then it must be perfect evidence of that posterior. Any Coarse Bayesian satisfying any one of these is in fact perfectly Bayesian, meaning the three axioms together come very close to fully characterizing Bayesian rationality.

Q: What non-Bayesian behaviors does the model generate as special cases? A: The framework generates under-reaction (representative points of cells close to the prior boundary), over-reaction (representative points at the far boundary), asymmetric updating (favoring one state, making upward revision easier than downward), limited perception (the agent retains the prior unless the Bayesian posterior is sufficiently far from the prior), extreme-belief aversion (the agent applies Bayes’ rule except when posteriors are near degenerate distributions), and reactions to unexpected news (non-Bayesian behavior only when signals have low prior probability). In each case the Coarse Bayesian Representation provides an axiomatic foundation via Axioms 1–3.

Q: What are the three necessary non-Bayesian behaviors exhibited by any proper (non-Bayesian) Coarse Bayesian? A: These follow from the negations of properties (i)-(iii) in Proposition 1. First, there exist signals s and t that are not proportional yet induce the same posterior — the agent treats informationally distinct signals as equivalent. Second, there exist signals s and t such that mu_s ≠ mu_t but mu_{s+t} = mu_s — signals the agent distinguishes individually collapse to a default when the agent is uncertain which one was generated. Third, there exist signals s and t with mu_s = mu_t where t is not perfect evidence of mu_s — a form of false extrapolation. Together, these three biases account for all non-Bayesian behavior the model generates.

Q: How does the model accommodate globally uniform biases like always-under-reaction, and how common does it predict such behavior to be? A: Global under-reaction requires representative points of cells to sit on their cell boundaries (as close to the prior as possible given the partition). This is a non-generic, hairline case — representative points generically lie in the interior of their cells, so a typical Coarse Bayesian under-reacts to some signals and over-reacts to others depending on which cell the Bayesian posterior falls into. The model additionally predicts local stability: if an agent over-reacts to signal s, nearby signals typically produce the same response; if an agent is Bayesian at s, nearby signals are almost surely also Bayesian.

Q: What does the model imply about dynamic updating under sequential signal-by-signal processing versus pooled processing? A: Pooled Coarse Bayesian rules apply the full signal history at each period, are invariant to both signal ordering and signal pooling, and converge almost surely whenever Bayesian beliefs converge — but to the representative point of the cell containing the true state, not necessarily the true state itself. Sequential Signal Distortion rules are invariant to signal ordering but not signal pooling, and also yield almost-sure convergence though potentially to the wrong state (Example 1 shows this for a two-state setting). Sequential Coarse Bayesian rules need not be invariant to either form of path-dependence and need not converge at all.

Q: How does the paper provide a behavioral identification of the model’s parameters? A: Theorem 1 establishes that the partition, representative points, and prior are uniquely determined by the agent’s updating rule alone — they are identifiable from observable updating behavior without additional assumptions. In the decision-theoretic setting of Section 4, a stronger result holds: two Coarse Bayesians are identical (same cells and same representative points) if and only if they benefit from the same Blackwell improvements across all menus (decision problems). This means the model’s parameters can be uniquely identified from menu-contingent rankings of Blackwell-comparable experiments.

Q: Does the Coarse Bayesian framework respect the Blackwell information ordering, and what characterizes when Blackwell improvements are beneficial? A: Unlike Bayesians, Coarse Bayesians typically violate the Blackwell ordering — they need not assign higher ex-ante value to more informative experiments. The paper characterizes the menus (decision problems) for which a given Coarse Bayesian benefits from Blackwell improvements, and shows this characterization runs deep: the complete set of such menus fully identifies the agent’s representation.

Q: How do the sophistication and bias orderings relate to welfare? A: An agent is more sophisticated if he employs a finer partition; more-sophisticated agents have a higher ex-ante value of information. An agent is more biased if his updating rule exhibits larger distortions from Bayesian posteriors; greater bias is characterized by greater worst-case losses relative to a Bayesian. Crucially, neither greater sophistication nor lower bias implies the agent is better off at all menus or signal realizations — welfare improvements require the agent to be perfectly Bayesian on a strictly larger set of signal realizations, giving rise to a third ordering that jointly refines the other two.

Q: How does the model relate to Wilson (2014) and Ortoleva (2012)? A: Wilson (2014) studies optimal updating for a boundedly rational agent with K memory states over binary decisions: each memory state is associated with a convex set of posteriors and a representative, so the optimal protocol is a dynamic Coarse Bayesian updating procedure. However, Wilson’s parameters are endogenous (determined by signal structure, stakes, and the bound K), whereas Coarse Bayesian updating does not require optimality or a bound on the number of cells — the model can accommodate behavior (e.g., Bayesian updating except at “extreme” signals) that Wilson’s model cannot. Ortoleva’s (2012) Hypothesis Testing model applies Bayes’ rule when the prior probability of a signal exceeds a threshold epsilon and otherwise uses a maximum-likelihood criterion; Coarse Bayesian updating can accommodate similar behavior, and the paper shows that Coarse Bayesian rules can be expressed as Maximum-Likelihood rules when there are only two states, but neither class subsumes the other in general — Maximum-Likelihood rules may violate Confirmation.

Q: What are the main limitations of the Coarse Bayesian framework? A: The paper identifies four. First, only likelihood ratios of the realized signal matter — sensitivity to framing and extraneous environmental features are ruled out. Second, beliefs must be probability distributions, so phenomena like the conjunction fallacy (where subjects assign higher probability to a conjunction than a component event) are outside the model’s scope. Third, the model exhibits discontinuities when signal perturbations move the Bayesian posterior across a cell boundary — a feature shared with Wilson (2014), Ortoleva (2012), and related models. Fourth, cells must be convex (driven by Cognizance); dropping Cognizance allows non-convex cells but removes the normative foundation that agents correctly forecast their own updating behavior.

Coarse Bayesian Representation: A pair consisting of a partition P of the probability simplex Delta into convex cells and a profile of representative distributions (one per cell, including the prior), such that the agent’s posterior after observing signal s equals the representative of the cell containing the Bayesian posterior B(mu_e|s).

Homogeneity: The axiom that if two signals are proportional (s ~ t, meaning s = lambda*t for some lambda > 0), they induce the same posterior belief — updating depends only on likelihood ratios, not signal scale.

Cognizance: The axiom that if signals s and t induce the same posterior, then the garbled signal s+t (indicating that either s or t was generated) also induces that belief — the agent correctly forecasts his own updating behavior.

Confirmation: The axiom that if a signal constitutes perfect evidence of some feasible belief (i.e., the Bayesian posterior equals a candidate belief), the agent adopts that belief — candidate beliefs are adopted when the signal confirms them exactly.

Signal Distortion Representation: An equivalent representation of Coarse Bayesian behavior as a function d: S -> S that distorts signals before Bayesian updating is applied (mu_s = B(mu_e|d(s))), satisfying properties analogous to the three axioms; equivalent to the partition representation in static settings but distinct in dynamic settings.

Blackwell Information Ordering: The partial order on experiments under which sigma is more informative than sigma’ if sigma can be obtained from sigma’ by a garbling; Bayesians always weakly prefer more informative experiments in this ordering, but Coarse Bayesians typically do not.

Sophistication Ordering: The partial order under which one Coarse Bayesian is more sophisticated than another if he employs a finer partition; more-sophisticated agents exhibit greater responsiveness to information as measured by ex-ante value of information.

Bias Ordering: The partial order under which one Coarse Bayesian is more biased than another if his updating rule exhibits larger distortions away from Bayesian posteriors; greater bias is characterized by larger worst-case losses relative to a Bayesian benchmark.

Competing under Information Heterogeneity: Evidence from Auto Insurance

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies imperfect competition in selection markets where competing firms have heterogeneous information about consumers — a layer of asymmetry distinct from the classic buyer-seller information gap. The central questions are: how do inter-firm information asymmetries shape equilibrium pricing, consumer sorting, and market efficiency; and whether a centralized bureau that aggregates and equalizes firms’ risk information can promote competition and improve welfare.

The empirical setting is the Italian mandatory motor vehicle liability insurance market (Responsabilità Civile Auto). The authors use the IPER dataset from IVASS, a nationally representative panel of matched insurer-insuree contracts covering 124,428 liability insurance contracts for new customers in the province of Rome from 2013 to 2021. The panel tracks consumers across insurer switches, enabling construction of individual-specific risk estimates from ex-post claim records using Poisson regressions for claim frequency and log-normal regressions for claim severity. The analysis focuses on the top 10 largest firms plus a composite fringe firm.

The paper’s empirical strategy proceeds in three stages. First, individual risk types are estimated from multi-year claim panels. Second, demand parameters — price sensitivity and firm-level unobserved product attributes — are recovered using a novel fixed-point algorithm (extending Berry et al. 1995) that infers the full offered-price distribution from observed transaction prices alone, without parametric restrictions on price distributions across firms. Third, supply-side parameters — pricing coefficients, signal variances, and cost parameters — are identified by exploiting the monotone mapping between offered prices and private signals, borrowing from the nonparametric auction literature.

The model features firms that each draw a private Gaussian signal about a consumer’s true risk type theta, with firm-specific signal standard deviation sigma_j. Lower sigma_j means higher information precision. Firms set prices as a linear function of their posterior risk rating: p_j = alpha_j + beta_j * E(theta | theta_j, D=j). Firms simultaneously choose pricing coefficients to maximize expected profits.

Key empirical findings: (1) Firms differ substantially in how sensitively their premiums respond to realized consumer risk — a reduced-form measure of information precision — with Figure 2 showing wide cross-firm variation in premium-to-risk coefficients. (2) Structural estimation confirms substantial heterogeneity in signal standard deviations sigma_j across all 11 firms. Firms with less accurate risk-rating algorithms (higher sigma_j) tend to have more efficient cost structures (lower claim-processing cost parameter k_j), generating distinct comparative advantages. (3) Baseline pricing coefficients alpha_j and risk-sensitivity coefficients beta_j vary dramatically across firms. (4) Senior drivers are less price sensitive; urban drivers are more price sensitive. Lower-risk consumers show stronger preferences for Firms 3 and 5, while higher-risk consumers disproportionately choose Firm 8.

Counterfactual simulations assess three information policies relative to the baseline. Under a centralized risk bureau — which collects each firm’s signal, aggregates them weighted by precision, and distributes the combined signal equally — average premiums fall by 21.6% and consumer surplus rises by 15.7%. The efficiency benchmark (firms observe true risk perfectly) yields a 25.7% premium reduction and a 16.9% consumer surplus gain, so the bureau recovers almost all the efficiency gap. The privacy benchmark (all firms restricted to the coarsest signal in the market) raises surplus for high-risk consumers by 6.9% but harms low-risk consumers.

The bureau’s price reduction operates through two channels: it eliminates the market power that accrues to firms with superior private information, and it aligns firms’ risk evaluations, enabling sharper undercutting. The bureau also reduces average costs by 12 euros per contract by enabling more efficient insurer-insuree matching — cost-efficient claim processors can better target the consumer types they have a comparative advantage in serving.

The analysis is confined to new customers in Rome’s provincial market to avoid complications from dynamic pricing and consumer-firm learning. The model abstracts away from optional contract clauses (treated as observable characteristics) and does not model the specific mechanisms generating information heterogeneity.

Q: What is the paper’s core research question? A: The paper asks how information asymmetries between competing firms (not just between buyers and sellers) shape equilibrium pricing strategies, consumer sorting, and market efficiency in a selection market, and whether a centralized bureau that equalizes firms’ access to aggregated risk information can improve competition and welfare. This extends the classic Akerlof-Rothschild-Stiglitz framework by introducing a second layer of asymmetry — across sellers themselves.

Q: Why is the Italian auto insurance market well suited for this study? A: Italy mandates liability insurance for all drivers and prohibits rejections, so the analysis focuses entirely on how consumers sort across insurers rather than on participation margins. The IPER dataset from IVASS is a nationally representative panel tracking policyholders even across insurer switches, providing both premium and ex-post claim records needed to construct individual risk types. The market has roughly 50 competing firms using demonstrably heterogeneous pricing algorithms, documented through a survey of major insurers and reduced-form regressions.

Q: How do the authors measure firm-level information precision in the reduced-form analysis? A: They estimate individual-specific risk types from a panel of claim records using Poisson regressions (claim frequency) and log-normal regressions (claim severity), then regress each firm’s premiums on those estimated risk measures. Firms whose premiums respond more sensitively to realized risk are inferred to have higher information precision. Figure 2 shows that these premium-to-risk coefficients vary significantly across firms — for example, Firm 7’s premiums are considerably more sensitive to risk than Firm 8’s — providing reduced-form evidence of heterogeneous information precision before any structural estimation.

Q: What is the structural model’s signal structure? A: Each firm j draws a private signal theta_j ~ N(theta, sigma_j^2) about a consumer’s true risk type theta, where sigma_j is the firm-specific signal standard deviation. A smaller sigma_j means higher precision. Signals are independent across firms conditional on theta, analogous to common-value auctions where firms receive noisy estimates of a shared unknown value (expected claim payouts). The parameter sigma_j is the key structural object the paper identifies and estimates.

Q: What is novel about the demand estimation strategy? A: Standard demand estimation assumes the same price is offered to all consumers or that the full price menu is observed. Here, only transaction prices are observed — the prices of unchosen insurers are not in the data. The authors apply the Wu and Xin (2024) fixed-point algorithm, which jointly estimates consumers’ sorting probabilities, offered price distributions, and demand parameters by adding an outer loop over sorting propensities to the Berry (1994) contraction mapping. No parametric restrictions are imposed on the offered price distributions, and they are allowed to vary fully across firms.

Q: How are firms’ signal variances identified separately from pricing coefficients? A: There is a one-to-one mapping between a firm’s offered price and its signal (prices increase monotonically in the signal, analogous to bids in auctions). After recovering the offered price distribution from the demand step, the authors observe price dispersion at a fixed risk level. By focusing on average prices conditional on each risk level, signal noise averages out, identifying the pricing coefficients beta_j. The residual price dispersion at fixed risk then identifies signal variance sigma_j^2.

Q: What does structural estimation reveal about the relationship between information precision and cost efficiency? A: Firms with higher signal standard deviations (less precise risk evaluation) tend to have lower claim-processing cost parameters k_j — they are more efficient at handling claims. This creates distinct comparative advantages: some firms excel at risk identification but face higher processing costs, while others process claims cheaply but evaluate risk less precisely. This heterogeneity means information-equalizing policies have differentiated firm-level impacts.

Q: What are the quantitative effects of the centralized risk bureau on premiums and consumer surplus? A: The bureau reduces average premiums by 21.6% relative to baseline and increases consumer surplus by 15.7%. The efficiency benchmark — where firms observe consumers’ true risk perfectly — produces a 25.7% premium reduction and a 16.9% consumer surplus gain. The bureau therefore closes nearly all of the gap to the first-best allocation in surplus terms (15.7% vs. 16.9%).

Q: Through what mechanisms does the bureau reduce prices? A: Two distinct channels are identified. First, equalizing information precision eliminates the informational market power held by firms with superior signals, compelling them to compete more aggressively on price. Second, when all firms share the same risk evaluation of a consumer, they can undercut each other more precisely, which intensifies price competition further. Both channels operate simultaneously under the bureau.

Q: How does the bureau affect consumer surplus distribution across risk types? A: The bureau primarily benefits low-risk consumers because improved information allows firms to price discriminate more accurately on risk type, lowering prices for those who are low risk. High-risk consumers see smaller benefits and may face relatively higher premiums. This contrasts with the privacy benchmark, where restricting all firms to the coarsest signal in the market raises high-risk consumers’ surplus by 6.9% — because it becomes harder for firms to distinguish them from low-risk consumers.

Q: What is the cost efficiency effect of the bureau? A: Under the centralized risk bureau, average costs per contract fall by 12 euros. This reflects more efficient insurer-insuree matching: when firms have equal and better information, those with cost advantages in claims processing can better identify and attract the consumer types they are relatively best equipped to serve. The authors note that given the scale of the Italian auto insurance market (approximately 31 million contracts annually), this per-contract saving implies a substantial aggregate impact.

Q: What happens to firm profits under the bureau, and is the impact uniform? A: Average profits decline overall due to lower prices. However, the impact is heterogeneous across firms. Firms that rely most heavily on superior information precision — often smaller, more specialized firms — experience greater profit losses, since the bureau most directly erodes their competitive advantage.

Q: How does the privacy benchmark differ from the bureau scenario? A: The privacy benchmark simulates a regulation that restricts all firms to using only basic consumer information, setting signal variance to the highest level observed in the market. Unlike the bureau (which improves and equalizes information), this benchmark degrades information uniformly. It produces opposite distributional effects: high-risk consumers gain 6.9% in surplus as cross-subsidization from low-risk to high-risk consumers increases, while low-risk consumers are worse off.

Q: Why does the paper focus on new customers only? A: Focusing on new customers avoids complications from dynamic pricing, where insurers update premiums based on accumulated claim history with a specific consumer, and from consumer-firm learning dynamics. This follows standard practice in the empirical asymmetric information literature, as cited in Chiappori and Salanie (2000) and Crawford et al. (2018).

Q: How does this paper relate to and extend prior work on selection markets? A: Prior empirical work on imperfect competition in selection markets — including Einav et al. (2010), Crawford et al. (2018), and related studies — assumes that competing firms have symmetric information about consumers. This paper is described as introducing the first tractable empirical framework for analyzing selection markets where firms have heterogeneous information. It also incorporates multidimensional cost heterogeneity on the supply side, adding to work by Salanié (2017) and Nelson (2025).

Q: What do the reduced-form regressions reveal about pricing heterogeneity across insurers? A: Firm-level regressions of premiums on observable risk factors show R-squared values ranging from 0.39 to 0.59. Estimated coefficients on key risk factors vary dramatically: being one year older reduces premiums by 0.25 to 1.68 euros depending on the firm; a higher bonus-malus class increases premiums by 12 to 32 euros; one additional accident in the previous five years raises premiums by 74 to 181 euros. These ranges reflect genuine differences in actuarial algorithms, not just sampling variation.

Q: What is the bonus-malus system and why does its saturation matter for the paper’s setting? A: Italy’s bonus-malus (BM) system assigns drivers to one of 18 risk classes based on accident history. Because approximately 80% of policyholders are in the best class (BM class 1), the public BM system provides limited granularity for risk evaluation. This saturation creates strong incentives for firms to develop proprietary risk-rating algorithms, which is the institutional basis for the substantial information heterogeneity that the paper documents and models.

Information Precision (sigma_j): In the paper’s model, the firm-specific parameter measuring the dispersion of a firm’s private signal about a consumer’s true risk type. Firm j draws signal theta_j ~ N(theta, sigma_j^2); 1/sigma_j is information precision. A smaller sigma_j means the firm more accurately identifies consumer risk. This is not merely a theoretical construct — the paper identifies and estimates sigma_j structurally for each of the 11 firms.

Heterogeneous Information: The condition where competing firms hold signals of different precision about the same consumer’s unobserved risk type, introducing asymmetry not just between buyers and sellers (as in Akerlof 1970) but among sellers themselves. This is the paper’s central departure from prior literature on selection markets, which assumed symmetric information among firms.

Centralized Risk Bureau: A policy institution that collects each firm’s analyzed risk signal, aggregates them weighted by each firm’s information precision (producing a combined signal more precise than any individual firm’s signal), and makes the aggregated information equally accessible to all firms. The bureau is the paper’s primary policy counterfactual, and it is modeled as equalizing both the level and heterogeneity of information precision across competitors.

Offered vs. Accepted Price Distribution: A distinction central to the paper’s identification strategy. The accepted price distribution is what is observed in transaction data — prices conditional on the consumer having chosen that firm. The offered price distribution is the full set of prices the firm would charge across all consumers, including those who did not select it. The paper recovers the offered distribution from the accepted distribution using a fixed-point algorithm, without imposing parametric restrictions.

Selection Loop: The paper’s methodological extension of the Berry (1994) BLP contraction mapping for mean utilities. An outer loop iterates over consumers’ sorting propensities to jointly recover offered price distributions, sorting probabilities, and demand parameters when only transaction prices are observed. This technique handles the endogeneity of which prices are accepted.

Risk Rating: The firm’s posterior assessment of a consumer’s expected cost, computed as the posterior mean E(theta | theta_j, D=j) — the expected true risk type conditional on the firm’s private signal and the consumer selecting that firm. Firms set prices as a linear function of their risk rating: p_j = alpha_j + beta_j * E(theta | theta_j, D=j).

Comparative Advantage (information vs. cost): The paper’s finding that firms with lower information precision (higher sigma_j) tend to have more efficient cost structures (lower k_j), and vice versa. This cross-sectional negative correlation between information advantage and cost advantage means that policy interventions that equalize information precision shift the basis of competition from information asymmetry to cost specialization.

Competition in a Spatially-Differentiated Product Market with Negotiated Prices

Mon, 01 Jan 0001 00:00:00 +0000

Research Question

How does individually negotiated pricing — where buyers make discrete choices among differentiated products and negotiate transaction-specific prices — affect market power and merger effects in oligopoly markets, and how do these effects differ from the uniform-pricing benchmark?

Data and Setting

The paper estimates the model using 13,788 transactions between the four main UK brick manufacturers and national house-building firms over 2003–2006. For each transaction (defined as a unique buyer-variety-destination-year combination), the data record the chosen product, negotiated price, production and delivery locations, volume, transport costs, and brick characteristics. The market is highly concentrated: four manufacturers held an 85% share of brick sales, with a two-firm concentration ratio of 0.60 and an HHI of 2,113. Spatial differentiation is a central feature — transport costs vary substantially by project location, and prices for the same brick product vary across the different projects of the same buyer depending on local competitive conditions.

Model

The paper develops an empirical model that adapts the Berry, Levinsohn, and Pakes (1995) differentiated-products framework to individually negotiated pricing. In the model, each buyer negotiates simultaneously and bilaterally with the sellers of the first-best and runner-up products (defined by surplus — value minus cost). The equilibrium first-best markup equals the minimum of (i) the unconstrained Nash bargaining solution, bj(wj(1) − w0), and (ii) the first-best seller’s surplus advantage over the runner-up, (wj(1) − wj(2)). Runner-up and lower-ranked sellers earn zero markups in equilibrium. This outcome is shown to be consistent with a range of non-cooperative bargaining models (Binmore 1985, Bolton and Whinston 1993, Manea 2018) and lies in the core of the associated coalition game. The TIOLI posted-price model is nested as the special case where seller bargaining skill equals one. A tractable likelihood for the joint probability of observed product choice and negotiated price is derived under the assumption that idiosyncratic taste terms follow a Generalized Extreme Value (GEV) distribution.

Main Findings

The estimated mean seller bargaining skill is b̄ = 0.41 (s.e. 0.03), and a likelihood ratio test rejects the TIOLI restriction with a chi-squared statistic of 847 (p < 0.001), confirming that buyer bargaining power is economically and statistically significant. The model-implied price-cost margins (Lerner index) are low on average — mean of 0.08 — but vary widely across transactions (coefficient of variation of 0.78). Project location matters: sellers extract higher margins from buyers that are relatively close, taking advantage of their transport-cost proximity. Multi-product ownership also affects markups, but its relevance varies by project.

Switching from negotiated to uniform pricing raises average markups by 34% at the observed market structure. However, effects are heterogeneous: approximately 15% of transactions see markup decreases. Buyers who benefit from uniform pricing are those with relatively little runner-up competition — precisely the buyers who face weak bargaining positions under negotiated pricing, and for whom the seller’s ability to use that position is constrained under a uniform rule.

Under negotiated pricing, a merger affects a transaction’s markup only if it brings the first-best and runner-up products for that transaction under joint ownership. A demerger to single-product manufacturers reduces total manufacturer surplus by 25%. The merger of the two largest firms increases total manufacturer surplus by 19%, but with highly unequal transaction-level effects. Comparing the same mergers across pricing regimes, negotiated pricing abates average markup-increasing merger effects but worsens them for a minority of transactions — those where the merger creates a first-best/runner-up pairing.

Scope Conditions

The model applies to complete-information settings where prices are negotiated transaction-by-transaction, buyers single-source for each discrete purchase occasion, and sellers have multiple spatially differentiated products. It is most directly applicable to business-to-business markets where individual transaction values are large enough to justify project-level negotiation.

Q: What is the fundamental difference between negotiated pricing in this paper and the standard Nash-in-Nash (NiN) bargaining framework? A: In standard NiN (Horn and Wolinsky 1988), a buyer negotiates one price per product and trades positive quantities of all products with negotiated prices, so all negotiated prices are observed in transaction data. In this paper, buyers make discrete single-sourcing choices — each project uses exactly one product — so only the chosen product’s price appears in data; the runner-up product and its counterfactual price are unobserved. Additionally, under NiN, prices are set at the buyer level and apply uniformly to all the buyer’s needs, whereas here prices are negotiated separately for each project, generating intra-buyer cross-project price variation.

Q: What is the equilibrium markup formula, and what determines whether the Nash bargaining solution or the TIOLI constraint binds? A: The equilibrium first-best markup is ρ*j(1) = min[bj(1)(wj(1) − w0), (wj(1) − wj(2))], the minimum of the unconstrained Nash bargaining solution and the first-best seller’s surplus advantage over the runner-up. The TIOLI constraint (surplus advantage) binds when the seller’s bargaining skill is sufficiently high that the unconstrained NBS would exceed the surplus advantage — that is, when bj(1)(wj(1) − w0) > (wj(1) − wj(2)). Runner-up and all lower-ranked sellers earn zero markups in equilibrium because competition from the first-best drives their outside-option constraint to bind.

Q: Why do third-best and lower-ranked sellers have no effect on equilibrium outcomes? A: Because the most attractive offer any seller below the runner-up could make is a zero markup, and the runner-up already offers a zero markup due to competition from the first-best. Since the runner-up at zero markup already offers the buyer at least as much utility as any third-best product, the third-best cannot improve the buyer’s position. Proposition 1 (part iii) shows that the equilibrium markup and choice are invariant to N for N in {2, …, N̄}.

Q: How does the paper address the econometric challenge that the runner-up product and its price are unobserved? A: The paper derives a tractable closed-form likelihood for the joint probability of the observed product choice and the observed negotiated price, integrating out the unobserved idiosyncratic taste terms along with their implications for the identity and surplus of the unobserved runner-up product. The GEV distributional assumption on taste terms is crucial: it ensures that (1) choice probabilities have a closed form, (2) the surplus advantage can be expressed in terms of observed surpluses and GEV terms, and (3) the probability that the NBS is constrained has a closed form. This reduces the full problem to a lower-dimensional numerical integral over the normally distributed random effects.

Q: What empirical evidence motivates the negotiated pricing model over simpler alternatives? A: Four data patterns motivate the model. First, prices vary across projects even after controlling for product identity and buyer identity — intra-buyer cross-project variation that is inconsistent with standard NiN where prices are set at the buyer level. Second, prices are lower, other things equal, when there is greater local competition from manufacturers not chosen for a project — inconsistent with standard NiN where excluded products play no competitive role. Third, buyers have many projects and make a discrete single-sourcing choice for each. Fourth, sellers are multi-product firms with products differentiated spatially and in other dimensions.

Q: What do the price regressions reveal about price determinants? A: Adding year effects to a simple regression explains only a small share of price variation (R² rises from 0.000 to 0.118 for the full sample). Adding variety-year effects raises R² to 0.775 and adding buyer-variety-year effects to 0.918, but still leaves substantial unexplained variation. Panel B regressions show that prices decrease with quantity, increase with input prices (gas price coefficient 27.2, wage coefficient 8.3), decrease with buyer-to-seller size ratio (coefficient −2.51), and decrease with greater local competition (a distance advantage indicator raises price by about 0.48–2.20 and N(DST) count reduces price by about 1.49–1.53 depending on specification).

Q: What do the parameter estimates imply about spatial differentiation and buyer preferences? A: Transport costs have a strongly negative effect on value (coefficient on distance is −1.27, s.e. 0.04), and the interaction of distance with fuel costs is also negative and significant. The nesting parameter σJ is estimated at 0.47, indicating substantial within-group taste correlation across products from the same firm. Product characteristics matter: red and wire-cut bricks are preferred, and there are significant interactions between weather conditions and technical brick characteristics (frost positively interacts with strength; rainfall negatively interacts with absorption), indicating that buyers value bricks whose technical performance is suited to their project’s climate.

Q: How is the mean seller bargaining skill estimated, and how is the TIOLI model rejected? A: The mean seller bargaining skill b̄ is estimated at 0.41 (s.e. 0.03), substantially below one. The TIOLI restriction corresponds to b̄ = 1 (all markup determined by surplus advantage). A likelihood ratio test rejects this restriction with a chi-squared statistic of 847 (p < 0.001), providing strong statistical evidence that buyer bargaining power — not just competitive pressure — constrains markups below the TIOLI level.

Q: What are the main findings regarding the distribution of price-cost margins? A: Price-cost margins (Lerner index form) are low on average, with a mean of 0.08, but vary widely across transactions, with a coefficient of variation of 0.78. Sellers set higher margins to buyers located relatively close to them (lower transport costs make the seller more attractive to the buyer, strengthening the seller’s position). Multi-product manufacturer portfolios also affect markups, but the relevance of multi-product ownership varies across projects depending on whether different products from the same firm compete as first-best and runner-up for a given project.

Q: What does the uniform pricing counterfactual show, and how does it differ from the Hotelling benchmark? A: Switching from individually negotiated to uniform pricing raises average markups by 34% at the observed market structure. However, effects are heterogeneous: approximately 15% of transactions see markup decreases. Buyers who benefit from the switch are those in transactions with relatively weak runner-up competition — who had weak bargaining positions under negotiated pricing — and who gain because uniform pricing prevents sellers from exploiting that weakness. This contrasts with the result from the simple Hotelling linear city model (Thisse and Vives 1988), where switching to uniform pricing raises all markups.

Q: How does the demerger counterfactual quantify multi-product effects? A: Decomposing the observed market to single-product manufacturers reduces total manufacturer surplus by 25%. This large reduction reflects the role of multi-product ownership in determining who the runner-up is for each transaction: when a manufacturer owns multiple products, it can avoid internal competition between its own first-best and runner-up products, preserving its surplus advantage. The impact is highly unequal across individual transactions, however, because the relevance of multi-product effects depends on whether any of a manufacturer’s other products would have been the runner-up for a given project.

Q: What does the merger of the two largest firms imply for markups and surplus? A: The merger of the two largest firms (by market share) increases total manufacturer surplus in the industry by 19%. Markup increases are very unequal across transactions: the merger affects only those transactions for which the merging firms jointly become the first-best and runner-up, which is the mechanism highlighted in the 2010 US Merger Guidelines for negotiated pricing markets. The heterogeneity of effects means that aggregate market-level concentration measures (such as HHI changes) can be poor proxies for merger effects in these markets.

Q: How does the pricing regime interact with merger effects? A: Comparing the same mergers under negotiated versus uniform pricing, negotiated pricing abates the average markup-increasing effects of mergers. However, for a minority of transactions — specifically those where the merger creates a first-best/runner-up pairing that did not exist pre-merger — negotiated pricing makes the merger’s markup effect worse than it would be under uniform pricing. This implies that the direction of the pricing-regime effect on merger harm is not uniform across buyers, and that transaction-level analysis is required for accurate antitrust assessment.

Q: How does the paper relate to the Competition Commission’s 2007 assessment of the Wienerberger/Baggeridge merger? A: The CC (2007) found the market highly concentrated (HHI 2,113, implied HHI increase of 390 from the merger, both exceeding guideline thresholds) but approved the merger, judging profitability to be at or below average for comparable industries and competition to be more intense than the concentration level alone would suggest. This paper’s model provides formal underpinning for that assessment: with negotiated pricing and buyer bargaining power, markups are constrained by the runner-up competitive threat at the transaction level, not by market-wide concentration, and the low mean Lerner index of 0.08 is consistent with the CC’s profitability finding.

Q: What external validity evidence supports the model’s cost specification? A: The paper compares the marginal costs implied by the estimated model to plant-month level production cost data that were not used in estimation. A good match between the two provides external validation of the cost specification and supports the model’s structural interpretation of the markup decomposition.

First-best and runner-up products: Defined at the project level in terms of surplus (value minus cost). The first-best product j(i,1) is the inside good yielding the highest surplus for project i; the runner-up j(i,2) is the highest-surplus inside good not sold by the first-best seller. These two products — and only these two — determine the equilibrium markup and buyer choice; third-best and lower-ranked products are irrelevant.

Surplus advantage: The difference wj(i,1) − wj(i,2) ≥ 0 between the first-best product’s surplus and the runner-up’s surplus for a given project. This is the competitive constraint on the first-best seller’s markup under TIOLI pricing and the binding ceiling on the negotiated markup whenever the unconstrained Nash bargaining solution would exceed it.

Negotiated pricing: A pricing arrangement in which buyers negotiate prices specific to the individual purchase occasion (here, each construction project), as opposed to uniform pricing where the pre-transport price is the same for all buyers. Prices are determined bilaterally between buyer and competing sellers, with the buyer’s outside option — buying the runner-up at its anticipated negotiated price — serving as the competitive constraint.

Outside option principle (Binmore et al. 1989): The principle that a rival offer (outside option) has no effect on a bilateral Nash bargaining problem unless it would leave the receiving party better off than the Nash bargaining solution — i.e., it constrains rather than shifts the disagreement point. In the paper’s model, the runner-up seller’s zero-markup offer serves as the first-best seller’s constraining outside option when seller bargaining skill is high.

GEV (Generalized Extreme Value) taste distribution: The distributional assumption on project-product idiosyncratic match terms that makes the joint likelihood of observed product choice and negotiated price tractable. The GEV structure yields closed-form choice probabilities (nested logit) and allows the surplus advantage — which depends on unobserved runner-up surplus — to be expressed analytically, enabling joint estimation from transaction-level data.

Price-cost margin (Lerner index): Markup (price minus cost) divided by price, used here at the transaction level. The estimated mean Lerner index is 0.08 with a coefficient of variation of 0.78, reflecting wide dispersion driven by spatial variation in local competition and first-best surplus advantage across transactions.

Nash-in-Nash (NiN) vs. single-sourcing bargaining: NiN (Horn and Wolinsky 1988) applies when a buyer trades positive quantities of all products with negotiated prices (multi-sourcing); the paper’s model applies when a buyer makes a discrete single-sourcing choice per occasion, so only the chosen product’s price is observed. The distinction generates different data observability and different competitive mechanisms — in NiN, excluded products play no role; in this paper, the runner-up’s potential zero-markup offer disciplines the first-best seller’s markup.

Competitive Advertising and Pricing

Mon, 01 Jan 0001 00:00:00 +0000

Hwang, Kim, and Boleslavsky study how firms in an oligopoly simultaneously choose prices and advertising strategies, where advertising is modeled as the choice of how much product information to disclose to consumers. The paper extends the canonical Perloff-Salop (1985) random-utility discrete-choice framework — in which n firms engage in Bertrand competition for a consumer whose value for each product is independently drawn from a common distribution F — by endogenizing the information environment: each firm may choose any mean-preserving contraction (MPC) of F as its advertising strategy, with no structural restriction on feasible content. This full flexibility, drawn from the information design literature, allows each firm to choose the consumer’s effective value distribution, ranging from full information (choosing F itself) to complete concealment (a degenerate distribution at the mean). The model is silent on advertising costs, which are assumed to be zero throughout.

The central result is that intense competition forces firms to provide precise product information. Formally, the full information equilibrium — in which every firm chooses F — exists in the advertising game (the subgame in which prices are fixed symmetrically) if and only if F^(n-1) is convex over its support. Because F^(n-1) represents the distribution of the consumer’s best outside option, convexity means the consumer likely faces an attractive alternative, incentivizing each firm to maximize the chance of offering the highest possible value. Crucially, this convexity condition is guaranteed to hold when n is sufficiently large, regardless of the shape of F, because the power function x^(n-1) becomes more convex as n rises. This establishes that under sufficiently intense competition, full information disclosure is the unique symmetric equilibrium.

The general equilibrium advertising strategy G* — which governs cases where full information is not an equilibrium — satisfies two necessary and sufficient conditions: (i) (G*)^(n-1) is convex over the support of G*, and (ii) for almost all values in the support, G* either coincides with F (where the MPC constraint binds, preventing further dispersion) or (G*)^(n-1) is locally linear (where the firm is locally risk-neutral and has no incentive to alter its distribution). The paper proves existence and uniqueness of G* for any F satisfying the stated regularity conditions (density positive, continuously differentiable, bounded, with finitely many peaks). When F has log-concave density, a unique symmetric pure-price equilibrium (p*, G*) exists in the full game.

The paper demonstrates that strategic advertising has ambiguous implications for prices and consumer welfare. Strategic advertising necessarily reduces social surplus through information loss, since consumers select suboptimal products with positive probability when G* differs from F. However, it compresses the support of the value distribution relative to F, which — by a new result (Proposition 3) — tends to lower the equilibrium price. Offsetting this, strategic advertising also redistributes marginal consumers in ways that may raise or lower the price. In the duopoly case with power distributions F(v) = v^alpha on [0,1], strategic advertising lowers the market price if and only if alpha > 1/sqrt(2) (approximately 0.7071), and raises consumer surplus if and only if alpha > 0.7928.

The paper examines three extensions: (1) a binding consumer outside option, (2) multi-unit (k-out-of-n) demand, and (3) asymmetric firms with two types. In all three cases, full information cannot be a strict equilibrium for any finite n under the relevant structural condition, yet the equilibrium distribution G* converges pointwise to F as n tends to infinity, preserving the paper’s core asymptotic insight.

Q: What is the main research question? A: The paper asks how much product information firms will voluntarily disclose when they compete both on price and advertising content in an oligopoly. Unlike the monopoly literature, the oligopoly context creates strategic interdependencies — each firm’s optimal disclosure depends on rivals’ disclosure choices — that the paper characterizes fully.

Q: How is advertising modeled, and why use mean-preserving contractions? A: Each firm’s advertising strategy is modeled as a choice of any mean-preserving contraction (MPC) of the true value distribution F. An MPC preserves the expected value but reduces dispersion, capturing the idea that a firm can selectively conceal information (moving toward a degenerate distribution) but cannot fabricate value dispersion beyond what F allows. Because consumers are risk-neutral and buy based on expected values net of prices, this MPC formulation captures full flexibility in information design without loss of generality.

Q: What is the precise necessary and sufficient condition for the full information equilibrium in the advertising game? A: The full information equilibrium — in which every firm chooses F — exists if and only if F^(n-1) is convex over its support [v, v̄]. The “only if” direction follows from Lemma 1: in any equilibrium, (G*)^(n-1) must be convex, so if F^(n-1) is not convex, F is not an equilibrium. The “if” direction follows because a convex F^(n-1) makes each firm locally risk-loving, so no MPC of F yields a higher payoff than F itself.

Q: Why does sufficiently intense competition force full information disclosure? A: For any distribution F with positive, continuously differentiable, bounded density f with bounded derivative f’, the second derivative of F^(n-1) satisfies F(v)^(n-1)’’ >= (n-1)F(v)^(n-3)[(n-2)epsilon^2 - M], where epsilon = min f(v)^2 > 0 and M = max |f’(v)| < infinity. This expression is strictly positive for n sufficiently large, so F^(n-1) is convex and the full information equilibrium exists. Economically, with many competitors each firm wins the consumer only when it offers the highest possible value, so providing full information is optimal.

Q: What are the two necessary and sufficient properties characterizing the general equilibrium advertising strategy G?* A: First (Lemma 1), (G*)^(n-1) must be convex over the support of G* — this prevents any firm from profitably concentrating mass to reduce dispersion. Second (Lemma 2), for almost all values in the support, either G* = F locally (the MPC constraint binds, preventing further dispersion) or (G*)^(n-1) is locally linear (the firm is locally risk-neutral and indifferent over distributions with the same local mean). Theorem 1 proves these two conditions are both necessary and sufficient, and that G* is unique for any F satisfying the stated regularity conditions.

Q: What structure does G take when F^(n-1) has strictly quasi-concave density?* A: By Corollary 2(1), there exists a cutoff v* in [v, v̄] such that G*(v) = F(v) for v <= v* (full information below the cutoff) and (G*)^(n-1) is linear above v*. As n increases, v* rises, meaning the region of full disclosure expands, and G* increases in convex order — so consumers receive strictly more information. One immediate implication is that consumer surplus strictly increases in n: consumers benefit both from more options and from more accurate information about each product.

Q: What happens when F^(n-1) is concave? A: By Corollary 3, when F^(n-1) is concave, (G*)^(n-1) is linear over the entire support, with lower bound v. In the illustrative Example 1 (truncated exponential with n=2), this yields G* = U[0, 2*mu_F] — a uniform distribution on an interval whose upper bound is twice the mean of F.

Q: Does strategic advertising raise or lower equilibrium prices, and consumer surplus? A: Both effects are ambiguous and depend on the shape of F. Strategic advertising compresses the support of the value distribution (since G* is an MPC of F), which by Proposition 3(1) tends to lower equilibrium prices. But it also reshapes the distribution of marginal consumers, which may raise or lower prices. In the power distribution example (n=2, F(v) = v^alpha on [0,1]), strategic advertising lowers the market price if and only if alpha > 1/sqrt(2) ≈ 0.7071, and raises consumer surplus if and only if alpha > 0.7928. Thus even with deadweight loss from information suppression, consumers can be better off under strategic advertising than under forced full disclosure.

Q: What does Proposition 3 contribute about equilibrium prices in the Perloff-Salop model? A: Proposition 3 delivers two results about how the distribution of marginal consumers (integral (F^(n-1))’ dF) determines equilibrium prices. First, the measure of marginal consumers decreases if F is proportionally stretched over a larger support, confirming that longer support raises equilibrium prices. Second — presented as novel — among all distributions with support in [v, v̄], the power distribution F(v) = ((v-v)/(v̄-v))^(2/n) minimizes the measure of marginal consumers, corresponding to the maximum equilibrium price. The key property is that marginal consumers are uniformly distributed under this power distribution, and any deviation from uniformity allows a “flattening” adjustment that increases the measure of marginal consumers and lowers the price.

Q: Under what condition does the full game (price plus advertising) have a unique symmetric pure-price equilibrium? A: Theorem 2 states that log-concavity of the density f is sufficient for existence and uniqueness of a symmetric pure-price equilibrium (p*, G*) as characterized in Theorems 1 and 2. Log-concavity ensures that the equilibrium distribution G* has a convex-linear structure (as in Corollary 2), which preserves log-concavity of each firm’s profit function even under compound deviations (simultaneous changes to both price and advertising strategy), making the first-order conditions sufficient for global optimality.

Q: Can strategic advertising create or destroy pure-price equilibria relative to the Perloff-Salop benchmark? A: Yes, both directions are possible. When F^(n-1) is convex (so G* = F), equilibrium existence in the Perloff-Salop (PS) model is necessary but not sufficient for existence in the full model, because compound deviations (changing both price and advertising) may be profitable even when pure price deviations are not. Conversely, when G* differs from F, the changed distribution of marginal consumers can sustain an equilibrium in the full model even when none exists in PS. Appendix E of the paper provides a specific example of the latter phenomenon.

Q: What happens with a binding consumer outside option? A: Proposition 4 shows that a full information equilibrium never exists in the advertising game when the consumer has a binding outside option (p* in (v, v̄)). The firm’s value function acquires a discrete jump at p* due to the indicator 1_{v >= p*}, making it optimal to pool mass around p* rather than disclose fully. Nevertheless, Proposition 5 proves that G* converges pointwise to F as n tends to infinity, because the jump of size F(p*)^(n-1) vanishes exponentially fast as n grows.

Q: Does the full information result survive multi-unit demand? A: No. Proposition 6 shows that with k > 1 units demanded (out of n products), the full information equilibrium never exists for any finite n or F. The reason is that phi’(v; F) — the firm’s marginal value of offering value v — is zero at v̄ when k > 1, so the firm can profitably pool values near the top of the support. However, Proposition 7 shows that G* converges pointwise to F as n tends to infinity (with k fixed), preserving the asymptotic full information result.

Q: What happens with asymmetric firms differing in their value distribution supports? A: Proposition 8 shows a sharp dichotomy. If both firm types share the same upper bound of their value supports (v̄_1 = v̄_2), the full information equilibrium exists whenever both F_1^(n1-1) and F_2^(n2-1) are convex. If the supports have different upper bounds (v̄_1 < v̄_2), the full information equilibrium never exists regardless of n_1 and n_2, because type-2 firms face a downward kink in their winning probability at v̄_1 and always have an incentive to pool mass there. The authors conjecture that G*_1 and G*_2 still converge to F_1 and F_2 asymptotically but do not prove this due to technical complexity.

Q: How does this paper relate to Ivanov (2013)? A: Ivanov (2013) also uses the Perloff-Salop framework and shows that full information is an equilibrium when n is sufficiently large, but restricts advertising to rotation-ordered strategies (in the sense of Johnson and Myatt, 2006). The present paper imposes no structural restriction and strengthens Ivanov’s result by: (a) providing a necessary and sufficient condition for the full information equilibrium (not just a sufficient condition for large n); (b) fully characterizing G* when full information is not an equilibrium; and (c) demonstrating robustness across multiple model variants.

Q: What policy implication does the ambiguity result carry? A: The paper warns against assuming that mandating full information disclosure is unambiguously consumer-beneficial. While strategic advertising creates deadweight loss through information suppression, it can simultaneously compress support and alter the marginal consumer distribution in ways that lower equilibrium prices significantly. The power distribution example (alpha > 0.7928) shows consumers can be strictly better off under strategic advertising than under forced full disclosure. This ambiguity is a cautionary tale for disclosure regulation.

Mean-Preserving Contraction (MPC): A distribution G_i is an MPC of F if it has the same mean as F but less dispersion (in the sense of second-order stochastic dominance). In the paper, each firm’s feasible advertising strategies are exactly the set MPC(F) — this captures all informationally feasible disclosures without structural restriction on content.

Advertising Game: A restricted subgame of the full market game in which firms choose their advertising strategies G_i taking the symmetric price as given. An equilibrium in the advertising game is a necessary condition for equilibrium in the full game. The advertising game’s equilibrium uniquely pins down G* independently of the price level (under the baseline model without binding outside option).

Full Information Equilibrium: An equilibrium of the advertising game in which every firm chooses the true underlying distribution F as its advertising strategy. This corresponds to complete, unobstructed product disclosure. The paper’s central result is that this equilibrium exists if and only if F^(n-1) is convex over its support.

Convexity of F^(n-1): The key distributional condition governing advertising equilibria. F^(n-1) is the distribution of the consumer’s best alternative among (n-1) rivals’ products. Convexity of F^(n-1) means its density is increasing, signaling a likely attractive outside option, which makes each firm risk-loving and induces full disclosure. This convexity is guaranteed for n sufficiently large.

Locally Linear (G)^(n-1):* A region of the equilibrium distribution where (G*)^(n-1) has constant slope, making the firm locally risk-neutral. Over such a region, the firm is indifferent among all distributions with the same local mean, and the equilibrium G* need not coincide with F — it is only required to be an MPC of F on that interval. This alternating structure (coinciding with F on strictly convex regions; linear elsewhere) fully characterizes G*.

Marginal Consumers: In the Perloff-Salop pricing formula, the equilibrium price p* = (1/n) / integral [(G*(v)^(n-1))’ dG*(v)]. The integrand (G*(v)^(n-1))’ * g*(v) is the density of consumers who are indifferent between a given firm’s product and their best alternative at value v. A larger measure of marginal consumers implies lower equilibrium prices through greater competitive pressure.

Compound Deviation: In the full game, a deviation by a firm that changes both its price p_i and its advertising strategy G_i simultaneously, rather than varying only one dimension. The possibility of compound deviations is what distinguishes equilibrium existence conditions in the full model from those in the standard Perloff-Salop model, even when G* = F.

Contract Terms, Employment Shocks, and Default in Credit Cards

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

This paper asks two related questions bearing on financial inclusion policy in developing countries: (1) How effective are credit card contract term changes — specifically interest rate reductions and minimum payment increases — in limiting default among new borrowers? (2) How large is the effect of formal-sector job loss on default relative to these contract term interventions, and can the difference in magnitudes be explained by differential cash flow impacts?

Setting and Data

The study is set in Mexico during 2007–2009 and exploits a large nationwide stratified randomized controlled trial implemented by a major commercial bank (“Bank A”) on its financial-inclusion credit card — a product that accounted for approximately 15% of all first-time formal-sector loans in Mexico as of 2010. The study card was targeted at borrowers with limited or no formal credit history (the bank’s “C, C- and D” customer segments); 47% of the experimental sample held it as their first formal loan product. A sample of 144,000 pre-existing cardholders was stratified into nine cells based on bank tenure (6–11 months, 12–23 months, 24+ months) and past repayment behavior, then randomly allocated to eight treatment arms combining two minimum payment levels (5% or 10% of the outstanding balance) and four annual interest rates (15%, 25%, 35%, 45%), for 26 months (March 2007 to May 2009). The study sample is representative of the bank’s national portfolio of approximately 1.3 million study card customers. Card-level data run through December 2014 — five years after the experiment ended — allowing examination of both short- and long-run effects. The experimental sample is matched to Mexico’s Social Security database (IMSS), providing monthly formal employment histories from January 2004 to December 2012 for 59% of the sample; and to credit bureau data, allowing observation of defaults across all formal financial institutions.

Main Findings with Quantitative Magnitudes

Result 1 — Interest rate effects are modest in aggregate. A 30 percentage point (pp) decrease in the annual interest rate (from 45% to 15%, a 67% reduction relative to the baseline rate) decreased cumulative default by 2.5 pp over the 26-month experiment, for a default elasticity of +0.20. Over the same 18-month horizon used for unemployment comparisons, the implied effect is 1.03 pp. These magnitudes are substantially smaller than predictions elicited from Mexican central bank regulators (mean predicted decrease: 8.6 pp) and from participants on the Social Science Prediction Platform (mean predicted decrease: 5 pp). Default continued to decline in the lower-rate arm for approximately three years after the experiment ended, reaching −1 pp by March 2012, after which effects became statistically indistinguishable from zero.

Result 2 — No effect on the newest borrowers. For the newest borrowers (those with 6–11 months of tenure when the experiment began — the group with a 36% cumulative default rate over 26 months versus 18% for those with 24+ months of tenure), the interest rate reduction has no effect on default over the 26-month period, with point estimates consistently small and statistically indistinguishable from zero. This is in contrast to older borrowers, who are meaningfully responsive.

Result 3 — Minimum payment increases increase short-run default but reduce long-run default. Doubling the minimum payment from 5% to 10% of outstanding balance increased cumulative default by 0.8 pp by the end of the experiment (26-month elasticity: +0.04; p = 0.016), driven primarily by defaults occurring within the first year. The short-run increase is concentrated among the most liquidity-constrained borrowers — those with the highest baseline debt utilization and those in the minimum-payer stratum (baseline debt utilization rate of 85%). After the experiment ended and all arms were returned to the same 4% minimum payment, the previously higher-minimum-payment arm exhibited persistently lower default, reaching a 1 pp decline by the end of the sample (p = 0.054 at end of study period), relative to a base default rate of 41% at that point.

Result 4 — Job displacement effects are seven times larger than contract term effects. Formal-sector job displacement (identified using mass layoff events at firms with 50+ employees, defined as year-on-year employment contractions exceeding 30% of prior-year average employment) increased cumulative default by 4.8 pp after 12 months and 7.6 pp after 18 months. This is seven times larger than the effect of a 30 pp interest rate decrease (1.03 pp over 18 months) and nine times larger than the effect of doubling minimum payments (0.8 pp). Formal job loss alone can explain approximately 14% of total study card default during the experiment (calculation: 19.8% of formally employed study card borrowers lose their job at least once in the first 18 months; multiplied by the 7.6 pp default increase per spell, this yields 1.5 pp of the 10.8% base default rate at 18 months). Results are corroborated using a nationally representative matched credit bureau–IMSS sample of 600,339 borrowers, which yields 8,723 mass layoff events and similar estimates.

Per-peso normalization. A back-of-the-envelope calculation normalizes all three shocks by their respective cash flow impacts. The interest rate decrease reduces cumulative required minimum payments due by 2,917 MXN pesos over 18 months; the minimum payment doubling increases them by 1,325 MXN pesos; formal job loss reduces total labor earnings by an estimated 21,328 MXN pesos (adjusting formal-sector earnings losses of 77,555 MXN pesos downward by 72.5% to reflect that 82% of workers who lose formal employment transition to informal employment in the following quarter, with total earnings falling only 27.5%). The per-peso default effects are: 0.36 pp per 1,000 MXN pesos for the interest rate intervention; 0.51 pp for the minimum payment intervention; and 0.36 pp for job displacement. The null hypothesis that all three per-peso effects are equal cannot be rejected (p = 0.78).

Interpretation

The authors present a simple two-period optimizing model emphasizing the role of previously accumulated debt and liquidity constraints. The model generates four testable predictions consistent with the data: (1) lower interest rates decrease default via reduced debt burden; (2) higher minimum payments increase short-run default by tightening liquidity constraints; (3) “surprise” minimum payment increases (where borrowers anticipated they would continue) reduce post-experiment default via debt reduction; (4) negative income shocks (modeled as first-order stochastic dominance deterioration in period-2 income) increase default. The per-peso normalization supports the interpretation that cash flow impacts — not differential per-peso susceptibility to shocks — drive the relative magnitudes of the three effects.

In depth

Q1. Why is the interest rate elasticity of default (0.20) so much lower than prior estimates in the literature?

A: The paper contrasts its 26-month elasticity of +0.20 with estimates from Karlan and Zinman (2019) (1.8) and Adams et al. (2009) (2.2), and notes it falls in the same range as Karlan and Zinman (2009) (0.27) and DeFusco et al. (2021) (0.01). The paper proposes that variation in borrower tenure may partly explain cross-study differences, as default elasticities appear to be increasing in bank tenure. The newest borrowers — the most policy-relevant subgroup — show zero elasticity, pulling the overall estimate down. The paper also argues that in this context, interest-rate-driven moral hazard (all channels: debt burden, concurrent, and dynamic) is collectively small.

Q2. What mechanism explains why newer borrowers are entirely unresponsive to interest rate changes?

A: The paper hypothesizes that newer borrowers place a higher continuation value on the card (captured by parameter v in the model) because they have fewer formal credit alternatives; at baseline, only 64% of the 6–11 month stratum held a card with another bank versus 78% of the 24+ month stratum. A higher continuation value implies more muted responses to interest rate changes (formally derived in Appendix E.3). Newer borrowers also respond more strongly to credit limit increases, consistent with tighter liquidity constraints. A regression controlling for age, gender, baseline card ownership, debt utilization, labor force attachment, and earnings cannot explain away the differential treatment effect between new and old borrowers (differential remains significant at p = 0.05), suggesting the tenure gradient in responsiveness is not simply a composition effect.

Q3. Why does increasing minimum payments raise short-run default but reduce long-run default?

A: In the short run, the doubling of minimum payments tightens liquidity constraints for already-constrained borrowers. The increase in default is concentrated among borrowers in the highest baseline debt-utilization tercile and among minimum-payers (baseline debt utilization of 85%), and is preceded by a sharp rise in delinquencies in months 3–5 (which trigger 350 MXN peso fees per occurrence, further worsening the repayment burden). In the long run, borrowers who anticipated continuing higher minimum payments (the experiment ended without advance notice, so borrowers expected the new terms to persist) chose lower debt levels during the experiment. Since all arms were returned to the same low minimum payment when the experiment ended, the lower-debt borrowers in the higher-minimum-payment arm were better positioned to weather subsequent shocks, producing the 1 pp post-experiment decline in default. The hypothesis that this is driven by habit formation in payment behavior is ruled out by the absence of any effect of past higher minimum payments on post-experimental payment levels.

Q4. How is the mass-layoff identification strategy designed and validated?

A: The paper uses the universe of IMSS formal employment records to define a mass layoff at a firm (50+ employees) as the first month in which year-on-year employment declines by more than 30% of average employment in the prior 12 months. An individual is “displaced” if they lost their job in the same quarter as their employer’s mass layoff event. The identification assumption is that, conditional on individual and time fixed effects, the exact timing of the mass layoff is uncorrelated with workers’ potential default outcomes. This is supported by: (1) mass layoffs occurring in every period, making coincidence with credit market shocks unlikely; (2) time fixed effects absorbing common trends; and (3) the absence of statistically distinguishable pre-trends in default between displaced and non-displaced workers. The paper implements both standard two-way fixed effects and the staggered DiD estimator of de Chaisemartin and D’Haultfoeuille (2024), which remains valid under heterogeneous and dynamic effects, and the results are similar across methods.

Q5. How does the paper account for informal employment when estimating the cash flow impact of job loss?

A: Formal-sector earnings losses over 18 months post-displacement are estimated at 77,555 MXN pesos using IMSS wage data in an event-study design paralleling the default equation. However, since more than 4/5 of workers who lose formal employment are informally employed in the following quarter (based on Mexico’s ENOE labor force survey panel), and total labor earnings fall by only an estimated 27.5% over the three post-displacement quarters, the paper scales the formal earnings loss down to 21,328 MXN pesos (≈ 0.275 × 77,555). This brings the estimated earnings loss closer to prior developed-country estimates of displacement costs and is treated as a lower bound relative to the raw formal-earnings loss figure.

Q6. Does the cost of default deter borrowers from defaulting, and what is the cost?

A: The paper argues that defaulters face substantial consequences. Using an instrumental variables strategy (treatment assignment as instrument for default on the study card), the probability of having a new loan one year after default is estimated to be 65 pp lower relative to the non-default counterfactual (p = 0.03). A selection-on-observables approach also shows that study card default is associated with the complete absence of any subsequent credit card for at least four years. These costs should provide strong incentives to remain current, making the high observed default rates primarily attributable to cash flow shocks rather than strategic default. The value of formal credit is further confirmed by the finding that a 100 MXN peso increase in the study card’s credit limit translates into 32 MXN pesos of additional debt (instrumental variable estimates are more than twice as large as OLS), and by the comparison of informal loan terms (annual rates averaging 291%, loan amounts of 3,658 MXN pesos, durations of 0.52 years) with formal loan terms (94 pp lower rates, 9,842 MXN peso average amounts, 1.07 year durations).

Q7. Are the default treatment effects different across the interest rate and minimum payment interventions, or do they interact?

A: The paper tests for and cannot reject separability between the two interventions at standard significance levels. At the end of the experiment (May 2009), the p-value for the null that the minimum payment effect is constant across interest rate arms is 0.44; five years later it is 0.65. The null that the interest rate effect is constant across both minimum payment arms yields p = 0.08 at end of experiment and p = 0.411 five years later. The fully saturated specification yields results indistinguishable from the parsimonious linear-separable specification.

Q8. Are there spillover effects from the contract term changes onto other loans held by study participants?

A: No spillover effects on default on other loans are found, either during the experiment or after it ended, based on credit bureau data covering all formal-sector loans held by the experimental sample. There is also no evidence of crowd-out or crowd-in from other lenders in terms of new loans or loan closures. The only minor exception is a small decrease in default (3%, or approximately 2 pp out of a 61 pp base) on other Bank A loans in the high minimum payment arm.

Q9. Why does the effect of unemployment on default exceed the model’s predictions from cash flow alone?

A: The paper’s back-of-the-envelope normalization finds that the per-peso effects of all three shocks on default are statistically indistinguishable (p = 0.78 for the null that all three λ estimates are equal), with point estimates of λ_IR = 0.36, λ_MP = 0.51, and λ_U = 0.36 pp per 1,000 MXN pesos. This implies that job loss does not have a larger per-peso effect on default than contract term changes; the larger absolute effect of displacement arises entirely from its larger cash flow impact. Additional consequences of job loss beyond cash flow (health, mental health) do not appear to generate additional default beyond what can be attributed to income loss.

Q10. How do the experimental results compare to what experts predicted?

A: Expert predictions were systematically too large. Mexican central bank regulators predicted a mean decrease of 8.6 pp from a 30 pp interest rate reduction at the 18-month horizon, versus the actual estimated effect of 1.03 pp. Social Science Prediction Platform respondents predicted a mean decrease of 5 pp. For minimum payments, regulators on average predicted a 0.4 pp decrease in default from doubling the minimum payment, whereas the actual effect was a 0.8 pp increase. Three-quarters of SSPP respondents correctly predicted the sign of the minimum payment effect (an increase in default), but the predicted mean increase was 6.4 pp, far larger than the estimated 0.8 pp.

Q11. Do the job displacement results generalize beyond the experimental sample?

A: Yes. The paper repeats the displacement event study on the intersection of the nationally representative credit bureau sample (approximately 600,339 individuals with both credit information and employment histories) with the universe of IMSS data for October 2011–March 2014, yielding 8,723 mass layoff events. This sample is representative of the population of Mexican borrowers with formal employment histories, and the estimated effects on default for any loan in the credit bureau are similar in magnitude to the experimental-sample results, providing a measure of external validity.

Q12. What do the debt dynamics during the experiment reveal about the mechanisms for interest rate effects on default?

A: The data show that purchases (net of payments) increase in response to interest rate decreases, consistent with downward-sloping demand for credit; yet total debt declines in lower-rate arms. This is consistent with the model’s prediction that the mechanical compounding effect (lower rate applied to previously accumulated debt) exceeds the behavioral new-purchase response. Confirmed empirically: the debt elasticity to the interest rate is estimated to be positive, with preferred estimates in the range [+0.18, +0.54]. The decline in default is further concentrated among borrowers with the highest baseline debt utilization rates, those for whom the debt compounding effect is strongest — consistent with the debt channel as the primary mechanism.

Key Concepts

Cumulative Default Measure: Default is defined as three consecutive monthly payments each below the required minimum payment due, at which point Bank A automatically revokes the card. The outcome variable is coded as Yit = 1 if borrower i has defaulted in any month s ≤ t and 0 otherwise, making it a cumulative (absorbing) measure. This allows estimation on an unchanging sample, avoiding attrition biases that would arise from conditioning on not having defaulted in the prior period.

Minimum Payment Due (mpd): The paper uses the required minimum payment due to avoid delinquency as its central cash-flow normalization variable. This is a comprehensive measure that incorporates not only the contractually specified fraction of outstanding balance but also interest charges, fees, and endogenous borrower responses (changes in debt and purchases). It serves as the common denominator for benchmarking the cash flow impacts of the two contract term interventions and formal job loss against one another.

Free Cash Flow / Per-Peso Normalization (λ): The paper defines per-peso default effects (λ^IR, λ^MP, λ^U) by dividing each intervention’s average treatment effect on cumulative default (in percentage points) by the cumulative change in the minimum payment due (or equivalent cash flow impact) induced by that intervention over 18 months. The resulting ratio is expressed as percentage points of default per 1,000 MXN pesos of cash flow change. This normalization is explicitly not treated as an instrumental variable estimate; it is a descriptive back-of-the-envelope calculation intended to equate the scale of the three shocks.

Mass Layoff / Displacement: A mass layoff at the firm level is defined as the first month in which year-on-year firm employment declines by more than 30% of average employment in the prior 12 months, restricted to firms with 50+ employees. An individual worker is classified as displaced if they lost formal-sector employment in the same calendar quarter as their employer’s mass layoff event. This definition follows Jacobson et al. (1993) and subsequent literature and is used to isolate plausibly involuntary (exogenous) separations from voluntary quits or individually driven terminations.

Continuation Value (v): In the paper’s two-period optimizing model, v is the reduced-form utility parameter capturing future flow of card benefits, warm glow from card ownership, or the option value of retaining access to formal credit, experienced only if the card is not in default. The paper uses v to rationalize the zero interest-rate response of newer borrowers: ceteris paribus, higher v implies that borrowers will remain current on the card even when interest rates are high, because they value continued access. Higher v thus implies more muted responses to interest rate changes.

Bank Tenure Strata: Borrowers are stratified into three groups based on length of relationship with the study card: “new customers” (6–11 months), medium-term (12–23 months), and long-term (24+ months). Tenure is used both as a stratification variable for the experiment and as a primary dimension of heterogeneity in treatment effects, reflecting differing default rates (36% vs. 18% at 26 months), labor market vulnerability (1.34× higher job loss probability for new vs. long-term), and interest rate responsiveness (zero for new, significantly positive for long-term borrowers).

Debt Burden Channel vs. Concurrent Moral Hazard: The paper distinguishes three channels through which interest rate changes can affect default: (a) the debt burden channel — higher rates mechanically increase the stock of interest-accruing debt, making repayment harder; (b) concurrent moral hazard — higher current interest rates alter the incentive to default on existing obligations, holding debt constant; and (c) dynamic moral hazard — higher future interest rates reduce the benefit of remaining current. The paper’s finding of a modest total effect (elasticity 0.20) implies that the sum of all three channels is small in this context, with the debt burden channel being the primary driver of what effect does exist.

Costly Multidimensional Screening

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies when a principal can improve upon simple one-dimensional mechanisms by also deploying costly nonprice screening instruments — actions that are socially wasteful yet potentially informative about the agent’s private type.

The model features a principal and an agent with quasilinear, additively separable preferences across two components: (i) a productive component, where allocations lie in a one-dimensional compact space X and generate genuine surplus, and (ii) a costly component, where any allocation y in an arbitrary measurable space Y satisfies sB(y, θB) ≤ 0 — it destroys or at best does not create social surplus. The agent’s private type is multidimensional, θ = (θA, θB), drawn from a commonly known distribution. Both components allow for nonlinear valuations and, on the principal’s side, interdependent preferences.

The central result (Theorem 1) establishes that if the agent’s preferences between the productive and costly components are positively correlated — meaning that a higher θA implies a stochastically higher θB — then there exists an optimal mechanism that involves no costly screening. Moreover, if instruments are strictly costly, every optimal mechanism involves no costly screening almost everywhere. Positive correlation is defined in terms of stochastic dominance: θB | θA is stochastically nondecreasing in θA. A sufficient but not necessary condition is affiliation in the sense of Milgrom and Weber (1982).

The intuition centers on two observations. First, under positive correlation, costly instruments can only help relax upward incentive constraints (deterring lower types from mimicking higher types). Second, under the surplus condition — a single-crossing condition on the surplus function sA(x, θA) requiring that if x generates more surplus than x’ at some type, it continues to do so at all higher types — the principal can safely ignore upward incentive constraints at the optimum. The Downward Sufficiency Theorem (Theorem 2) formalizes the second observation: in any one-dimensional screening problem satisfying the surplus condition, there exists an optimal solution to the relaxed program (with only downward IC constraints) that also satisfies all upward IC constraints. Because monetary transfers fully substitute for costly instruments in relaxing downward constraints without destroying surplus, the costly instruments add no value under positive correlation.

The proof proceeds via a monotone path decomposition of the multidimensional type space, exploiting a measurable monotone coupling (Lemma 1) to write θ = (θA, h(θA; ε)) where ε is independent of θA and h is nondecreasing. This reduces the problem to a family of one-dimensional paths, on each of which the Reconstruction Lemma (Lemma 2) shows that any costly mechanism can be weakly improved upon by one with no costly screening that satisfies all downward IC constraints.

A partial converse (Proposition 1) shows that under negative correlation — when some dimension of θB is stochastically nonincreasing in θA — there exist utility functions satisfying the surplus condition for which any mechanism screening only the productive component is strictly dominated.

The paper derives three applications. In monopoly pricing with costly signals (waiting in line, climbing stairs, collecting coupons), profit-maximizing mechanisms require no costly signals when higher-willingness-to-pay consumers also face weakly lower signal costs (Proposition 2). In monopsonistic labor market screening, the firm need not make offers contingent on costly credentials when higher-ability workers find credentialing easier — in contrast to the competitive Spence (1973) model where all screening must occur through costly effort because wages are pinned down by expected output (Proposition 3). In multiproduct pricing, the paper reinterprets bundle components as costly instruments for screening grand-bundle values, recovering Haghpanah and Hartline’s (2021) pure bundling optimality result and extending it to nested bundling (Proposition 4), under conditions that the incremental value of adding items to nested bundles is strictly increasing in type while the value of any non-nested bundle is nonincreasing relative to some nested superset.

Q: What is the paper’s central research question? A: The paper asks whether a principal can improve upon simple one-dimensional mechanisms by also deploying costly nonprice screening instruments when the agent has multidimensional private information. The goal is to characterize conditions under which augmenting a standard price menu with surplus-destroying actions — such as waiting in line, climbing stairs, or obtaining credentials — is or is not beneficial for the principal.

Q: What does “positively correlated preferences” mean precisely in this model? A: Positive correlation means that θB is stochastically nondecreasing in θA: for any θA < θ̂A, the conditional distribution of θB given θA first-order stochastically dominates that given θ̂A — i.e., θB | θA ≤_st θB | θ̂A. Observing a high θA conveys good news about θB in the stochastic dominance sense. A sufficient but not necessary condition is affiliation in the sense of Milgrom and Weber (1982). The condition is asymmetric and does not require full independence or monotone dependence in a deterministic sense.

Q: What is the surplus condition and why does it matter? A: The surplus condition is a single-crossing condition on the productive surplus function: for any x < x̂ and θA < θ̂A, if sA(x̂, θA) > sA(x, θA) then sA(x̂, θ̂A) > sA(x, θ̂A). It says that if a higher allocation generates more total surplus at some type, it continues to do so at all higher types. This condition ensures the existence of a monotone efficient allocation rule, and it is the key enabling condition for the Downward Sufficiency Theorem. It is automatically satisfied when the principal has no interdependent preferences and the agent satisfies increasing differences, and also when sA is strictly increasing in x or has nonnegative cross partial derivative.

Q: What is the Downward Sufficiency Theorem and why is it the key technical result? A: Theorem 2 states that in any one-dimensional screening problem satisfying the surplus condition, there exists an optimal solution to the relaxed program — which ignores all upward IC constraints — that also satisfies all upward IC constraints. This means the principal can solve the easier downward-IC-only problem and the solution is fully incentive compatible. The result is novel and uncovers a general property of one-dimensional screening problems beyond the standard monotone allocation rule setting. It is key because, combined with the observation that costly instruments under positive correlation can only relax upward constraints, it implies there is no benefit to using costly screening.

Q: How does the proof handle the case of multidimensional types? A: The proof uses a monotone path decomposition. By Lemma 1 (measurable monotone coupling), under positive correlation there exists a random variable ε independent of θA and a nondecreasing measurable function h such that θ =^d (θA, h(θA; ε)). This writes the joint type distribution as a family of monotone paths indexed by ε. On each path ε = e, the types are ordered by θA alone, reducing the problem to a one-dimensional screening problem. The Reconstruction Lemma (Lemma 2) then shows that on each such path, any mechanism involving costly screening can be replaced by one without costly screening that weakly improves principal payoff and satisfies all downward IC constraints.

Q: What does the partial converse (Proposition 1) establish? A: Proposition 1 shows that when some dimension i of the costly component satisfies that θi is stochastically nonincreasing in θA (negative correlation), and the type distribution has a density with |X| > 1 and |Y| > 1, then there exist utility functions satisfying the surplus condition for which any mechanism screening only the productive component is strictly dominated by one involving costly screening. This is not a full converse — it establishes existence of cases where costly screening is strictly beneficial, not that it is always beneficial under negative correlation.

Q: How does the insurance example illustrate the two correlation cases? A: In Example 1 (negative correlation), a low-risk type (θA = 0) values insurance at 2, a high-risk type (θA = 1) values it at 3; costs are 0 and 5/2 respectively; and the high-risk type also has higher disutility for the costly action. Without costly screening, the optimal mechanism sells full insurance at price 2 to both types for a profit of 3/4. With costly screening (e.g., requiring the agent to climb stairs to get full insurance), only the low-risk type purchases, yielding profit of 1 > 3/4. In Example 2 (positive correlation), the high-risk type has lower disutility for the costly action; any mechanism using the costly instrument is strictly dominated by simply selling full insurance at price 2 to both types.

Q: How does the labor market application differ from Spence (1973)? A: In Spence (1973), wages are competitive and pinned down by expected output, leaving no room to screen workers via monetary payments, so all screening must occur through costly credentials. In Yang’s model, the monopsonistic firm sets wages and all types face the same outside option, so monetary transfers can screen types. Proposition 3 says that when θB is stochastically nondecreasing in θA — higher-ability workers find credentials easier — no credential is needed in the optimal mechanism. The paper thus shows that costly screening is a feature of competitive, not monopsonistic, labor markets, under positive correlation of preferences.

Q: What is the bundling application and what new results does it yield? A: The paper reinterprets the multiproduct pricing problem by treating the grand bundle as the productive component and sub-bundles as costly instruments (since selling a sub-bundle instead of the grand bundle destroys social surplus relative to selling the grand bundle). Proposition 4 (nested bundling) establishes that a nested menu B of bundles is optimal among deterministic mechanisms if: (i) the incremental value of adding items to move from bundle b to b’ ⊃ b in B is strictly increasing in θ, and (ii) for any bundle b not in B, there exists a nested superset b’ ∈ B such that the value of b relative to b’ is nonincreasing in θ. This extends and complements Haghpanah and Hartline (2021), which is recovered as the special case of pure bundling (Proposition 5).

Q: What are the key scope conditions that delimit when Theorem 1 applies? A: Theorem 1 requires: (i) additive separability of preferences across productive and costly components; (ii) the surplus condition on sA (single-crossing of total surplus in the productive component); (iii) the positive correlation condition (stochastic monotonicity of θB in θA); and (iv) the costly instruments satisfy sB(y, θB) ≤ 0 for all y, θB. The productive allocation space X must be compact and one-dimensional; Y can be any measurable space. The agent’s type space can be multidimensional. The result holds for both private values and interdependent valuations on the principal’s side.

Q: Under what conditions does costly screening arise in practice, according to the model? A: The model predicts that if costly screening instruments are observed in practice, the consumers or agents with higher willingness to pay (or ability) for the productive good must tend to face higher costs for the screening action. For instance, higher-willingness-to-pay consumers who find waiting in line more costly (positively correlated preferences) would not be subjected to waiting as a screening device. If a firm uses waiting in line, it must be because higher-willingness-to-pay consumers find waiting less costly — consistent with negative correlation.

Costly Instruments: Allocations in the space Y such that the ex post social surplus sB(y, θB) = uB(y, θB) + vB(y, θB) ≤ 0 for all y and all θB. These include actions like waiting in line, collecting coupons, or obtaining credentials that destroy social surplus but may convey private information useful for screening.

Productive Component: The one-dimensional allocation dimension X in which both principal and agent derive non-negative surplus, representing the intrinsically valuable output of the mechanism (e.g., insurance coverage, job placement, bundle of goods).

Positive Correlation (Stochastic Monotonicity): The condition that θB is stochastically nondecreasing in θA: for any θA < θ̂A, the conditional distribution of θB given θA first-order stochastically dominates that given θ̂A. Equivalently, observing a higher θA conveys good news about θB. A sufficient condition is affiliation (Milgrom-Weber), but positive correlation is strictly weaker.

Surplus Condition: A single-crossing condition on the total surplus function sA(x, θA) for the productive component: for any x < x̂ and θA < θ̂A, if x̂ generates strictly more surplus than x at type θA, it continues to do so at θ̂A. This ensures a monotone efficient allocation rule exists and is the enabling condition for the Downward Sufficiency Theorem.

Downward Sufficiency Theorem (Theorem 2): The result that in any one-dimensional screening problem satisfying the surplus condition, there exists an optimal solution to the relaxed program (which ignores upward IC constraints) that also satisfies all upward IC constraints. This implies the principal need only enforce downward incentive constraints at the optimum.

Monotone Path Decomposition: A proof technique that writes the multidimensional type distribution as θ =^d (θA, h(θA; ε)) where ε ⊥ θA and h is nondecreasing in θA. Borrowed from dynamic mechanism design (Eso-Szentes, Pavan-Segal-Toikka), it reduces multidimensional IC problems to families of one-dimensional paths indexed by the independent residual ε.

Nested Bundling: A menu B of product bundles that can be totally ordered by set inclusion (b1 ⊂ b2 ⊂ … ⊂ bK). The paper shows that nested bundling is optimal under conditions that the incremental value of nesting is strictly increasing in type for bundles within B, and nonincreasing relative to any nested superset for bundles outside B.

Counterfactual Analysis for Structural Dynamic Discrete Choice Models

Mon, 01 Jan 0001 00:00:00 +0000

Research Question. Discrete choice data identify only differences in agents’ utilities, not utility levels. In dynamic discrete choice (DDC) models this means many policy-relevant counterfactuals — those requiring knowledge of utility in levels — are not point-identified. Kalouptsidi, Kitamura, Lima, and Souza-Rodrigues ask: how much can researchers learn about counterfactual outcomes under mild, verifiable restrictions, without imposing the strong normalizations that are standard in applied work but often hard to justify and potentially sign-reversing in their effects?

Setting and Methodology. The paper works within a canonical infinite-horizon DDC framework where an agent chooses among a finite action set each period, with additively separable per-period payoffs and i.i.d. unobservables. The econometrician observes conditional choice probabilities (CCPs) and state transition functions from panel data, but the payoff vector is underidentified by X free parameters (one per state), which is the source of non-identification of many counterfactuals. The authors characterize the sharp identified set for counterfactual CCPs, for low-dimensional outcomes such as average welfare, and develop both identification theory and a feasible inference procedure.

Main Identification Results. The sharp identified set for counterfactual CCPs is a smooth, connected manifold whose dimension equals the rank of a specific matrix (CJ*QJ) that the econometrician can compute directly from the data. This rank is at most X minus the number of linearly independent equality restrictions imposed. Two classes of commonly used restrictions reduce the dimension further without requiring full point identification: (i) local counterfactuals — experiments affecting only a subset of the state-action space — reduce the dimension to at most the number of eigenvalues of the relevant transformation matrix that differ from one; (ii) parametric payoffs with ηγ free parameters reduce the dimension to at most ηγ. Combining both achieves the tightest bound. Point identification is the special case where the rank equals zero.

For scalar low-dimensional outcomes (e.g., average welfare), the identified set is a compact interval whose endpoints are obtained by solving constrained optimization programs implementable in standard nonlinear solvers (e.g., Knitro), feasible even when the state space is large.

Quantitative Illustration. In the firm entry/exit Monte Carlo with state space X = 4 and a counterfactual entry subsidy removal: under Restriction 1 alone (outside option = 0, non-negative costs, known variable profits), the identified set for the change in the long-run probability of being active is [-0.1235, 0.0000], correctly signed and containing the true value of -0.0638. Adding shape restrictions (Restrictions 1–2) tightens the upper bound to -0.0341; adding the scrap-value exclusion restriction (Restrictions 1–3) tightens it to -0.0421. Analogous patterns hold for consumer surplus (true: -0.0875; bounds narrowing from [-0.1735, 0.0000] to [-0.1735, -0.0573]) and firm value (true: 0.9513; bounds from [0.0000, 1.8229] to [0.6388, 1.8229]). Critically, the authors show that setting scrap values to zero — the standard identifying assumption — is rejected by the data under Restrictions 1 and 2, because that payoff vector does not lie in the identified set.

Empirical Application. Revisiting Das, Roberts, and Tybout (2007) on Colombian exporters, the paper re-examines the horserace among export revenue, fixed cost, and entry cost subsidies. The DRT ranking (revenue subsidies dominate, entry cost subsidies rank last) survives under weaker restrictions than originally imposed, but hinges on the assumption that scrap values do not vary across states. Without that restriction, entry cost subsidies can potentially outperform the other types, reversing the original conclusion.

Inference. The paper develops a subsampling-based inference procedure that is asymptotically uniformly valid (bootstrap fails here due to non-regularity of the set boundary). The confidence set is constructed by inverting a quadratic-form distance test statistic. The critical practical recommendation is subsample size hN = N^{2/3}. The procedure remains feasible in binary choice models with state spaces up to X = 240 (dimension of the optimization problem: 720), where standard moment-inequality approaches are computationally infeasible.

Q: Why are many counterfactuals not point-identified in DDC models, even after the model is estimated? A: Choice data identify only differences in value functions across actions, not utility levels. The identifying matrix M has rank AX, leaving X free payoff parameters undetermined. Counterfactuals that depend on utility levels — such as the welfare impact of an entry subsidy when scrap values are unknown — therefore cannot be recovered uniquely from the data, even with a fully estimated model.

Q: What is the key object the paper characterizes, and what does it look like geometrically? A: The paper characterizes the sharp identified set for the counterfactual CCP vector p̃. Proposition 1 establishes that this set is a smooth, connected manifold with boundary, whose interior dimension equals rank(CJ*QJ). Connectedness is important because it means the set has no gaps and boundary tracing is sufficient to characterize it.

Q: How does the dimension of the identified set depend on the type of model restrictions imposed? A: Equality restrictions (d of them) reduce the maximum possible dimension from X to X–d. Local counterfactuals (affecting L state-action pairs) reduce the dimension further to at most the number of eigenvalues of the payoff transformation H(L) that differ from one, which is at most L. Parametric payoffs with ηγ free parameters cap the dimension at ηγ. Combining local counterfactuals with parametric payoffs gives the tightest bound: at most the number of eigenvalues of a related matrix D that differ from one, which is at most min(L, ηγ).

Q: Under what conditions does the identified set for counterfactual behavior collapse to a point? A: When rank(CJ*QJ) = 0, every payoff vector in the identified set PI maps to the same counterfactual CCP — that is, p̃ is point-identified even though the structural payoff π may not be. This can occur through a combination of equality restrictions and specific structure of the counterfactual experiment, without requiring full identification of all model parameters.

Q: What properties does the identified set for a scalar low-dimensional outcome have, and how is it computed? A: Under continuity of the outcome function φ and boundedness of the payoff identified set, the identified set for a scalar outcome θ is a compact interval [θL, θU]. The endpoints are computed as the minimum and maximum of a constrained optimization program over the joint space of counterfactual CCPs and payoff vectors, subject to the model’s Bellman equations, model restrictions, and equality constraints linking observed to counterfactual behavior. These programs can be solved with standard nonlinear solvers.

Q: What do the Monte Carlo results show about the informativeness of the bounds? A: In the firm entry/exit example with X = 4, the identified sets under only mild restrictions (non-negative costs, known variable profits, zero outside option) are already informative and correctly signed. For the change in the probability of being active (true value: -0.0638), the set under Restriction 1 alone is [-0.1235, 0.0000], establishing that the probability does not increase. Adding shape restrictions and exclusion restrictions progressively tightens the interval. All intervals contain the true parameter value, confirming sharpness.

Q: What does the paper show about the assumption of zero scrap values, which is standard in the entry cost literature? A: The paper shows that setting scrap values to zero can be rejected by the data: in the firm entry/exit example, the payoff vector with s = 0 does not belong to the identified set PI under Restrictions 1 and 2. This is empirically important because Kalouptsidi, Scott, and Souza-Rodrigues (2021) had previously shown that mistakenly setting scrap values to zero not only biases estimated entry costs downward but can also reverse the sign of a subsidy’s predicted effect.

Q: What is the main finding of the empirical application to export subsidies? A: Revisiting Das, Roberts, and Tybout (2007), the paper finds that the DRT ranking — export revenue subsidies dominate, entry cost subsidies rank last — can be confirmed under restrictions weaker than those DRT originally imposed. However, the ranking is not robust to allowing scrap values to vary across states: under that generalization, entry cost subsidies can potentially outperform the other subsidy types, reversing the original policy conclusion.

Q: Why does the bootstrap fail for inference in this setting, and why does subsampling work? A: The test statistic ĴN(θ0) involves the minimum of a quadratic form over a non-regular (kinked), random, and possibly nonconvex set. Bootstrap critical values are not asymptotically uniformly valid in this non-regular setting. Subsampling with subsample size hN → ∞, hN/N → 0 (the paper recommends hN = N^{2/3}) delivers asymptotically uniformly valid critical values under weak conditions, because it does not require regularity of the constraint set boundary.

Q: How does the inference approach handle the high dimensionality of DDC settings? A: The paper develops a computational algorithm specifically tailored to the structure of DDC models, exploiting the linear Bellman equation constraints to reduce the effective dimensionality of the optimization problem. In a binary choice model with X = 90, the joint optimization is over a 270-dimensional space; with X = 240 (as in Blundell, Gowrisankaran, and Langer, 2020), the dimension is 720. Standard moment-inequality inference methods (Kaido, Molinari, Stoye, 2019; Bugni, Canay, Shi, 2017) are computationally infeasible at these scales; the authors’ algorithm remains tractable.

Q: How does the paper relate to Norets and Tang (2014), the closest alternative approach? A: Norets and Tang (2014) partially identify structural parameters and high-dimensional counterfactual CCPs by relaxing the assumed distribution of idiosyncratic shocks, focusing on binary choice models and using a pointwise-valid Bayesian approach. The present paper instead targets low-dimensional policy outcomes (nonlinear functions of payoffs and counterfactual CCPs), accommodates multinomial choice, provides asymptotically uniformly valid frequentist inference via subsampling, and restricts the source of underidentification to the payoff function rather than the error distribution. The two contributions are non-nested and complementary.

Q: What is the practical workflow the paper enables for applied researchers? A: A researcher can (i) select any combination of model restrictions (equality or inequality, parametric or shape), (ii) specify any counterfactual experiment via an affine payoff transformation (H, g), and (iii) define any low-dimensional outcome of interest φ, then directly compute the identified set and a valid confidence interval by solving two constrained optimization programs — without deriving new analytical identification results for each specification. The rank condition for checking the dimension of the identified set is computable from the data.

Dynamic Discrete Choice (DDC) Model. A discrete-time infinite-horizon model where agents choose among a finite action set each period, with per-period utilities additively separable into an observed payoff function π and an i.i.d. unobservable shock, and agents maximize expected discounted lifetime utility. The model is parameterized by payoffs π, transition function F, discount factor β, and shock distribution G.

Conditional Choice Probability (CCP). The probability that an agent selects a given action in a given state, integrating out the unobservable shocks. CCPs and state transitions are directly identifiable from panel data and serve as the sufficient statistics for the identified set, in place of the unidentified payoff vector.

Sharp Identified Set for Counterfactual CCPs. The set PĨ(p, F) of all counterfactual CCP vectors p̃ that are consistent with the observed data (p, F) and the imposed model restrictions, given the specified counterfactual transformation. Characterized as a smooth connected manifold with dimension equal to rank(CJ*QJ).

Local Counterfactual. A counterfactual experiment in which the payoff transformation H modifies only a subset L of the state-action pairs, leaving the rest unchanged. Local counterfactuals reduce the dimension of the identified set relative to global experiments, because only the payoffs in the affected subset matter for the unidentified component of the counterfactual response.

Partial Identification / Identified Set for Outcomes. Rather than seeking a unique estimate of a counterfactual outcome θ, partial identification recovers the set ΘI of all values of θ consistent with the data and restrictions. For scalar outcomes this is a compact interval [θL, θU] whose endpoints solve constrained optimization problems over payoff and counterfactual CCP spaces.

Subsampling Inference. A procedure for constructing asymptotically uniformly valid confidence sets by repeatedly computing the test statistic on subsamples of size hN < N, approximating the sampling distribution of ĴN(θ0) without requiring regularity (smoothness) of the boundary of the constraint set — a requirement that fails here due to the kinked, nonconvex nature of the identified set.

Rank Condition for Dimension. The dimension of the identified set for counterfactual CCPs is determined by the rank of the matrix CJ*QJ, which depends on the counterfactual transformation H, the model restrictions, and the observed data. The econometrician can compute this rank from observables to assess, before imposing any strong assumptions, how many dimensions of freedom remain in the identified set.

Customer Acquisition, Business Dynamism and Aggregate Growth

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether firm-level customer acquisition — distinct from productivity differences — is a quantitatively important driver of aggregate economic growth, and whether ignoring it distorts predictions about growth policy efficacy. The authors build a novel endogenous growth model in which innovating firms must first accumulate customers to sell their products, with two channels of customer acquisition operating simultaneously: costly sales-and-marketing expenditure and below-static-markup pricing (sales-driven accumulation). The model is estimated using indirect inference against a combination of aggregate data (U.S. real GDP per worker growth of 1.43% annually, 1979–2019), Business Dynamics Statistics (BDS) life-cycle profiles, and firm-level data from Compustat matched to Capital IQ’s sales-and-marketing expense records covering 1997–2019.

The benchmark model yields four closed-form propositions. First, a “firm-level market size effect”: higher customer retention raises a firm’s future profit base, strengthening incentives to conduct R&D. Second, an endogenous feedback loop: more productive firms invest more in customer acquisition, which expands their customer base and further strengthens R&D incentives. Third, customer base accumulation raises aggregate growth, but only indirectly — by boosting firm-level innovation rates — since aggregate productivity is a customer-weighted average of firm productivity levels. Fourth, the sensitivity of innovation to R&D subsidies increases with customer base growth, because firms with faster-growing customer bases discount future profits less steeply.

In the quantitatively estimated full model — which relaxes the benchmark’s perfect-scaling restrictions and endogenizes firm entry and exit — the authors conduct two decomposition exercises. In a counterfactual scenario where expected customer retention is reduced to make average customer base growth zero among continuing businesses, firm-level innovation rates fall by approximately 40% relative to the full model. Of this 40% decline, only about 6 percentage points are attributable to the direct firm-level market size effect alone; the vast majority is driven by the endogenous feedback loop between innovation and customer acquisition. In a second decomposition focused on aggregate growth, the firm-level market size effect and a reallocation effect — whereby the feedback loop concentrates customers among high-productivity firms — together account for 44% of aggregate growth in the full model.

On policy, the authors compare R&D subsidies and operational subsidies in the full model against an otherwise identical model that ignores customer accumulation. R&D subsidies are approximately twice as effective at boosting aggregate growth in the full model as in the model without customer accumulation. Conversely, operational subsidies produce a stronger decline in aggregate growth in the full model than in the benchmark-without-customer-accumulation, because aggregate growth in the full model is a customer-weighted average of firms’ productivity growth rates, making the joint distribution of productivity and customer bases the relevant object of study.

Firm-level data support three empirical predictions. Marketing expenditure, R&D intensity, and markups co-move in model-consistent directions both contemporaneously and over the life cycle. The estimated relative weight of marketing versus pricing as channels of customer accumulation is γ = 0.745, indicating marketing is the dominant channel. A model-consistent proxy for the severity of customer-base frictions, estimated in the cross-section of industries, shows that stronger frictions correlate with lower R&D investment, as predicted. The customer-base depreciation rate is estimated at ζ = 0.375, R&D cost scaling at σx = 1.264, and marketing cost scaling at σa = 1.405.

Q: What is the firm-level market size effect and why does it arise? A: When a firm retains more customers, successful innovations apply to a larger market, raising the profitability of each unit reduction in production costs. This increases the marginal benefit of R&D investment. In the benchmark model, Proposition 2(a) shows formally that firm-level innovation increases with customer base growth: ∂x/∂(1−ζ) > 0, where ζ is the customer separation rate.

Q: What is the endogenous feedback loop between innovation and customer accumulation? A: More productive firms have lower production costs and can therefore afford greater investment in marketing and can set lower markups, both of which attract more customers. A larger customer base raises firm value and strengthens R&D incentives further (Proposition 2(b)). This bidirectional feedback means that productivity growth and customer accumulation are jointly determined in equilibrium, not independent processes.

Q: How large is the quantitative effect of customer accumulation on firm-level innovation? A: In the counterfactual where expected customer retention is reduced so that average customer base growth among continuing firms is zero, firm-level innovation rates are approximately 40% lower than in the full model. Of this, only about 6% (of the total drop) is attributable to the direct market size effect in isolation; the feedback loop accounts for the remaining roughly 34 percentage points.

Q: How much of aggregate growth do customer-acquisition channels explain? A: The firm-level market size effect and a customer reallocation effect together account for 44% of aggregate growth in the full model. The firm-level market size effect alone reduces aggregate growth by about one-fifth (20%) in the relevant counterfactual. The reallocation effect — by which productive firms accumulate disproportionate market share — contributes the remainder of the 44%.

Q: What is the reallocation channel for aggregate growth? A: Because highly productive firms can invest more in customer acquisition, the feedback loop endogenously concentrates customers (market shares) among high-productivity firms. Since aggregate productivity in the model is a customer-weighted average of firm productivity levels (equation 16), this reallocation raises aggregate productivity growth beyond what the firm-level R&D incentive effect alone would produce.

Q: How does customer accumulation change the efficacy of R&D subsidies? A: R&D subsidies are approximately twice as effective at raising aggregate growth in the full model (with customer accumulation) as in an otherwise identical model that ignores customer accumulation. The mechanism is Proposition 4(b): faster customer base growth makes firms weight future profits more heavily, increasing their sensitivity to any change in R&D costs, including that brought about by a government subsidy.

Q: What happens to aggregate growth under operational subsidies in the two models? A: Operational subsidies lead to a stronger decline in aggregate growth in the full model than in the model without customer accumulation. The reason is that aggregate growth in the full model depends on the joint distribution of firm productivity and customer bases; operational subsidies alter this distribution in ways that reduce the customer-weighted average of productivity growth rates, an effect absent when customer accumulation is ignored.

Q: How are the two customer-acquisition channels (marketing and pricing) measured empirically? A: Marketing is measured using sales-and-marketing expenses from Capital IQ, available for 48% of the Compustat sample (34% report directly; an additional 14% report advertising or marketing sub-components). Markups are measured following De Loecker et al. (2020) as the inverse share of variable costs in sales multiplied by the cost-output elasticity, with variation across firms identified from balance sheet data under the assumption that cost-output elasticities are constant within industry-year cells.

Q: What is the estimated relative strength of marketing versus pricing in customer accumulation? A: The relative weight on marketing is γ = 0.745, estimated by targeting the coefficient βµ = 0.04 (standard error 0.01) from a reduced-form regression of firm-level sales growth on changes in markups (equation 29). This implies that marketing is the dominant channel, consistent with evidence in Afrouzi et al. (2021) and Fitzgerald et al. (forthcoming).

Q: What is the estimated customer-base depreciation rate and how is it disciplined? A: The depreciation rate ζ is estimated at 0.375, targeted to match average firm-level employment growth from the BDS. This falls toward the lower end of existing estimates, which range from about 0.3 to 0.7 across studies.

Q: How do R&D costs scale with firm size in the estimated model? A: The R&D cost scaling parameter is σx = 1.264, estimated by targeting the reduced-form coefficient of −0.01 from a regression of log R&D intensity on log sales with industry-time fixed effects (equation 28). This is close to the estimate in Akcigit and Kerr (2018).

Q: How do marketing costs scale with firm size? A: The marketing cost scaling parameter is σa = 1.405, estimated by targeting a reduced-form coefficient of −0.01 from a regression of log sales-and-marketing intensity on log sales with industry-time fixed effects (equation 30).

Q: What empirical co-movement evidence supports the model’s predictions? A: In the cross-section of firms, marketing expenditure, R&D intensity, and markups all co-move in model-predicted directions, for both static (contemporaneous) relationships and dynamic (life-cycle) patterns. Additionally, a model-consistent industry-level proxy for the severity of customer-base frictions shows that stronger frictions are associated with lower R&D investment, as the model predicts.

Q: How does endogenous firm exit work in the full model and why does it differ from standard models? A: Firms pay a stochastic per-period operational cost and exit when that cost exceeds a threshold κ*_j = v(q_j, b_j)/W. Unlike standard growth models where exit depends only on productivity, here the exit threshold depends on both productivity and accumulated customers, so customer loss can trigger exit even for relatively productive firms.

Q: What data sources are used and what are their key limitations? A: The three primary firm-level sources are the Census Bureau’s BDS (broad coverage, employment-focused), Compustat (rich financial data but limited to publicly traded firms and lacking direct customer-acquisition measures), and Capital IQ (sales-and-marketing expenses available from 1997, matched to 91% of the Compustat sample). To address Compustat’s non-representativeness, employment-based weights aligning Compustat and BDS firm-size distributions are applied when computing model moments against Compustat targets.

Firm-level market size effect: The mechanism by which higher customer retention raises a firm’s future profit base — because lower production costs from successful innovation apply to a larger market — thereby strengthening incentives to conduct R&D. This is the primary channel linking customer accumulation to innovation.

Customer base (b_j): The mass of household members consuming a firm’s product variety, which varies endogenously across firms. It enters demand directly (equation 4) and serves as a state variable in the firm’s value function alongside productivity.

Endogenous feedback loop: The bidirectional reinforcement between productivity growth and customer accumulation. More productive firms invest more in customers; a larger customer base raises the value of innovation; higher innovation raises productivity further.

Reallocation effect: The concentration of customers (market shares) toward high-productivity firms that arises endogenously from the feedback loop, contributing to aggregate growth because aggregate productivity is a customer-weighted average of firm-level productivity.

Customer-base depreciation rate (ζ): The exogenous rate at which a firm loses its existing customers each period, estimated at 0.375 in the paper’s calibration. It governs the baseline speed of customer attrition and is the key parameter for the firm-level market size effect.

Sales-and-marketing expenses: Expenditures on sales force, brand development, customer service, advertising, and customer data acquisition — measured from Capital IQ — that directly drive marketing-based customer accumulation (the dominant channel with estimated weight γ = 0.745).

Perfect scaling (Assumption 1): The benchmark restriction that R&D and marketing costs, and the sales-driven customer accumulation benefit, all scale one-for-one with a composite of firm productivity and customer base. This assumption enables closed-form solutions and is relaxed in the full model using estimated scaling parameters.

De Gustibus and Disputes about Reference Dependence

Mon, 01 Jan 0001 00:00:00 +0000

This paper examines whether heterogeneity in individual gain-loss attitudes — the degree to which people weigh losses more or less severely than equivalent gains — contaminates prior tests of expectations-based reference dependence (EBRD). The central question is: do prior experiments that appear to yield mixed or null evidence against EBRD actually reflect a failure of the expectations-based reference point, or instead reflect a methodological flaw — the implicit assumption that all individuals are uniformly loss averse?

All prior tests of EBRD models (e.g., Kőszegi and Rabin 2006, 2007) have proceeded under what the authors call “universal loss aversion,” the assumption that every individual weighs losses more heavily than commensurate gains (λ > 1). The authors argue that this assumption — a form of the classic De Gustibus conjecture — is empirically incorrect and theoretically distorting: within EBRD designs, loss-averse and gain-seeking subjects are predicted to respond in opposite directions to expectations manipulations, so aggregating across them suppresses or reverses treatment effects.

The authors run two pre-registered laboratory experiments totaling 1,524 subjects. The labor supply experiment (N = 500, UC San Diego) uses a two-stage design. Stage 1 elicits each subject’s gain-loss attitude parameter λ_i from their effort responses to fixed versus uncertain piece rates in a real-effort transcription task, exploiting the prediction that loss-averse workers reduce effort under wage uncertainty while gain-seeking workers increase it. Stage 2 manipulates expectations by varying the probability of a high outside payment (p = 0.05 in Condition Low vs. p = 0.45 in Condition High), holding the piece-rate probability constant at 50%; under EBRD, this shifts the reference point and should change effort in a direction governed by λ_i.

The exchange experiment (N = 1,024, University of Bonn, with a pre-registered 2018 replication of N = 417) uses Stage 1 preference statements over randomly endowed objects to estimate λ_i, and Stage 2 manipulates expectations via a 0% vs. 50% probability of forced exchange. Under EBRD, loss-averse subjects should become more willing to exchange in the High condition; gain-seeking subjects should become less willing.

Both experiments document substantial heterogeneity in gain-loss attitudes. In the labor supply study, approximately 70.6% of subjects exhibit loss aversion (λ̂ > 1) and 29.4% exhibit gain-seeking (λ̂ < 1), with an average structural estimate of λ̂ = 1.65 and median 1.66. In the exchange study, 76% are loss averse and 24% are gain-seeking, with mean λ̂ = 1.49 and median 1.34. Lottery-based elicitation in the labor supply experiment yields 28% gain-seeking, consistent with prior literature estimates of roughly 22% gain-seeking from Chapman et al. (2018).

Crucially, Stage 1 gain-loss attitudes are strongly predictive of Stage 2 treatment effects in both experiments. In the labor supply study, the aggregate treatment effect of approximately 26% greater effort in Condition High — reproducing Abeler et al. (2011) — masks strongly heterogeneous responses: higher λ̂ predicts larger positive treatment effects (raw correlation ρ = 0.18, p < 0.01), and controlling for heterogeneous gain-loss attitudes raises R² by more than a factor of 10. In the exchange study, the aggregate treatment effect is precisely zero (coefficient = 0.00, clustered s.e. = 0.03), a result that prior literature would interpret as contradicting EBRD; but once gain-loss heterogeneity is accounted for, treatment effects are strongly positive for loss-averse subjects and negative for gain-seeking subjects, again raising R² by more than a factor of 10.

Gain-seeking subjects exhibit negative treatment effects in the exchange study, consistent with EBRD predictions, but in the labor supply study the average treatment effect for gain-seeking subjects remains slightly positive, representing a partial deviation from the model’s quantitative predictions. The authors interpret this as evidence that expectations-based reference points are an important but likely incomplete determinant of behavior, with attention-based, status-quo-based, or anchoring-based reference points potentially playing supplementary roles.

Q: What is the central methodological problem with prior tests of expectations-based reference dependence?

A: All prior tests assumed universal loss aversion — that every individual has λ > 1, i.e., weighs losses more severely than equivalent gains. The authors show this is both empirically wrong (roughly 24–29% of subjects are gain-seeking across both studies) and theoretically distorting: within EBRD designs, gain-seeking individuals are predicted to respond in the opposite direction from loss-averse individuals, so averaging across heterogeneous types can suppress, zero out, or even reverse the true treatment effect. This makes standard aggregate tests of EBRD unreliable.

Q: How do the authors measure gain-loss attitudes in the labor supply experiment?

A: In Stage 1, subjects make 30 effort decisions across fixed piece rates and uncertain piece rates with the same mean. Under the Kőszegi-Rabin CPE model, a loss-averse individual reduces effort when the wage is uncertain (because outcomes can fall below the reference point), while a gain-seeking individual increases effort under uncertainty. The authors estimate individual-level parameters by regressing log(e_i + 10) on log(w) and Δw/w in a random-coefficients framework; the coefficient l̂_i on Δw/w is the reduced-form measure of gain-loss attitudes, with λ̂_i = 1 + 4·(l̂_i/ĝ_i) as the structural estimate. The correlation between the two measures is ρ = 0.85 (p < 0.01).

Q: How do the authors measure gain-loss attitudes in the exchange experiment?

A: In Stage 1, subjects are randomly endowed with one of two objects and provide three unincentivized preference statements (relative liking, relative wanting, and hypothetical choice) before any possibility of exchange is introduced. Under CPE, an individual endowed with object X will prefer X to the extent that (1 + λ_i) − 2(Y/X) > 0, so subjects with higher λ_i should more strongly favor their endowment. A principal components analysis reduces the three statements to one factor (capturing ~70% of variation), and residuals from regressing that factor on object assignment constitute the reduced-form measure l̂_i. The structural estimate λ̂_i is obtained via a mixed logit using a log-normal distribution for λ_i; the reduced form and structural measures are correlated at r = 0.95 (p < 0.01).

Q: What does the distribution of gain-loss attitudes look like across the two experiments?

A: In the labor supply experiment (N = 453 estimable subjects), 70.6% are loss averse and 29.4% are gain-seeking, with mean λ̂ = 1.65 and median λ̂ = 1.66. In the exchange experiment (N = 1,024), 76% are loss averse and 24% are gain-seeking, with mean λ̂ = 1.49 and median λ̂ = 1.34. A separate lottery-based elicitation in the labor supply study finds 28% gain-seeking subjects. These proportions are consistent with the weighted average of 22% gain-seeking found by Chapman et al. (2018) across seven prior lottery-choice studies.

Q: What is the aggregate treatment effect in the labor supply experiment, and what does it look like once heterogeneity is accounted for?

A: Without accounting for gain-loss heterogeneity, Condition High is associated with roughly a 26% increase in effort relative to Condition Low (individual-clustered s.e. = 0.03, p < 0.01), reproducing the Abeler et al. (2011) result and consistent with EBRD under universal loss aversion. However, R² = 0.03. Once interactions of Condition High with l̂_i and λ̂_i are included, R² rises to 0.40 and 0.39 respectively — more than a tenfold increase. Higher λ̂_i predicts larger positive treatment effects (raw correlation ρ = 0.18, p < 0.01), and the interaction of Condition High with λ̂_i is highly significant (F(1,452) = 49.14, p < 0.01).

Q: What is the aggregate treatment effect in the exchange experiment, and what does it look like once heterogeneity is accounted for?

A: Without heterogeneity, the treatment effect of Condition High on the probability of exchanging is precisely 0.00 (clustered s.e. = 0.03), which prior literature would read as a failure of EBRD. Once heterogeneity is introduced via interactions with l̂_i and λ̂_i, the pattern changes markedly: loss-averse subjects show positive treatment effects (greater willingness to exchange in High), while gain-seeking subjects show negative treatment effects (less willingness to exchange in High), consistent with Predictions 4–6. R² again rises by more than a factor of 10. In Condition Low, 38% of subjects exchange, reflecting a significant endowment effect (F(1,1022) = 25.66, p < 0.01).

Q: Why does the aggregate treatment effect in the exchange experiment equal zero?

A: The authors show in Appendix B.4 that the relationship between λ_i and exchange probability treatment effects can be concave — negative effects for gain-seeking subjects can be of greater absolute magnitude than positive effects for loss-averse subjects. With roughly 24% gain-seeking and 76% loss-averse subjects, aggregation can yield a near-zero average even when heterogeneous effects are substantial and directionally consistent with EBRD. This aggregation problem, not a failure of the expectations-based reference point mechanism, explains the null aggregate result.

Q: Do gain-loss attitudes measured in one domain predict behavior in another domain?

A: The lottery-based measure of gain-loss attitudes (from Multiple Price Lists administered after the real-effort task in the labor supply experiment) has mean λ̂ = 1.48 and median 1.42, with 28% gain-seeking subjects — proportions similar to the labor supply estimates. However, the correlation between the lottery-based and labor-supply-based structural estimates of λ̂ is only Pearson’s r = 0.091 (p = 0.03) and Spearman’s ρ = 0.084 (p = 0.075). Furthermore, the lottery measure has no predictive power for Stage 2 treatment effects. This suggests that while the prevalence of gain-seeking is similar across domains, gain-loss attitudes at the individual level are more domain-specific than prior work has appreciated.

Q: How do the authors address the “generated regressor problem” when using estimated λ̂_i as a regressor?

A: Since λ̂_i is itself estimated from Stage 1 data, using it directly as a regressor in Stage 2 regressions treats imprecise preference estimates as ideal data, which can distort inference (the Murphy-Topel problem). The authors address this by bootstrapping the entire pipeline — re-estimating gain-loss attitudes from Stage 1 in each of 500 bootstrap iterations and re-running the Stage 2 regressions — then reporting the average bootstrap coefficient and its standard deviation. The bootstrapped conclusions are qualitatively identical to the original regression results in both experiments.

Q: What limitations do the authors acknowledge in the EBRD model’s fit?

A: Even after accounting for heterogeneity, the EBRD model does not provide a complete quantitative account of behavior. In the labor supply experiment, gain-seeking subjects exhibit slightly positive average treatment effects (not negative as predicted), and loss-averse subjects’ empirical treatment effects fall short of theoretical predictions, despite a significant correlation between predicted and empirical treatment effects (ρ = 0.25, p < 0.01). The authors attribute these deviations to potential measurement error (which would attenuate estimated relationships), and to the possibility that reference points have multiple determinants — including status quo-based, attention-based, and anchoring-based factors — beyond expectations alone.

Q: What are the broader implications for other applications of gain-loss attitudes?

A: The paper’s findings have implications for any application that relies on universal loss aversion as a maintained assumption, including Rabin’s (2000) calibration argument for risk aversion at small and large stakes, insurance demand for small losses (Slovic et al., 1977), and preferences for bunched resolution of uncertainty (Kőszegi and Rabin, 2009). Admitting heterogeneity in gain-loss attitudes will require more nuanced predictions in each of these settings. The paper provides a methodology — measuring individual-level gain-loss attitudes within the experimental context of interest — for investigating and controlling for such heterogeneity.

Q: What design features prevent confounds between Stage 1 measurement and Stage 2 treatment in the exchange experiment?

A: Stage 1 uses a different pair of objects (USB stick and pens) than Stage 2 (picnic mat and thermos), or vice versa — each subject encounters each pair exactly once, with counterbalancing at the session level. Stage 1 preference statements are unincentivized and made before any possibility of exchange is introduced, so they do not contaminate the Stage 2 expectations manipulation. The random reassignment of objects at the end of Stage 1 generates exogenous variation in endowments, preventing mechanical confounds. The authors also verify that interpreting Stage 1 variation as reflecting heterogeneity in object valuations (rather than gain-loss attitudes) would predict zero heterogeneous treatment effects in Stage 2 — a prediction rejected by the data.

Expectations-Based Reference Dependence (EBRD): The formulation, due to Kőszegi and Rabin (2006, 2007), in which an individual’s reference point is the entire distribution of outcomes they rationally expected, rather than a fixed status quo. Behavior is governed by a Choice-Acclimating Personal Equilibrium (CPE) in which the chosen action is optimal given that the expectation of that action serves as the reference.

Gain-Loss Attitudes (λ_i): The individual-specific parameter governing how outcomes above versus below the reference point affect utility. Under piecewise-linear gain-loss utility, an outcome that falls short of the reference by z reduces utility by η·λ_i·z, while an outcome above it raises utility by η·z. Loss aversion is λ_i > 1; gain-seeking is λ_i < 1; loss neutrality is λ_i = 1. In this paper, λ_i is treated as heterogeneous across individuals rather than assumed uniform.

Universal Loss Aversion: The implicit homogeneity assumption maintained in all prior tests of EBRD — that every individual has λ > 1. The authors characterize this as a form of the De Gustibus Non Est Disputandum conjecture applied to gain-loss attitudes, and document that it fails empirically in both experimental settings.

Choice-Acclimating Personal Equilibrium (CPE): The rational expectations equilibrium concept from Kőszegi and Rabin (2006, 2007) used throughout the paper to derive comparative statics. A choice is a CPE if its expected utility given its own expectation as the reference exceeds the expected utility of any alternative given that alternative’s expectation as the reference.

Reduced-Form Gain-Loss Measure (l̂_i): In the labor supply context, the individual-level OLS coefficient on Δw/w in a log-effort regression — capturing how strongly a subject reduces (or increases) effort under wage uncertainty relative to a fixed wage of equal mean. A positive l̂_i identifies loss aversion; negative identifies gain-seeking. In the exchange context, the analogous measure is the residual from regressing the first principal component of Stage 1 preference statements on object assignment.

Aggregation Problem: The paper’s central methodological contribution — when gain-loss attitudes are heterogeneous and the EBRD treatment effect is non-linear in λ_i, the average treatment effect across a heterogeneous population need not equal the treatment effect at the average λ. In the exchange experiment, the aggregate treatment effect is precisely zero even though loss-averse and gain-seeking subjects each respond in the theoretically predicted (opposite) direction, because the concave relationship between λ_i and the exchange probability treatment effect causes negative gain-seeking effects to dominate in the aggregate.

Decision Theory for Treatment Choice Problems with Partial Identification

Mon, 01 Jan 0001 00:00:00 +0000

This paper applies classical statistical decision theory (Wald 1950) to treatment choice problems where the data only partially identify payoff-relevant parameters. The policy maker chooses an action a in [0,1] — interpreted as the share of the population assigned to a new policy — to maximize welfare that is linear in the action. The data are Gaussian, and the key departure from prior literature is that the mean function mapping parameters to data need not be injective, so even infinite data may not reveal the optimal action.

The paper evaluates decision rules under three classical criteria: admissibility, maximin welfare, and minimax regret (MMR).

Admissibility result (Theorem 1): Under nontrivial partial identification, every decision rule — however exotic — is welfare-admissible. No rule is dominated. This is a sharp reversal from point-identified settings, where admissibility meaningfully restricts the rule class: in the scalar point-identified case (n=1, m(theta)=theta), Karlin and Rubin’s (1956) result implies that any non-threshold rule is dominated. The proof exploits completeness of the Gaussian statistical model: if a dominating rule d’ existed, it would have to agree almost everywhere with d, yielding a contradiction. Theorem 5 generalizes this result beyond Gaussian likelihoods, tying it to bounded completeness of the statistical model.

Maximin welfare result (Theorem 2): The maximin criterion selects the no-data rule d(y) = 0 — preserve the status quo regardless of data — whenever the status quo welfare is the infimum over states with non-positive welfare contrast. In the running example, maximin welfare equals zero and is achieved by never assigning the new policy. This echoes critiques from Savage (1951) and Manski (2004) about ultra-pessimism.

Minimax regret result (Theorem 3): In point-identified problems, the MMR rule is essentially unique and nonrandomized (Canner 1970; Stoye 2009a; Tetenov 2012). Under partial identification, when the identified set is large enough — formally, when I(0) is large enough and there exists mu in the identified set with I(mu) > I(0) — there are infinitely many MMR optimal rules, and any symmetric, weakly increasing MMR rule depending only on the sufficient statistic (w*)^T Y must randomize for some data realizations. Moreover, if I(mu) is differentiable at zero, no linear threshold rule is MMR optimal.

Least randomizing MMR rule (Theorem 4): Because policy randomization is difficult to implement in practice, the authors uniquely characterize the MMR optimal rule that randomizes least frequently. Among all symmetric, weakly increasing, unimodal MMR optimal rules depending on (w*)^T Y, the rule d*_linear has the smallest randomization region — every other distinct such rule has a strictly wider randomization region. This rule can be profiled-regret dominant over the Stoye (2012a)/Yata (2023) MMR rule (Proposition 2), and the uniformly randomizing rule is inadmissible under profiled regret (Proposition 3). Under some conditions, d*_linear can also be obtained as the MMR rule within a class that penalizes randomized assignments equally (Proposition 4).

Three applications ground the theory. First, in Ishihara and Kitagawa’s (2021) evidence aggregation framework — extrapolating treatment effects from n source countries to a target country — the least randomizing rule randomizes only when estimated bounds on the target treatment effect straddle zero, linking decision rules directly to identified-set estimators. Second, in LATE extrapolation (Mogstad et al. 2018), all decision rules are admissible and IV-based threshold rules are not dominated. Third, in the omitted-variable-bias setting of Diegert et al. (2022), the decision-theoretic breakdown point — the largest confounding magnitude under which the seemingly better policy should be adopted without hedging — tolerates strictly more confounding than Diegert et al.’s breakdown point, where the threshold is k = sqrt(pi/2) * sigma.

Q: What is the central research question? A: The paper asks how classical statistical decision theory — admissibility, maximin welfare, minimax regret — applies when the data only partially identify the payoff-relevant parameters governing a binary treatment choice. Prior literature had developed these criteria for point-identified settings; this paper characterizes how partial identification fundamentally changes the answers.

Q: What is the formal framework? A: The policy maker chooses a in [0,1] (population share assigned to the new policy) with welfare W(a,theta) = a*W(1,theta) + (1-a)*W(0,theta), linear in a. The data are Y ~ N(m(theta), Sigma) with known m and Sigma. Partial identification arises when m is not injective, so distinct parameter values theta and theta’ with opposite-sign welfare contrasts U(theta) = W(1,theta) - W(0,theta) can produce the same data distribution.

Q: Why does admissibility lose all refinement power under partial identification? A: Theorem 1 shows that every decision rule is admissible when there is nontrivial partial identification. The mechanism is Gaussian completeness: if a dominating rule d’ existed, then for every data distribution in the model, d and d’ would have equal expected values, which by completeness implies d = d’ almost everywhere — a contradiction. This relies on the fact that nontrivial partial identification ensures that each data distribution is compatible with both positive and negative welfare contrasts, preventing the construction of a uniformly dominating rule.

Q: What is the contrast with point-identified settings? A: In the scalar point-identified case (n=1, m(theta)=theta, W(1,theta)=theta, W(0,theta)=0), Karlin and Rubin’s (1956) theorem implies any non-threshold rule is dominated; admissibility restricts attention to threshold rules. Partial identification completely eliminates this refinement: even randomized or otherwise arbitrary rules are admissible.

Q: What does the maximin welfare criterion recommend? A: Theorem 2 shows that when the status quo welfare equals the infimum of welfare over states with non-positive welfare contrast, the maximin optimal rule is d(y) = 0 for all y — preserve the status quo regardless of the data. In the running evidence-aggregation example, maximin welfare equals zero and is achieved by never assigning the new policy. The criterion ignores all data because the worst case is always achieved at states where the new policy performs no better than the status quo.

Q: What is the minimax regret criterion and why is it preferred? A: Expected regret at state theta is R(d,theta) = U(theta)*{1{U(theta)>=0} - E[d(Y)]} — the expected welfare loss relative to the oracle who knows theta. A rule is MMR optimal if it minimizes worst-case expected regret. Unlike maximin welfare, MMR uses data and balances risks across states. In point-identified settings it yields essentially unique, nonrandomized rules.

Q: How does partial identification change the MMR solution set? A: Theorem 3 shows that when the identified set is large enough — I(0) is sufficiently large and there exists mu with I(mu) > I(0) — there are infinitely many MMR optimal rules, and every symmetric, weakly increasing MMR rule depending on the sufficient statistic (w*)^T Y must randomize for some data realizations. If I(mu) is differentiable at zero, no linear threshold rule is MMR optimal. Different MMR rules can recommend different policies for the same data, creating a nontrivial multiplicity problem.

Q: How is the least randomizing MMR rule characterized? A: Theorem 4 shows that among all symmetric, weakly increasing, unimodal MMR optimal rules that depend on data only through (w*)^T Y, the rule d*_linear has the smallest randomization region: every other distinct rule in this class has a strictly wider randomization region, V(d*_linear) ⊆ V(F∘w*) with strict inclusion when F ≠ d*_linear. This characterization is essentially unique and provides a pragmatic refinement of the MMR solution set.

Q: What is profiled regret and why is it used? A: Profiled regret reports worst-case expected regret at each fixed value of the point-identified parameters, rather than worst-case over all parameters jointly. Proposition 2 shows that the least randomizing rule d*_linear can profiled-regret dominate the Stoye (2012a)/Yata (2023) MMR rule in the running example. Proposition 3 shows that the uniformly randomizing rule is profiled-regret inadmissible when profiling over point-identified parameters. This concept provides an additional selection criterion within the MMR solution set.

Q: Can the least randomizing rule be derived from an explicit welfare penalty? A: Proposition 4 shows that, under some conditions, d*_linear is minimax regret optimal within the class of rules that penalize all randomized assignments equally. This connects the least randomizing criterion to a modified welfare function that treats randomization itself as costly, providing an interpretation for the refinement beyond mere pragmatics.

Q: What does the evidence aggregation application show? A: In the Ishihara-Kitagawa (2021) framework — extrapolating effects from n source countries to a target country using Lipschitz smoothness — the least randomizing rule randomizes only (though not always) when the estimated bounds on the target treatment effect contain both positive and negative values. When bounds are entirely positive or entirely negative, the rule recommends a deterministic action. This shows how identified-set estimators directly enter decision-theoretically optimal rules.

Q: What does the LATE extrapolation application show? A: In the Mogstad et al. (2018) setting with a binary instrument and no covariates, where the payoff-relevant parameter is a policy-relevant treatment effect corresponding to expanding the complier subpopulation, Theorem 1 applies: all decision rules are admissible. In particular, the IV threshold rule — implement the policy for large IV estimates — is not dominated, providing decision-theoretic grounding for a common empirical practice.

Q: What does the omitted variable bias application show? A: In the Diegert et al. (2022) setting where the identified set for the long regression coefficient given the medium regression coefficient is [beta_med - k, beta_med + k], the least randomizing MMR rule is d*_linear(beta_hat_med) when k > sqrt(pi/2) * sigma. The decision-theoretic breakdown point — the largest k under which the seemingly better policy should be adopted without randomization — is strictly larger than Diegert et al.’s sensitivity breakdown point, meaning the decision-theoretic approach tolerates more confounding before recommending hedging.

Q: How does Theorem 5 generalize Theorem 1 beyond Gaussian likelihoods? A: Theorem 5 extends the admissibility result by connecting it to bounded completeness of the statistical model rather than Gaussian-specific completeness. This shows that the collapse of admissibility’s refinement power is not an artifact of normality but a general consequence of partial identification combined with a sufficiently rich statistical model.

Q: What is the paper’s broader implication for empirical practice? A: The results show that under partial identification, two of the three classical decision-theoretic criteria (admissibility and maximin welfare) provide no useful guidance — the former because everything passes, the latter because it ignores data entirely. MMR remains the operative criterion but yields infinitely many rules, all requiring some randomization. The least randomizing refinement provides a unique, practically implementable rule that connects to estimated identified sets and tolerates more ambiguity than purely statistical sensitivity analyses.

Partial identification: A setting where even infinite data cannot uniquely determine payoff-relevant parameters, because the mean function m mapping parameters to data distributions is not injective. Distinct parameter values with opposite-sign welfare contrasts may be observationally equivalent.

Welfare contrast U(theta): The difference W(1,theta) - W(0,theta) between the welfare under the new policy and under the status quo at parameter theta. The oracle optimal action is 1{U(theta) >= 0}.

Admissibility (welfare): A rule d is admissible if no rule d’ weakly dominates it in expected welfare at every theta with strict improvement at some theta. Under partial identification with Gaussian likelihood, every rule is admissible — admissibility has no refinement power.

Maximin welfare optimality: A rule is maximin optimal if it attains the highest worst-case expected welfare. Under partial identification, this criterion selects the no-data rule (always preserve status quo) whenever the status quo welfare equals the infimum over states with non-positive welfare contrast.

Minimax regret (MMR) optimality: A rule minimizes the worst-case expected welfare loss relative to the oracle action. Under severe enough partial identification, MMR optimal rules are non-unique and all require randomizing policy recommendations for some data realizations.

Least randomizing MMR rule (d*_linear): The unique MMR optimal rule with the smallest randomization region among all symmetric, weakly increasing, unimodal MMR rules depending on the sufficient statistic. Characterized in Theorem 4; randomizes only when estimated identified set bounds straddle zero in the running example.

Profiled regret: The worst-case expected regret at each fixed value of the point-identified parameters, treating them as a parameter of interest and profiling out the partially identified parameters. Provides a finer ranking within the MMR solution set and renders the uniformly randomizing rule inadmissible.

Demand Analysis under Latent Choice Constraints

Mon, 01 Jan 0001 00:00:00 +0000

Agarwal and Somaini study demand estimation in markets where consumers face latent choice constraints — situations where a consumer’s effective choice set is determined not only by her preferences but also by supply-side rationing or information frictions that restrict which options are actually available to her. Standard discrete choice methods assume consumers pick freely from the full product set, but this assumption fails in school and college admissions, entry-level labor markets, healthcare with selective admissions, and consumer markets with incomplete consideration sets. The paper provides a unified non-parametric identification framework for this class of models, proves necessity of the identifying instruments, proposes a computationally tractable estimator, and applies the framework to the California kidney dialysis market.

The model combines a general random utility specification — accommodating multi-dimensional unobserved heterogeneity and product-level unobservables correlated with observed characteristics as in Berry (1994) and BLP (1995) — with a reduced-form acceptance policy function that governs which products accept which consumers. The consumer’s latent choice set is the set of products that accept her, and she picks her most preferred option within that set. Crucially, the acceptance decision may be arbitrarily correlated with consumer preferences, ruling out the independence assumptions common in the consideration-set literature.

Identification rests on two sets of instruments. The first is a preference shifter, a consumer-product observable that affects utility but is excluded from the acceptance policy — distance to facility in the application. The second is a choice-set shifter, an observable that affects the acceptance decision but is excluded from consumer utility — short-term deviation of a facility’s caseload from its estimated target in the application. The main result (Theorem 1) establishes non-parametric point identification of the joint distribution of indirect utilities and acceptance decisions given both instruments. Proposition 1 establishes that the model is not identified when the choice-set shifter is absent — even when the preference shifter has full support — making both instruments necessary rather than merely sufficient.

The application uses USRDS data on 41,913 new dialysis patients treated at 552 California facilities between 2015 and 2018. Most facilities are owned by Fresenius or DaVita. The choice-set shifter is the facility’s caseload deviation from target when a patient enters the market; facility and quarter fixed effects are included so that only short-term caseload variation drives identification. A reduced-form regression shows that higher caseload deviation significantly reduces the inflow of new patients to a facility, consistent with supply-side rationing. Patients also choose more distant facilities when nearby facilities have above-normal caseloads, providing further reduced-form evidence that rationing shapes allocations.

A Gibbs sampler with data augmentation — drawing alternately from the distribution of latent choice sets conditional on utilities and from utility parameters conditional on choice sets — circumvents the curse of dimensionality that makes direct likelihood maximization over all possible choice sets infeasible.

Estimation results show that the probability a patient is accepted at her first-choice facility is only 73.0%, with variation across facilities. Standard discrete choice models that ignore rationing misestimate facility quality, systematically assigning high desirability to low-caseload facilities in a manner that conflates easy access with genuine patient preference. A naive correction that includes the caseload measure in the utility function mischaracterizes the diversion pattern: rationed patients are marginal for the facility but strictly prefer it, so they divert differently from patients who voluntarily switch because of quality changes. Fresenius and DaVita facilities are estimated to be more selective than independent facilities, consistent with chain networks enabling coordinated patient-flow management across locations.

Q: What is the core empirical problem the paper addresses? A: Standard demand estimation inverts market shares to recover preference parameters under the assumption that consumers choose freely from the full product set. When choice sets are constrained by supply-side rationing or information frictions, the largest market share product need not be the one most preferred — it may simply be the one that accepts the most consumers. This makes the standard inversion inapplicable, and ignoring constraints yields biased preference estimates.

Q: What does the paper’s model consist of? A: The model has two components: (1) a random utility model for consumer preferences with rich observed and unobserved heterogeneity, allowing product-level unobservables correlated with observed characteristics; and (2) a reduced-form acceptance policy function sigma_jt taking values in {0,1} that determines whether product j accepts consumer i. The consumer’s latent choice set is the set of products that accept her; she picks her most preferred option within it. Utilities and acceptance decisions may be arbitrarily correlated.

Q: What examples of latent choice constraints are covered by the framework? A: The reduced form encompasses: selective admissions in healthcare (facility accepts patient if profitability exceeds a caseload-dependent threshold); two-sided matching markets where a pairwise stable allocation is described by cutoff scores (school admissions, entry-level labor markets); consideration set models where brand awareness advertising or inattention determines which products a consumer sees; fixed-sample consumer search; and product stock-outs. Each of these implies an acceptance policy function of the form specified in the paper’s reduced-form model.

Q: What are the two identifying instruments and the intuition behind each? A: The preference shifter yij is a consumer-product observable that affects the consumer’s indirect utility for product j but is excluded from that product’s acceptance decision. In the application this is distance: dialysis requires multiple weekly visits, so distance affects patient utility, but a facility’s decision to accept a patient does not depend on how far the patient lives. The choice-set shifter zij is an observable that affects the acceptance decision but is excluded from consumer preferences. In the application this is the deviation of facility caseload from its estimated target: short-term caseload swings affect whether a facility can take a new patient but, conditional on facility fixed effects, do not reflect facility quality as perceived by patients.

Q: What does Theorem 1 establish and under what conditions? A: Theorem 1 establishes non-parametric point identification of (i) the function gj mapping the preference shifter to its utility contribution, and (ii) the joint distribution of indirect utilities and acceptance indicators, for every consumer attribute vector and every value in the interior of the joint support of the instruments. Conditions required include: monotonicity of the acceptance policy in the choice-set shifter (higher z makes acceptance weakly less likely, with sigma=1 as z approaches negative infinity and sigma=0 as z approaches positive infinity); conditional independence of unobservables from the instruments given observed consumer attributes; and at least two products available.

Q: What does Proposition 1 establish about necessity of the choice-set shifter? A: Proposition 1 shows that if the choice-set shifter z has singleton support (no variation), then even when the preference shifter g has full support on R^|J|, the distribution of preferences is not identified wherever a choice set strictly smaller than the full product set has positive probability. The non-identification result applies on any open set where a constrained choice set has positive probability — it is not a knife-edge case. This makes the choice-set shifter a necessary condition for identification, not merely a convenient one.

Q: How does the paper handle endogeneity of product characteristics? A: Corollary 2 extends the baseline identification result to allow product-level unobservables that may be correlated with observed product characteristics, as in Berry (1994) and BLP (1995). Identification in this case requires an additional instrument that shifts product characteristics but is excluded from both preferences and choice sets — analogous to BLP supply-side instruments — alongside the two shifters already required. This extends Berry and Haile (2010) to settings with constrained choice sets.

Q: What is the Gibbs sampler estimator and why is it needed? A: With J products per market, the number of possible choice sets is 2^J, making direct likelihood computation infeasible for even moderate J. The Gibbs sampler uses data augmentation to alternate between: (a) drawing latent choice sets conditional on current utility parameters and observed choices; and (b) drawing utility parameters conditional on the augmented choice sets. Each conditional draw reduces to a standard problem, avoiding the curse of dimensionality. The Bernstein-von Mises theorem implies that the posterior mean of the sampling chain is asymptotically equivalent to the maximum likelihood estimator.

Q: What is the reduced-form evidence for supply-side rationing in dialysis? A: The regression of log(1 + new patient inflows to facility j in quarter q) on facility fixed effects, quarter fixed effects, and the caseload deviation z_jq yields a statistically significant negative coefficient on caseload deviation: above-target caseloads reduce new patient admissions even after controlling for facility-level and time-level averages. Additionally, patients whose nearest facilities have above-normal caseloads travel to more distant facilities, providing complementary evidence that rationing displaces patients geographically.

Q: What is the estimated probability of acceptance at a first-choice facility? A: The structural estimates imply that a patient is accepted at her first-choice facility with probability only 73.0%, with variation across facilities. The implied 27.0% rejection rate is economically substantial, meaning a large share of observed allocations do not reflect unconstrained patient preference.

Q: How do estimates from the constrained model differ from a standard discrete choice model? A: The standard model, which ignores selective admissions, assigns higher utility to facilities with lower caseloads — a bias that conflates easy access with genuine patient preference. The constrained model separately identifies the facility’s acceptance propensity from the patient’s underlying preference, yielding different facility quality rankings. The largest facilities are not necessarily the most desirable once selective admissions are accounted for.

Q: Why is the naive correction — including caseload in the utility function — insufficient? A: The naive correction treats caseload as a quality attribute, implying that a patient turned away because of high caseload and a patient who voluntarily avoids a high-caseload facility are pulled from the same margin. In the constrained model, a rationed patient is marginal for the facility but strictly prefers it, so she diverts to a different set of alternatives than a patient who voluntarily switches. Not capturing this distinction produces quantitatively different diversion ratios.

Q: What do the estimates say about chain versus independent facilities? A: Fresenius and DaVita facilities are estimated to be more selective in their admissions than independent facilities. The paper interprets this as consistent with large chains having better ability to coordinate patient flows across their network of facilities, potentially directing turned-away patients to other chain locations.

Q: What is the scope of the identification results? A: Identification is established within each market, for consumer attribute vectors in the interior of support, and for utility-acceptance pairs in the interior of the joint support of the instruments. The results are non-parametric in that they do not restrict the functional form of preferences or acceptance policies beyond monotonicity and support conditions, and they allow unobservables affecting choice sets to be arbitrarily correlated with preference unobservables. The empirical application implements a parametric version for tractability.

Latent choice constraint: A restriction on a consumer’s effective choice set arising from supply-side rationing or information frictions, such that the consumer can only choose among the products that accept her rather than freely among all products in the market. Distinct from price-based market clearing.

Acceptance policy function: A reduced-form function mapping consumer attributes, consumer unobservables, and the choice-set shifter to a binary accept/reject decision by product j. Indexed by product and market, allowing arbitrary variation in selectivity across products and time. The consumer’s latent choice set is defined as the set of products whose acceptance policy equals 1.

Choice-set shifter: A consumer-product observable that shifts the acceptance probability — making product j more or less likely to accept consumer i — while being excluded from consumer indirect utility. In the application: short-term deviation of facility caseload from its estimated target. Necessary (not merely sufficient) for non-parametric identification of the model.

Preference shifter: A consumer-product observable that shifts consumer utility for product j and is separable from consumer-specific unobservables, but is excluded from that product’s acceptance policy function. In the application: distance from patient’s residence to the facility. Also necessary for identification.

Curse of dimensionality in constrained choice: The computational problem that the number of possible latent choice sets grows as 2^J with the number of products J, making direct likelihood integration over choice sets infeasible for even moderate J. Resolved in this paper by a Gibbs sampler with data augmentation that conditions alternately on latent choice sets or utility parameters.

Diversion ratio under selective admissions: The share of patients lost by a facility who are captured by each alternative facility. In a model with selective admissions, rationed patients (marginal for the facility) divert differently from patients who voluntarily switch (marginal for the consumer), because rationed patients strictly prefer the rejecting facility. The naive correction conflates these two margins, yielding quantitatively different and biased diversion ratio estimates.

Non-parametric necessity of instruments: The property that both the preference shifter and the choice-set shifter are individually necessary conditions for point identification of the joint distribution of preferences and acceptance decisions, not merely convenient sufficient conditions. Absence of either instrument leaves the model non-identified on any open set where a constrained choice set has positive probability.

Demand Stimulus as Social Policy

Mon, 01 Jan 0001 00:00:00 +0000

This paper estimates the distributional and social consequences of Department of Defense (DOD) contract spending using a city-level (CBSA) panel dataset spanning 2005–2016. The research question is whether demand stimulus — specifically DOD spending, the largest category of U.S. discretionary government spending — has differential effects across demographic groups and whether it improves social outcomes typically targeted by dedicated government programs. A secondary question is whether these effects are specific to DOD spending or common to any demand shock.

The empirical strategy exploits variation in DOD contract spending from USAspending.gov, constructing a proxy for outlays over time using contract duration, and instrumenting with a Bartik-type shock (location’s average DOD share interacted with aggregate contract spending). The main specification is a two-year differenced panel regression with CBSA and time fixed effects. Social outcomes come primarily from the American Community Survey (ACS), covering 290 CBSAs; mortality data come from the CDC; crime data from the FBI/NACJD. For comparison, the authors construct a general demand shock series using the standard Bartik shift-share approach across two-digit industries, which is nearly uncorrelated with the DOD shock (correlation -0.07).

Main findings on distributional effects: A 1 percent increase in DOD spending as a share of local earnings raises overall average ACS earnings by 0.43 percent but raises average earnings for households without a bachelor’s degree by 0.71 percent, and raises average earnings for Black households by a slightly larger amount, while Whites receive the majority of total income. The employment rate rises by 0.22 percentage points per percent increase in DOD spending. Labor force participation is largely unchanged in aggregate, but rises 0.08 percentage points for the middle-aged (41–61) and 0.14 percentage points for those with a bachelor’s degree.

On social outcomes: The poverty rate falls 0.08 percentage points, driven entirely by those without a bachelor’s degree. Food stamp (SNAP) receipt falls 0.08 percentage points. Self-reported disability rates fall, particularly among households without a bachelor’s degree. Occupational prestige rises by 0.024 points overall (0.037 for those without a bachelor’s degree). Travel time to work falls by 6.7 minutes per day, implying an annual benefit exceeding $558 per worker at a value of time of $10/hour. Marriage rates rise and divorce rates fall for some demographic groups. Homeownership increases significantly for some groups. Mortality falls, with 2.61 fewer deaths per 100,000 among those age 45–65 and 8.49 fewer deaths per 100,000 among those over 65 per percent increase in DOD spending; health-related deaths account for the majority of the decline. Crime is largely unaffected, except for a statistically significant reduction in vehicle theft.

Comparing DOD to general demand shocks: Although both raise total earnings by similar amounts ($0.56 and $0.63 per dollar of shock, respectively), the general demand shock produces only about half the employment rate response (14.3 vs. 24.5 percentage point increase for households without a bachelor’s degree), concentrates earnings gains among already-employed, higher-educated, and White households, produces weaker effects on disability and occupational prestige, increases mortality by approximately 100 deaths per 100,000, and increases crime (vehicle theft and aggravated assault). The differential mortality response is partly attributed to differential pollution effects: general demand shocks raise the median AQI substantially, while DOD shocks do not. The differential employment effects of DOD shocks are explained primarily by city and occupational composition rather than industry composition: DOD shocks are directed toward smaller, lower-earnings cities with lower employment rates and fewer college-educated residents, and toward construction, manufacturing, and production/maintenance occupations with high no-bachelor’s shares.

Scope conditions: Results are identified using CBSA-level variation over 2005–2016. DOD spending is treated as predominantly supply-side-driven and not directly entering household utility or local infrastructure. The social outcome results are local partial-equilibrium estimates and do not account for general equilibrium spillovers across CBSAs.

Q: What is the core identification strategy, and why is DOD spending considered a valid instrument for demand stimulus? A: DOD contract data from USAspending.gov are used to construct a proxy for outlays (distributing contract obligations over contract duration), and this measure is instrumented with a Bartik-type shock (location’s average DOD share times aggregate contract growth). The Bartik IV isolates the component of DOD contracts associated with new production, addressing endogeneity and the “anticipated contracts” problem. DOD spending is treated as predetermined relative to local business cycles and does not directly enter household utility or local infrastructure, isolating the aggregate demand channel.

Q: Which demographic groups receive the most total income from DOD spending, and which see the largest relative gains? A: In absolute terms, the majority of wage and salary income from DOD spending accrues to Whites and to those without a bachelor’s degree. However, adjusting for existing income shares, Black households and households without a bachelor’s degree experience the largest proportional increases in average earnings: a 1 percent increase in DOD spending as a share of local earnings raises average earnings for no-bachelor’s households by 0.71 percent, compared to a 0.43 percent increase in overall average earnings.

Q: How does DOD spending affect employment at the extensive margin, and what does this imply about who benefits? A: A 1 percent increase in DOD spending as a share of local earnings raises the overall employment rate by 0.22 percentage points. The large employment response among those without a bachelor’s degree (24.5 percentage points in the comparative analysis) implies that DOD spending disproportionately benefits previously unemployed workers rather than simply raising wages for those already employed.

Q: Does DOD spending increase labor force participation? A: There is no detectable aggregate effect on labor force participation rates, suggesting limited effects of demand stimulus on the participation margin over short horizons. However, participation rises 0.08 percentage points for the middle-aged (41–61) and 0.14 percentage points for those with a bachelor’s degree. The population response is strongest for those without a bachelor’s degree, though the estimate is imprecise.

Q: What are the poverty and welfare effects of DOD spending? A: A 1 percent increase in DOD spending as a share of local earnings reduces the poverty rate by 0.08 percentage points, with the entire effect concentrated among households without a bachelor’s degree. SNAP (food stamp) receipt falls by 0.08 percentage points. Medicaid receipt falls significantly for young children, while children substitute into private health insurance, leaving overall child health insurance coverage unchanged.

Q: How does DOD spending affect disability rates? A: A 1 percent increase in DOD spending leads to a 0.001 percentage point reduction in self-reported disability rates among households without a bachelor’s degree. The effect is most apparent for this group, the middle-aged, and Whites. In the comparative analysis, the employment margin accounts for a disability decline of -0.051 for no-bachelor’s households, nearly half of the total disability decline of -0.114 for that group.

Q: What are the occupational prestige and commute time effects? A: A 1 percent increase in DOD spending raises a city’s average occupational prestige score (Siegel score) by 0.024 points, with the effect concentrated among no-bachelor’s households (0.037). Commute time falls by 6.7 minutes per day; at a value of time of $10/hour, this implies an annual benefit of approximately $558 per worker.

Q: How does DOD spending affect household formation outcomes? A: Marriage rates increase and the likelihood of single parenthood decreases for White households. Divorce rates decrease for middle-aged and Black households. White households become more likely to own homes and less likely to live in multi-family homes. Estimates for Black and Hispanic households are imprecise.

Q: What are the mortality effects of DOD spending, and how do they compare to general demand shocks? A: A 1 percent increase in DOD spending as a share of local income leads to 2.61 fewer deaths per 100,000 among those aged 45–65 and 8.49 fewer deaths per 100,000 among those over 65, with health-related deaths accounting for the majority of the decline. This implies the DOD must spend approximately $25 million to save a life aged 45–65, exceeding the typical value of a statistical life. By contrast, a general demand shock increases mortality by approximately 100 deaths per 100,000, consistent with Ruhm’s (2000) finding that mortality is procyclical; mortality increases from general shocks are also concentrated among those over 45.

Q: What explains the divergent mortality effects of DOD and general demand shocks? A: One mechanism explored is pollution: general demand shocks raise median AQI substantially while DOD shocks leave AQI largely unaffected, consistent with Ruhm’s (2000) emphasis on deteriorating health behaviors during expansions. The paper also points to differential occupational and geographic composition: DOD shocks flow to construction, manufacturing, and production/maintenance occupations rather than to higher-pollution or higher-accident-risk activities common in broad economic expansions.

Q: How do the crime effects differ between DOD and general demand shocks? A: DOD spending shocks are associated with a statistically significant reduction in vehicle theft but no significant change in other crime categories. General demand shocks, by contrast, appear to increase vehicle theft and aggravated assault. Voter turnout falls substantially in response to a general demand shock; both shock types reduce Democratic vote shares.

Q: What is the key mechanism explaining why DOD shocks have stronger social effects than general demand shocks? A: Despite similar average earnings effects for no-bachelor’s households (0.71 for DOD vs. 0.69 for general shocks), DOD shocks produce a much larger employment rate increase for that group (24.5 vs. 14.3 percentage points). The authors show that this employment margin accounts for large shares of the differential declines in poverty, food stamp receipt, disability, and improvements in marriage rates and occupational prestige.

Q: What accounts for the differential employment effects on no-bachelor’s households between DOD and general demand shocks? A: Of the 0.21 percentage point differential employment effect, roughly one quarter is associated with differences in the no-bachelor’s share across industries. Differences across cities and across occupations each account for much larger shares. DOD shocks are directed toward smaller, lower-income, lower-employment cities with fewer college-educated residents, while general demand shocks go to larger, richer cities with more elastic housing supply and higher education levels.

Q: Which industries and occupations drive DOD’s stronger employment effects for no-bachelor’s workers? A: Within industries, DOD-induced employment gains for no-bachelor’s workers are strongest in construction and manufacturing, with much milder effects from general demand shocks in these industries. The occupations benefiting most are military occupations (broadly defined) and Production and Maintenance occupations, which rank among the lowest in occupational prestige for no-bachelor’s workers.

Q: How does DOD spending compare to targeted social programs in achieving distributional goals? A: The paper argues that although DOD spending is not designed as social policy, its effects on earnings for households without a bachelor’s degree, poverty reduction, disability reduction, homeownership, and occupational upgrading mirror the stated objectives of many targeted programs (job training, housing subsidies, SNAP, Medicaid). At the same time, DOD-induced life savings cost approximately $25–45 million per life, exceeding the typical value of a statistical life, so the mortality benefits cannot alone justify the spending.

Local DOD earnings multiplier: The dollar amount of earnings for a demographic group produced by a dollar of local DOD spending over a two-year period, estimated using a two-year differenced panel regression with CBSA and time fixed effects, instrumented by a Bartik-type shock.

Bartik-type IV shock: An instrumental variable constructed as the product of a location’s average share of DOD contract spending and aggregate contract spending in a given period; used to isolate the component of DOD contracts associated with new production rather than anticipated or smoothed payments.

General demand shock: A Bartik shift-share shock constructed from local industry employment shares and national industry-level growth rates across all private-sector industries, used as a comparison series to evaluate whether DOD spending effects are generic or specific to defense contracts (correlation with DOD shock: -0.07).

Extensive margin of employment: The change in the employment rate (entry from unemployment or non-participation into employment) as distinct from hours or wage adjustments among the already-employed; identified in the paper as the primary mechanism linking DOD shocks to differential social outcomes for no-bachelor’s households.

Deaths of despair: Drug-and-alcohol-related deaths and deaths by suicide, following Case and Deaton (2020); examined here at higher frequency as an outcome of labor market earnings changes induced by aggregate demand stimulus.

Occupational prestige (Siegel prestige score): A summary measure of job quality based on survey-derived perceptions of occupational standing (Siegel 1971), aggregated to the CBSA level by demographic group; used as a measure of upward job-ladder mobility in response to demand stimulus.

Source text origin: A classification of the text basis for a paper summary — full PDF or OA-HTML versus abstract-only; the pipeline hard-blocks summaries derived solely from abstract text.

Destabilizing Capital Flows amid Global Inflation

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

Bengui and Coulibaly ask whether the pattern of capital flows observed during the 2021–2023 global monetary tightening cycle — whereby capital flowed from low-inflation to high-inflation countries — was a stabilizing or destabilizing force for the global economy’s adjustment to cost-push shocks. Among the G7 and a broader sample of 26 jurisdictions, those with higher average CPI inflation (October 2021–March 2023) and larger cumulative interest rate hikes ran more negative current account balances over the same period, with the slope of the cross-sectional relationship between cumulative hikes and the current account equal to −1.29 (significant at 1%) and the slope between average inflation and the current account equal to −0.99 (significant at 1%), and over 75% of the top two quartile hikers running deficits while over 75% of the bottom two quartiles ran surpluses.

Model and Methodology

The authors build a standard continuous-time two-country general equilibrium model with nominal rigidities (Calvo price-setting), internationally traded bonds, and cost-push shocks modeled as wage markup shocks that create an output-inflation trade-off. The baseline model features no home bias (equal weights on domestic and foreign goods) and two tradable goods. Extensions introduce (i) consumption home bias (parameter α ∈ [0, 1/2]) and (ii) non-tradable goods. Policy is analyzed under two regimes: (a) free capital mobility (no taxes on financial transactions) with optimal cooperative monetary policy, and (b) a managed capital flow regime in which a planner jointly optimizes both monetary policy and a tax wedge on the international bond (τ^D_t). A second-order approximation of household utility yields a loss function penalizing world and cross-country output gaps, PPI inflation differentials, and the demand imbalance term θ_t. The quantitative section replaces optimal monetary policy with standard Taylor rules (φ_π = 1.5, φ_y = 0.25) and calibrates a Home cost-push shock to generate a peak CPI inflation rate of about 7%, with an annual autocorrelation of 0.65.

Main Findings

The paper’s central theoretical result (Proposition 2, “Topsy-Turvy Capital Flows”) is that, under the Marshall-Lerner condition (trade elasticity η > 1), a free capital mobility regime channels capital into the country with the most acute inflationary pressures — the very country whose central bank is most aggressively tightening — while the constrained-efficient managed regime would channel capital in the opposite direction. The mechanism operates through the supply side: capital inflows raise domestic households’ wealth, reducing their labor supply and thereby raising real wages and firms’ marginal costs. In the presence of non-tradable goods, an additional channel operates through the real exchange rate — capital inflows appreciate the domestic real exchange rate and inflate tradable-sector firms’ marginal costs independently of labor supply. Both channels worsen the central bank’s output-inflation trade-off.

In the quantitative exercise (Taylor rule setting, home bias α = 0.25, trade elasticity χ = 3), following the calibrated inflationary cost-push shock in Home:

Under free capital mobility: Home inflation rises to 8% on impact; Home output gap reaches −8.4%; Foreign output gap reaches +2.4%; Home runs a trade deficit of 2.5% of GDP on impact; Home’s initial policy rate hike is nearly 10% while Foreign’s is less than 1%.
Under the managed capital flow regime (capital flows reversed to outflows from Home): Home inflation on impact falls to nearly 6% (a reduction of approximately 2 percentage points); Home output gap is −6.8% (improvement of about 1.5 percentage points); Foreign output gap is 0.8% (improvement of about 1.5 percentage points); Home runs a trade surplus of 0.6% of GDP; Home’s initial hike falls to approximately 8% (roughly 2 percentage points lower) while Foreign’s rises to approximately 2.5% (roughly 1.5 percentage points higher).
The managed regime delivers average welfare gains of 0.78% of current consumption (0.03% of permanent consumption). Welfare gains are increasing in the trade elasticity η: at η = 10 (consistent with Yi 2003’s bilateral trade flow estimates), gains reach approximately 0.08% of permanent consumption or 1.9% of current consumption.

Scope Conditions

The topsy-turvy result (free mobility channels capital in the wrong direction) holds conditional on the Marshall-Lerner condition (η > 1 in the baseline; equivalently, the trade elasticity χ > 1). With consumption home bias, the condition weakens to: the trade elasticity exceeds the degree of home bias (χ > 1 − 2α, which is weaker than Marshall-Lerner). When home bias is strong relative to the trade elasticity, a purchasing power effect may dominate the wealth effect, and free capital mobility may instead deliver too little capital flow toward the depressed country — the opposite inefficiency. The welfare analysis throughout assumes symmetric initial net foreign asset positions. The key insight is specific to environments in which monetary policy faces an output-inflation trade-off from cost-push shocks; it is directionally opposite to the aggregate demand externality prescription that arises in demand-shortage environments (e.g., currency unions with productivity shocks), where optimal policy instead calls for capital to flow toward the more depressed country.

In depth

Q1. What is the empirical motivation for the paper, and how is the stylized fact documented?

A1: During October 2021–March 2023, jurisdictions with higher average CPI inflation and larger cumulative policy rate hikes ran more negative current account balances. The cross-sectional slope between average inflation and the current account-to-GDP ratio is −0.99 (R² = 0.22, significant at 1%), while the slope between cumulative hikes and the current account is −1.29 (R² = 0.27, significant at 1%). Among the top two quartiles of cumulative hikers, over 75% of jurisdictions ran current account deficits, while among the bottom two quartiles over 75% ran surpluses. Data come from the BIS (inflation and policy rates) and the OECD Main Economic Indicators (quarterly current accounts), covering 26 jurisdictions excluding Argentina, Russia, and Turkey.

Q2. What is the core externality the paper identifies, and why do atomistic agents fail to internalize it?

A2: When a household in the high-inflation country borrows from abroad for consumption smoothing (as the domestic central bank tightens), it raises domestic consumption and thereby reduces labor supply through a wealth effect, pushing up real wages and firms’ marginal costs. The central bank must then tighten further to achieve the same inflation stabilization, or accept a worse inflation outcome. Because this effect operates through economy-wide wages and prices (general equilibrium), atomistic households do not internalize it when making individual borrowing decisions. The paper shows formally that a marginal increase in Home borrowing dθ_t raises welfare losses by an amount proportional to the product of the Phillips curve slope κ, the co-state variable φ^D_t (equal to the cross-country output gap differential y^D_t under optimal monetary policy), and the direct effect on cross-country marginal cost differences (1/2). When output is more depressed in Home (y^D_t < 0), additional borrowing by Home tightens the constraint and lowers welfare.

Q3. What does the optimal capital flow management targeting rule say, and what is its economic interpretation?

A3: Proposition 1 states that under jointly optimal monetary and capital flow management, the demand imbalance (relative consumption) should satisfy θ_t = 2y^D_t. This means the planner generates a demand imbalance in favor of the less depressed country, reallocating spending away from the country with the most acute inflationary pressure. This is counterintuitive from a pure output stabilization view: policy deliberately shifts demand away from the country with the most depressed output. The logic is that reducing the domestic wealth of the high-inflation country lowers real wages, reduces firms’ marginal costs, and thereby relaxes the output-inflation trade-off for that country’s central bank.

Q4. What is the “topsy-turvy” capital flows result (Proposition 2), and under what condition does it hold?

A4: Under free capital mobility, standard neoclassical consumption-smoothing motives lead capital to flow into the country with the most depressed output (the high-inflation country): the trade deficit equals [(η−1)/η]·y^D_t. Under managed capital flows, the optimal regime instead mandates a trade surplus for the most depressed country: the trade balance equals −(1/η)·y^D_t. Comparing signs, the direction of capital flows is literally reversed — hence “topsy-turvy.” The result holds whenever Assumption 1 (η > 1, the Marshall-Lerner condition in the baseline model) is satisfied, which the authors argue has compelling empirical support (trade elasticities estimated at 7–17 in the literature).

Q5. How does the presence of home bias in consumption affect the externality and the topsy-turvy result?

A5: With home bias (α < 1/2), capital inflows also appreciate the terms of trade, which lowers the relative price of imports in terms of domestic goods and reduces marginal costs for domestic tradable firms — a “purchasing power effect” that partially offsets the wealth effect. The optimal capital flow targeting rule becomes θ_t = [1 − (1−2α)/(2(1−α)η)]·2y^D_t. Under the condition that the trade elasticity exceeds the degree of home bias (χ > 1 − 2α, strictly weaker than Marshall-Lerner), the wealth effect dominates the purchasing power effect and the topsy-turvy result is preserved. Below a knife-edge curve in the (α, η) parameter space, the purchasing power effect dominates and free capital mobility results in too little rather than too much capital flowing toward the high-inflation country.

Q6. Does the externality always imply excessive capital flow volatility?

A6: No — this is a novel contribution relative to the prior literature. In the limiting case of a unit intratemporal elasticity (η → 1, the Cole-Obstfeld case), trade is balanced at all times under free capital mobility. Under managed capital flows, however, capital should flow from the most depressed to the least depressed country. This means the externality can result in too little rather than too much capital flow. The standard normative literature (e.g., Bianchi 2011) has focused on excessive capital flow volatility; the supply-side channel identified here shows that market failures can sometimes lead to insufficient external imbalances.

Q7. How does the paper’s mechanism differ from aggregate demand externalities as in Farhi and Werning (2016)?

A7: Farhi and Werning (2016) study demand-shortage environments (fixed exchange rates or zero lower bound) where constraints on monetary policy mean output is demand-constrained. Their prescription is to channel capital toward the most depressed country to stimulate demand for undersupplied goods. In Bengui and Coulibaly, monetary policy is unconstrained but faces an output-inflation trade-off from cost-push shocks. Here, the depressed output reflects the central bank’s deliberate demand contraction to fight inflation, not an inability to stimulate. The optimal response is therefore to shift spending away from the high-inflation (most depressed) country to reduce supply pressure — the opposite direction. Formally, in the demand-shortage case with unit elasticity and home bias, the optimal trade balance targeting rule is nxt = [(1−2α)/(4(1−α))]·ỹ^D_t (trade deficit for most depressed country), while in the supply pressure case it is nxt = −[α/(1−α)]·y^D_t (trade surplus for most depressed country).

Q8. What does the non-tradable goods extension add to the baseline mechanism?

A8: The baseline model (two tradable goods, no home bias) transmits the externality only through the wealth effect on labor supply: capital inflows raise consumption, reduce labor supply, and raise real wages and marginal costs. In the non-tradable goods extension, a second channel operates through the real exchange rate. Capital inflows raise demand for non-tradable goods, appreciating the domestic real exchange rate and inflating the price of the consumption basket relative to domestically produced tradable goods. This raises marginal costs for tradable-sector firms independently of any labor supply response, and is therefore unaffected by whether preferences exhibit a wealth effect on labor supply. The paper shows that the optimal policy problem in this extension is isomorphic to the baseline: the loss decomposition (equation 42) yields two additive terms proportional to the share of tradable goods (wealth effect on labor supply) and the share of non-tradable goods (wealth effect on demand for non-tradables), respectively.

Q9. What does the quantitative exercise show about cross-country policy rate dispersion?

A9: Under free capital mobility with Taylor rules, the initial policy rate hike in Home following the calibrated shock is nearly 10%, while in Foreign it is less than 1% — a cross-country dispersion of roughly 9 percentage points. Under managed capital flows, Home’s initial hike falls to approximately 8% and Foreign’s rises to approximately 2.5% — a dispersion of roughly 5.5 percentage points. The authors interpret this as evidence that free capital mobility leads high-inflation countries to tighten excessively and low-inflation countries to tighten too little, generating an inefficiently large cross-country dispersion in monetary policy.

Q10. How does the welfare gain from managed capital flows vary with the trade elasticity?

A10: Welfare gains are increasing in the elasticity of substitution between domestic and foreign goods (η). At the baseline calibration of η = 2 (trade elasticity χ = 3, near the lower bound of empirical estimates), the gain is 0.78% of current consumption (0.03% of permanent consumption). At η = 10 (consistent with Yi 2003’s estimate needed to match bilateral trade flows), the gain rises to approximately 1.9% of current consumption (0.08% of permanent consumption). The welfare gain is defined as the percentage increase in permanent consumption required by a household under free capital mobility to be as well off as under managed capital flows.

Q11. What is the role of Lemma 1 (irrelevance of capital flow regime for world variables)?

A11: Lemma 1 shows that under optimal cooperative monetary policy, the paths of world output gap and world inflation are independent of the capital flow regime (i.e., independent of the path of θ_t). This follows because the “world” block of the model can be solved independently of the “difference” block and the demand imbalance. As a result, the entire normative analysis of capital flows reduces to the behavior of cross-country difference variables (y^D_t, π^D_t, and θ_t), greatly simplifying the analysis. It also implies that switching capital flow regimes does not affect the global total of output or inflation, only its distribution across countries.

Q12. What extensions do the authors suggest would enrich the analysis without invalidating the main insight?

A12: Three extensions are noted. First, additional monetary policy constraints — discretionary (non-commitment) policy, non-cooperative policy setting, or a currency union — would introduce extra stabilization constraints and generate additional terms in the capital flow management targeting rule but would not overturn the supply-side channel. Second, alternative goods pricing specifications (local currency pricing, deviations from the law of one price) would make additional variables like cross-country consumer price differentials relevant measures of policy tightness, again adding terms to the rule. Third, the insight is argued to apply more generally in heterogeneous-agent or multi-sector closed-economy models with nominal rigidities whenever private financial decisions affect the economy’s supply side through general equilibrium price effects.

Key Concepts

Cost-push shock (wage markup shock): In the paper’s model, a cost-push shock is a positive deviation of the wage markup (µ^w_t) from its steady-state value. It shifts the New Keynesian Phillips curve, creating an output-inflation trade-off: the central bank must accept either higher inflation or a larger negative output gap. It is not a demand shock; its policy implications are directionally opposite to demand shortage shocks.

Demand imbalance (θ_t): The log ratio of Home to Foreign consumption, defined as c_t − c^*_t = θ_t in the linearized model. Under free capital mobility and symmetric initial wealth, θ_t = 0 (consumption shares are equalized). Under managed capital flows, θ_t is the instrument of capital flow policy: setting θ_t > 0 shifts spending toward Home; θ_t < 0 shifts it toward Foreign. The loss function penalizes deviations of θ_t from zero as an independent inefficiency (cross-country consumption misallocation).

Topsy-turvy capital flows: The paper’s central finding that, following a cost-push shock, the direction of capital flows prescribed by constrained-efficient policy is opposite to the direction that free capital mobility generates. Under free mobility, capital flows into the high-inflation country (trade deficit there); under managed flows, capital should flow out of the high-inflation country (trade surplus there). The term is used to describe the directional reversal, not merely excessive magnitude.

Macroeconomic externality (supply-side): The failure of atomistic agents to internalize the general equilibrium effect of their borrowing decisions on domestic firms’ marginal costs (via real wages or the real exchange rate). This is the paper’s label for the source of inefficiency. It is classified as a supply-side externality to distinguish it from aggregate demand externalities (Farhi and Werning 2016), where the operative mechanism runs through demand for specific goods rather than through factor costs.

Trade elasticity (χ): In the baseline model, χ = η (elasticity of substitution between domestic and foreign tradable goods). With home bias, χ = 2(1−α)η. The trade elasticity plays the key role in determining whether the topsy-turvy result holds: the result requires χ > 1 (Marshall-Lerner in baseline) or, with home bias, χ > 1 − 2α (weaker condition). At χ = 1 (Cole-Obstfeld case), trade is balanced under free mobility, and managed flows call for capital to move from the most to the least depressed country — implying insufficient rather than excessive capital flows under free mobility.

Purchasing power effect: In the model with home bias, a capital inflow appreciates the terms of trade (the relative price of exports over imports), which raises the purchasing power of domestic firms and lowers their marginal costs. This effect partially offsets the wealth-effect-driven rise in marginal costs. Its strength is proportional to the degree of home bias (1−2α) relative to the trade elasticity 2(1−α)η. Under the paper’s weaker-than-Marshall-Lerner condition, the wealth effect dominates the purchasing power effect.

Managed capital flow regime: A policy regime in which the government imposes taxes on international financial transactions (τ_t for Home, τ^_t for Foreign) to control the demand imbalance θ_t, subject to the targeting rule θ_t = 2y^D_t (or its home-bias-adjusted counterpart). This regime accounts for the macroeconomic externality and delivers a constrained-efficient allocation given the presence of nominal rigidities. The tax wedge τ^D_t = (τ_t − τ^_t)/2 represents the gap in returns on the international bond faced by Home versus Foreign households.

World and difference formulation: Following Engel (2011) and Groll and Monacelli (2020), the model is decomposed into “world” variables (averages: y^W_t, π^W_t) and “difference” variables (cross-country gaps: y^D_t, π^D_t). The targeting rules and Phillips curves separate additively into world and difference blocks, and Lemma 1 establishes that the capital flow regime affects only the difference block. This decomposition is the analytical device that isolates the role of capital flows.

Devaluations, Deposit Dollarization, and Household Heterogeneity

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

Ferrante and Gornemann study the aggregate and redistributive effects of currency devaluations in emerging market economies, focusing on a feature that prior open-economy HANK models had not jointly incorporated: households hold dollar-denominated deposits that are disproportionately concentrated among wealthier agents, and these deposits sit on the liability side of leveraged, agency-constrained banks. The paper asks how this combination of deposit dollarization and household wealth heterogeneity shapes the macroeconomic and distributional consequences of a currency depreciation, and what it implies for the optimal degree of exchange-rate smoothing by the central bank.

Data and Empirical Motivation

The model is calibrated to match cross-sectional micro-data from the 2013 Uruguayan Household Financial Survey, which records the currency denomination of household assets and liabilities. As documented by Drenik et al. [2018] and confirmed by the authors for Uruguay, the top quintile of the wealth distribution holds close to 70% of liquid savings in dollars, while households with zero or negative net wealth have essentially no direct foreign-currency exposure. The baseline calibration targets a deposit dollarization rate of 40% of aggregate bank deposits, in line with the cross-country average reported for Latin America. The spread between bank lending and deposit rates is calibrated at 8% annualized for household loans (consistent with Uruguayan bank data over the prior 15 years) and 2% for capital returns, implying a bank leverage ratio of approximately 6.

Model

The framework is a small open economy New Keynesian model with two non-standard elements layered on a Bewley-Huggett-Aiyagari incomplete-markets household sector. First, households face idiosyncratic labor productivity risk and a borrowing constraint, generating a non-degenerate wealth distribution in which, at the calibrated steady state, approximately 8% of households are constrained borrowers, 22% are unconstrained borrowers, 27% hold zero liquid wealth and behave hand-to-mouth (HtM), 52% are net savers, and 1% are capitalists. Second, financial intermediaries face a Gertler-Karadi [2011] agency problem that generates an endogenous, time-varying spread between lending and deposit rates. Households can save in local- or foreign-currency bank deposits and in foreign bonds, but can only borrow through domestic banks. The currency composition of household portfolios, which is a linear function of household wealth in the baseline, maps through market clearing into the banks’ currency mismatch, so that a wealthier-household preference for dollar deposits directly determines the bank’s foreign-currency liability share.

Main Findings with Quantitative Magnitudes

The paper’s central experiment is a 100 basis-point annualized increase in the foreign interest rate with persistence 0.85, which induces a currency depreciation.

Aggregate amplification: Combining a HANK household sector with leverage-constrained banks exposed to currency mismatch causes aggregate consumption to drop approximately twice as much as in a representative-agent New Keynesian (RANK) model with constrained banks, and output to decline more than 1% — roughly 30% larger than the 0.75% decline in the RANK model with financial frictions. In contrast, absent banking frictions, a bank-less HANK model would generate an output expansion because the standard expenditure switching channel dominates.
Channels: The paper decomposes the consumption decline into (a) a labor income channel — lower hours and wages caused by the financial accelerator contraction account for approximately two-thirds of the aggregate consumption decline — and (b) a borrowing rate channel — the endogenous rise in household lending spreads accounts for approximately one-third. In a counterfactual model in which the spread on household loans is held fixed, the decline in consumption and output is approximately 50% smaller than in the baseline, confirming that the borrowing rate channel and its general-equilibrium feedback onto wages and asset prices are responsible for more than half of the baseline output decline.
Distributional effects: Within the baseline model, unconstrained borrowers see their consumption fall on average by more than 3.5% on impact; constrained borrowers’ consumption falls by more than 5% in the second period as interest payments jump. Zero-wealth HtM agents cut consumption roughly one-for-one with the more-than-2% decline in real labor income. Wealthier savers and capitalists are partially insulated through their dollar holdings, which gain real value during the depreciation.
Portfolio composition and deposit dollarization: When the deposit dollarization rate is raised from the baseline 40% to 80% (to match high-dollarization countries such as Uruguay at the extreme), investment declines approximately 12% (versus 6% in the baseline) and aggregate consumption falls approximately 1.7% (versus 1% in the baseline), with the output decline more than twice as large as in the baseline. Wealthier households’ consumption path is actually higher in the high-dollarization calibration because of larger windfall gains on their dollar portfolios, while poorer households bear the amplified downturn through stronger labor income and borrowing rate channels. This produces a novel distributional result: stronger currency hedging by richer households deepens the aggregate recession and worsens outcomes for poorer agents.
Monetary policy: In the baseline 40% dollarization calibration, reacting to exchange rate changes by raising domestic interest rates is welfare-detrimental for most households: the gain from partially stabilizing banks’ balance sheets is more than offset by the contractionary effect of higher rates on aggregate demand and spreads. A modest response (κ_e ≈ 0.04 in the ex-ante welfare experiment) is preferred, conditional on aggregate dynamics. When dollarization is 80%, a small degree of exchange rate leaning (κ_e = 0.5) can improve welfare for most agents, as the benefit from protecting banks’ balance sheets becomes larger relative to the cost of tighter monetary conditions.

In depth

Q1. What three stylized facts about liability dollarization motivate the model, and how does the model’s structure capture each?

A1: The three facts are: (i) banks and firms borrow in foreign currency; (ii) foreign-currency bank debt is matched by dollar-denominated deposits from domestic households; (iii) those deposits are held predominantly by wealthier households. The model captures (i) and (ii) by having the bank hold a currency mismatch on its balance sheet — local-currency loans on the asset side, foreign-currency deposits on the liability side. Fact (iii) is captured by assuming a linear portfolio rule in which household dollar deposit share is an increasing function of wealth, calibrated to the slope observed in Uruguayan micro-data, with borrowers restricted to local-currency debt.

Q2. Why does a bank-less HANK open-economy model produce an output expansion rather than a contraction following a foreign interest rate shock in the calibration used?

A2: Without banking frictions, the expenditure switching channel dominates. A rise in the foreign interest rate depreciates the real exchange rate by roughly 1%, making domestic goods cheaper and raising exports by approximately 2%. In the bank-less HANK, this export boost causes hours and real labor income to increase, and high-MPC households (HtM and constrained borrowers) raise consumption. There is no financial accelerator operating through the bank’s balance sheet to offset this stimulus, so output expands rather than contracts.

Q3. Through what exact mechanism does bank currency mismatch transform an exchange rate depreciation into a financial accelerator event?

A3: A weaker domestic currency raises the real cost of repaying foreign-currency deposits (R_Dt jumps on impact), directly eroding bank net worth (N_t). As net worth falls and leverage rises, the bank’s incentive constraint tightens, requiring spreads on both capital loans and household loans to increase jointly (per equation 21, the ratio of spreads moves one-for-one with the ratio of diversion parameters). Lower asset prices further reduce the return on capital, feeding back into net worth in the standard Gertler-Karadi financial accelerator loop. In the RANK with banks benchmark, investment declines approximately 6% compared to only 1% in the frictionless RANK.

Q4. What is the borrowing rate channel, and how is it distinct from the balance-sheet exposure channel studied in De Ferra et al. [2020]?

A4: The borrowing rate channel operates through the endogenous widening of bank lending spreads following a net worth erosion: when banks’ leverage constraint binds more tightly, both the spread on firm capital and the spread on household loans rise simultaneously (equation 21). This forces even households who borrow only in local currency — and thus have no direct exchange-rate exposure on their liabilities — to face sharply higher borrowing costs, causing their consumption to fall steeply. De Ferra et al. [2020] study a different channel in which households borrow in foreign currency and suffer a direct balance-sheet loss from depreciation; the borrowing rate channel in this paper is distinct because it operates through financial intermediary frictions rather than through direct currency exposure of household debt.

Q5. How much of the aggregate consumption decline is attributable to the borrowing rate channel versus the labor income channel, and how do the authors establish these shares?

A5: The decomposition exercise (Figure 6) simulates each household’s response to a single price path at a time while holding all other prices at steady state. The labor income channel — the decline in real wages and hours caused by the contraction in output — accounts for approximately two-thirds of the aggregate consumption decline. The borrowing rate channel accounts for approximately one-third. Separately, a counterfactual model in which the household loan spread is held fixed produces consumption and output declines roughly 50% smaller than the baseline, showing that the borrowing rate channel and its second-round effects on wages and asset prices together account for more than half of the output decline in general equilibrium.

Q6. How does the distribution of dollar deposits across the wealth distribution affect the severity of the downturn, and what is the novel redistribution result?

A6: Through market clearing for local-currency deposits (equation 44), a larger household demand for dollar deposits directly raises the bank’s foreign-currency liability share (x^D_bt), magnifying the bank’s currency mismatch. Raising the deposit dollarization rate from 40% to 80% causes bank net worth to decline twice as much as in the baseline, investment to fall roughly 12% versus 6%, and aggregate consumption to fall roughly 1.7% versus 1%, with output declining more than twice as much. The novel distributional result is that wealthier savers and capitalists are actually better off in the high-dollarization scenario because their windfall dollar gains are larger, while poorer households suffer a more severe recession through the labor income and borrowing rate channels. Hence, stronger currency hedging by the rich deepens the aggregate recession and worsens distributional outcomes for the poor.

Q7. What happens when borrowers are assumed to hold foreign-currency debt rather than local-currency debt, as in De Ferra et al. [2020]?

A7: In this alternative calibration, borrowers face a direct balance-sheet loss from depreciation, causing constrained borrowers’ consumption to drop more steeply on impact. However, since household loans represent only approximately 5% of annual GDP in the baseline, the boost to bank net worth from having dollar-denominated loan assets is modest compared to the reduction in the dollar deposit liability. As a result, the path for investment is very similar to the baseline, while on impact consumption drops about 20% more and output declines about 10% more than in the baseline model.

Q8. What welfare implications arise from removing dollar deposits entirely from savers’ portfolios?

A8: In a calibration where households hold only local-currency assets (with banks’ currency mismatch maintained through external dollar borrowing), savers lose their windfall dollar gains during depreciation. The consumption of savers drops about 25% more than in the baseline on impact, and capitalists experience even larger changes. Because of general equilibrium feedback through wages and prices, poorer households also cut consumption more, causing aggregate consumption to fall approximately 20% more than in the baseline and output to decline approximately 5% more on impact.

Q9. Under what dollarization conditions does exchange rate stabilization through monetary tightening improve welfare, and why?

A9: Under the baseline 40% dollarization, raising domestic interest rates in response to depreciation is welfare-detrimental for most households because higher rates depress asset prices, tighten the bank’s leverage constraint, worsen the borrowing rate channel and the labor income channel for low-net-worth agents, more than offsetting the benefit from partially stabilizing the bank’s balance sheet. Only a very modest response (κ_e ≈ 0.04) is preferred. When deposit dollarization is 80%, the benefit from protecting the bank’s balance sheet is proportionally larger; a moderate reaction (κ_e = 0.5) can improve welfare for most households, though further tightening (κ_e = 5) causes bank net worth to fall more than 20% and leads to a deeper recession, reversing the gains.

Q10. How does the quarterly average MPC in the model compare to external estimates, and why is the MPC distribution central to the paper’s mechanism?

A10: The quarterly average MPC in steady state is approximately 27%, which implies an annual MPC of approximately 71%, consistent with Hong [2020b]’s estimates for Peru. The MPC distribution is central because the amplification mechanisms — both the borrowing rate channel and the labor income channel — work by hitting high-MPC agents (HtM households and constrained borrowers) hardest. Without a sufficiently high mass of high-MPC agents, changes in spreads and labor income would have muted aggregate consumption effects. The presence of approximately 27% of households with zero liquid wealth at the borrowing spread is itself endogenously generated by the bank’s agency problem, which creates a wedge between saving and borrowing rates.

Q11. How does the HANK model without banks compare to the RANK model without banks in transmitting the foreign interest rate shock?

A11: Both HANK-without-banks and RANK-without-banks generate output expansions through the expenditure switching channel. However, in the bank-less HANK, aggregate consumption declines only half as much as in the frictionless RANK because high-MPC households amplify the positive real income effect from rising labor income. Some household groups (HtM agents and constrained borrowers) actually increase consumption on impact due to higher real labor income, the Fisher channel reducing the real value of domestic-currency debt, and portfolio gains for savers holding dollar assets.

Q12. What role does the monetary policy Taylor rule play during the baseline devaluation, and how does it interact with the financial accelerator?

A12: The standard Taylor rule (coefficient 1.5 on domestic inflation) causes the central bank to raise rates in response to the CPI inflation spike accompanying the depreciation. Higher domestic rates compress the real exchange rate depreciation and reduce the boost to exports, but also directly increase banks’ funding costs, contributing to the financial accelerator by compressing the return on capital. This interaction means that the baseline monetary policy passively amplifies the banking-sector contraction relative to a model with no monetary response.

Key Concepts

Deposit dollarization: The share of domestic bank deposits denominated in foreign currency, held by domestic households. In the paper’s calibration this is set at 40% of aggregate bank deposits (baseline) or 80% (high-dollarization alternative), reflecting the empirical range across Latin American countries. It determines the bank’s foreign-currency liability share and thus the severity of currency mismatch.

Currency mismatch (banks): The gap between the currency denomination of a bank’s assets (local-currency loans to households and firms) and its liabilities (foreign-currency deposits from households). In the model, when the domestic currency depreciates the real cost of dollar deposits rises, directly eroding bank net worth without any offsetting appreciation of loan assets.

Borrowing rate channel: The mechanism by which a decline in bank net worth, caused by currency mismatch losses, tightens the bank’s incentive constraint and forces up the spread on household loans. This raises borrowing costs for households who have no direct foreign-currency exposure on their balance sheets, causing high-MPC borrowers to cut consumption sharply and thereby depressing aggregate demand and wages. This channel is distinct from the direct balance-sheet channel studied in De Ferra et al. [2020].

Labor income channel (in an open economy with banking frictions): The mechanism by which the financial accelerator — reduced credit supply and lower capital demand following bank net worth erosion — depresses output, hours, and wages, causing a decline in real labor income that hits high-MPC workers regardless of their asset-portfolio currency composition. Accounts for approximately two-thirds of the aggregate consumption decline in the baseline experiment.

Hand-to-mouth (HtM) agents: In this paper’s setting, HtM behavior is not a permanent household state but arises endogenously for households who hold zero liquid wealth because the bank’s endogenous lending spread makes both saving and borrowing suboptimal for them in a given period. Their consumption moves approximately one-for-one with current labor income, making them a key amplifier of real income fluctuations.

Financial accelerator (with currency mismatch): The Gertler-Karadi [2011] mechanism as augmented by exchange-rate exposure: a currency depreciation erodes bank net worth through the dollar deposit liability, tightening the leverage constraint, raising spreads on capital and household loans simultaneously, lowering the price of capital, further reducing net worth, and feeding back to reduce credit supply. The currency mismatch channel and the asset-price channel interact to amplify the initial shock.

Portfolio dollarization rule: The assumption that each household’s share of savings held in foreign-currency deposits is a linear function of net wealth (x_i = λ_bar + λ·b_i, with λ > 0 and x_i = 0 for borrowers). This rule is calibrated to match the wealth-gradient of dollar holdings in the 2013 Uruguayan Household Financial Survey, and through market clearing it pins down the aggregate bank deposit dollarization rate and the distributional exposure of households to exchange rate shocks.

Exchange rate stabilization trade-off: The central bank’s choice of how much to raise domestic interest rates in response to a depreciation (parameterized by κ_e in the augmented Taylor rule). A higher κ_e reduces the bank’s currency mismatch loss but simultaneously depresses asset prices and raises borrowing costs, potentially worsening the financial accelerator. The paper shows the net welfare effect depends critically on the level of deposit dollarization: at 40% dollarization aggressive leaning is harmful for most agents; at 80% dollarization a moderate response (κ_e = 0.5) can be welfare improving.

Diversification, Market Entry, and the Global Internet Backbone

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates how buyer demand for supplier diversification shapes entry incentives and market structure, using the global undersea fiber-optic cable industry as the empirical setting. The research question has two parts: first, how much of observed cable entry and surplus generation is attributable to buyers’ diversification motives rather than standard price competition; and second, whether market forces produce too much or too little diversification relative to the social optimum.

The empirical setting spans 2005–2021 and covers the worldwide network of undersea cables that carries more than 98% of all international internet traffic. Cables fail frequently — hundreds of faults per year — and industry professionals confirm that “no customer would buy capacity on a single cable.” The median monthly price for a 10Gbps lease fell from $55,500 in 2005 to $2,200 in 2021, and the number of active cables roughly doubled over the sample period.

The authors use proprietary data from TeleGeography covering cable characteristics (construction costs, capacity, landing points, entry dates), quarterly bandwidth prices at the city-pair level, annual used bandwidth at the country-pair level, and 168 documented cable faults. Markets are defined as country-pairs in calendar quarters.

The theoretical model begins with a representative buyer who splits bandwidth purchases equally across n symmetric cable operators to minimize expected disruption costs. Because disruption shocks are i.i.d. across cables, adding suppliers reduces the variance of realized bandwidth delivery, lowering the required over-provisioning buffer. This generates a “market expansion” channel: entry increases aggregate demand holding prices fixed, not just through price competition. The aggregate demand equation takes log-linear form with cable count indicators alongside price and demand shifters.

The structural model adds a dynamic oligopoly game where firms make entry and exit decisions as a non-stationary Markov Perfect Equilibrium, with Cournot competition in each period. The three-step estimation procedure recovers: (1) price elasticities and diversification parameters from an IV demand regression using electricity generation cost shares as instruments; (2) marginal costs from firms’ first-order conditions; (3) entry and fixed costs from a nested pseudo-likelihood (NPL) estimator, supplemented by construction cost data to separately identify entry costs given the near-absence of observed exits.

Key demand results: the IV price elasticity is −1.36. The market expansion effect is large and exhibits decreasing marginal returns — entry of a second cable expands demand by as much as a 28.3% price decrease; a third cable is equivalent to a 19.3% price decrease; an eighth cable is equivalent to a 7.5% price decrease. The demand model achieves R² = 95%.

The first counterfactual removes the diversification channel entirely (entry raises competition only). Without diversification, cable investment falls by 12%. The net present value of total surplus per market over the sample period averages $1.11 billion under the observed equilibrium; supplier diversification accounts for 11% of total surplus and 27% of consumer surplus.

The second counterfactual quantifies two opposing distortions relative to the social optimum. Business-stealing creates excessive entry (entrants reduce incumbents’ output), while diversity effects create insufficient entry (marginal entrants generate surplus through diversification they cannot fully capture). At end-of-sample (2021-Q4), diversity distortions in terms of number of entrants range from 54% to 125% of the business-stealing distortion. Business-stealing tends to dominate for most markets, producing moderately excessive entry. Relative to the market outcome, total surplus under the social planner’s solution is on average 10% higher: 53% of this welfare gap is attributable to diversity effects and 47% to business-stealing effects. These findings hold across market heterogeneity in entry costs, market size, and demand growth.

The paper concludes that profit-maximizing suppliers fail to fully internalize diversification-related social benefits, and that targeted entry subsidies would pass cost-benefit tests in settings where diversity distortions dominate.

Q: What is the core mechanism by which supplier diversification expands demand? A: When buyers split purchases across n cable operators whose disruption shocks are i.i.d., adding a supplier reduces the variance of realized delivered bandwidth. The buyer therefore needs to hold a smaller over-provisioning buffer to achieve the same expected level of used bandwidth B. This lowers the effective cost of a given quantity of used bandwidth, shifting the aggregate demand curve outward. As the number of suppliers grows to infinity, the expected disruption cost converges to zero.

Q: How large is the market-expansion effect of diversification empirically? A: The effect is large but exhibits decreasing marginal returns. Entry of a second cable expands demand by as much as a 28.3% price reduction holding prices fixed; the third cable is equivalent to a 19.3% price reduction; and the eighth cable is equivalent to a 7.5% price reduction. All cable-count coefficients are positive and statistically significant in the IV demand model.

Q: How is price endogeneity addressed in the demand estimation? A: Bandwidth prices are instrumented using the marginal cost of electricity generation — specifically, country-level electricity generation shares (coal, gas, oil) interacted with quarterly commodity price series for coal, gas, and oil (Brent crude, Australian coal price, EU natural gas price). The first-stage results indicate electricity costs are strong predictors of bandwidth prices. Accounting for endogeneity raises the price elasticity from an OLS level to −1.36 in absolute value, consistent with the expected direction of OLS bias.

Q: What share of cable investment and surplus is attributable to diversification motives? A: In the counterfactual where the diversification channel is eliminated — entry raises competition and lowers prices but provides no diversification benefit — cable investment falls by 12%. Under the observed equilibrium, the net present value of total surplus per market over 2005–2021 averages $1.11 billion; supplier diversification accounts for 11% of this total surplus and 27% of consumer surplus.

Q: How are the two distortions — business-stealing and diversity — defined and separated? A: Business-stealing distortion arises because entrants reduce incumbents’ outputs and revenues, so private entry benefits exceed social benefits, leading to excessive entry. Diversity distortion arises because entrants create surplus for buyers through diversification but cannot fully capture it without perfect price discrimination (following Spence (1976) and Mankiw and Whinston (1986)), leading to insufficient entry. The authors disentangle these by comparing: (i) the social planner’s solution (eliminates both distortions), and (ii) a coordinated entry solution maximizing producer surplus (eliminates only business-stealing). The residual gap between the two identifies the diversity distortion.

Q: What is the net direction and magnitude of distortion in equilibrium market structure? A: At 2021-Q4, for most markets, business-stealing dominates, leading to moderately excessive entry. Diversity distortions in number of entrants range from 54% to 125% of the business-stealing distortion across markets. Relative to the market outcome, the social planner’s solution yields average total surplus that is 10% higher. Of that welfare gap, 53% is attributable to diversity effects and 47% to business-stealing effects.

Q: How do market characteristics affect which distortion dominates? A: The paper analyzes cross-market heterogeneity and identifies market features — including the size of entry costs, market size, and the rate of demand growth over time — as determinants of whether insufficient diversification or excessive entry is the binding distortion. Markets with higher entry costs or slower demand growth are more likely to exhibit insufficient diversification.

Q: How are entry costs identified given the near-absence of cable exits in the data? A: Because exit events are rare in a nascent industry — only a handful of exits observed, mostly after 2020 — entry and fixed costs cannot be separated by exit decisions alone. The authors address this by using cable-level construction cost data from TeleGeography to estimate entry costs outside the dynamic model. With entry costs in hand, firms’ optimal entry decisions identify fixed costs. Scrap values are normalized to zero, consistent with industry reports that retired cables are typically abandoned on the seabed.

Q: What role does the non-stationarity of the market environment play in the model? A: The data covers the industry’s earliest growth phase, with demand growing by roughly three orders of magnitude (used bandwidth from 5 Tbps in 2005 to 2,886 Tbps in 2021) and prices falling by a factor of roughly 25. The authors use a non-stationary Markov Perfect Equilibrium concept in which strategies and transition functions are indexed by time, aligning with the treatment of high-tech commodities in Igami (2017).

Q: What are the policy implications of the findings? A: Because profit-maximizing suppliers do not fully internalize the diversification-related social benefits of entry, entry rates can be sub-optimal from a welfare perspective when diversity distortions dominate. The authors suggest targeted entry subsidies would pass cost-benefit tests in such cases. For antitrust analysis, regulators who ignore the demand-expansion effect of incremental suppliers may incorrectly judge a market as sufficiently competitive. In merger review, authorities must account for firms’ private incentives to provide diversification to reach accurate welfare conclusions.

Q: How does the paper verify that diversification demand is not a spurious empirical artifact? A: Several checks support the causal interpretation. The estimated demand parameters are consistent with the predictions of the consumer-level utility maximization problem derived analytically: decreasing marginal returns to diversification and a positive relationship between the number of suppliers and demand. The demand model achieves R² = 95%, suggesting limited unobserved confounders. Additionally, 78% of cable faults involve only a single cable, confirming that disruptions are geographically isolated and that cross-cable diversification provides genuine insurance value.

Q: What are the main data limitations acknowledged by the authors? A: The authors cannot observe cable-level revenue or market shares, nor contracts between buyers and sellers; only aggregate country-pair used bandwidth is observed. Price coverage is not comprehensive — TeleGeography collects prices on a voluntary basis from dozens of providers. The cable faults dataset (168 faults) represents only a subset of total faults, as collection focuses on publicly disclosed events. The demand model also does not explicitly account for substitution patterns across firms due to lack of firm-level market share data, though the high R² partly mitigates this concern.

Diversification (in this paper’s sense): Buyers’ practice of splitting bandwidth purchases across multiple cable operators to reduce exposure to idiosyncratic disruption risk. Diversification across n cables with i.i.d. disruption shocks reduces the variance of realized delivered bandwidth and lowers the required over-provisioning buffer, making the effective cost of a given usage level B a decreasing function of n.

Market Expansion Effect: The channel through which entry of additional cable suppliers raises aggregate demand holding prices fixed. This occurs because each additional supplier reduces disruption risk, allowing buyers to demand more used bandwidth for the same price. It is distinct from the conventional competition channel (entry lowering prices).

Diversity Distortion: The tendency toward insufficient entry arising because marginal entrants generate consumer surplus through diversification benefits but cannot fully capture this surplus absent price discrimination. Follows Spence (1976) and Mankiw and Whinston (1986).

Business-Stealing Distortion: The tendency toward excessive entry arising because entrants reduce incumbents’ output and revenues, creating a gap between private and social returns to entry.

Non-Stationary Markov Perfect Equilibrium: The equilibrium concept used for the dynamic entry game, in which strategies and equilibrium selection rules are indexed by calendar time to accommodate substantial secular trends in demand and costs — as opposed to a stationary MPE which assumes a stable long-run distribution.

Used Bandwidth vs. Purchased Bandwidth: Used bandwidth B is the amount the buyer is committed to delivering (to downstream customers or for internal use). Purchased bandwidth Q is what the buyer actually contracts for across all cables; Q > B because the buyer holds an over-provisioning buffer against disruption risk. The ratio B/Q is a decreasing function of the disruption cost parameter gamma and an increasing function of the number of suppliers n.

Nested Pseudo-Likelihood (NPL) Algorithm: The baseline estimator for the dynamic game, following Aguirregabiria and Mira (2007). It iterates on the best-response mapping to impose equilibrium restrictions. The authors supplement NPL with two-step estimators (1-PML, 1-MD) and the spectral algorithm of Aguirregabiria and Marcoux (2021), which solves for the root of a nonlinear system using a quasi-Newton method and is robust to fixed-point instability.

Do The Effects of Nudges Persist? Theory and Evidence from 38 Natural Field Experiments

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks why the Home Energy Report (HER) — a widely deployed social-comparison nudge that shows households how their electricity consumption compares to their neighbors — produces behavioral changes that persist long after the nudge is discontinued, while analogous nudges in other domains (charitable giving, financial savings, voter turnout, tax compliance) fade almost entirely within a year or two. The authors formalize a research design to decompose the HER’s long-run effectiveness into two channels: technology adoption (a change in the stock of energy-efficient capital in the home) and habit formation (a change in the stock of habits or skills in the resident).

The identifying strategy exploits the administrative rule that when the initial resident in an HER experiment moves out, HER mailings stop immediately — but electricity consumption in the home continues to be observed as new residents occupy it. Under three assumptions — (1) treatment assignment did not influence the initial resident’s decision to move; (2) treatment assignment did not influence the type of resident who moved in; and (3) energy-efficient technology adopted in response to the HER remained in the home after the move — the post-move HER effect identifies the fraction of the long-run treatment effect attributable to technology adoption (ATK), and the remainder identifies the fraction attributable to habit formation (ATH).

Data come from 38 natural field experiments administered by Opower between 2008 and 2013 across 21 U.S. residential energy providers, comprising 61,310,166 electricity bills for 1,810,096 homes. The mover sample, restricted to homes where the initial resident deactivated service at or after the receipt of their fourth HER, contains 5,890,855 bills for 139,908 homes. Treatment and control homes enter the mover sample at statistically indistinguishable rates and have similar baseline electricity consumption.

The main findings: the HER reduced electricity consumption by 2.1 percent in the long run (the pre-move ATE). After the initial resident moved and the HER was discontinued, 1.1 percent of the reduction persisted in the home — attributable to technology. The habit channel accounts for the remaining 1.0 percent reduction. Normalizing by the ATE, 51.4 percent (s.e. = 13.1) of the long-run effectiveness is attributable to technology adoption and 48.6 percent to habit formation. The persistence of the post-move effect is robust across alternative specifications, different HER-receipt cutoffs, balanced panels, and exclusion of low-consumption move-period homes. A falsification test using rental homes — where tenants do not typically own appliances and the technology channel is therefore shut down — yields a null post-move effect, consistent with the balanced-habits assumption.

The authors use these results to explain a broader empirical pattern: one year after discontinuation, social comparison nudges targeting compliance, charitable giving, savings, and voter turnout retain on average only 4 percent of their initial effect, while nudges targeting energy and water conservation retain 65 percent. The paper argues this divergence reflects the relative abundance of enabling technologies in conservation contexts versus their absence in compliance or voting contexts. The findings also have cost-benefit implications: ignoring HER-induced technology adoption overstates net benefits by as much as 65 percent, depending on assumed technology cost per kWh saved (ranging from $0.03 per kWh saved per Gillingham et al. 2018 to $0.12 per kWh saved per Billingsley et al. 2014).

Scope conditions: results are specific to electricity-consumption nudges in the U.S. residential sector; the technology channel identification requires that adopted equipment stays in the home after a move; the decomposition rests on a linear production function for outcomes in habits and technology.

Q: What is the Home Energy Report and how was it administered in these experiments? A: The HER is a mailed social-comparison report that contrasts a household’s electricity consumption with that of similar neighbors. In each of the 38 waves, homes were observed for a 12-month baseline, then randomly assigned to treatment (receiving HERs) or control. HERs were mailed monthly, bimonthly, or quarterly; generation ceased when the initial resident deactivated electricity service.

Q: What is the paper’s central identification strategy? A: The authors exploit a discontinuity created when the initial treated resident moves out: HER mailings stop, but the home’s electricity consumption continues to be measured as new residents move in. Under three assumptions about non-interference of treatment with moving decisions, balanced habits of subsequent residents, and stability of adopted technology, the post-move HER effect point-identifies the technology-adoption component (ATK) of the long-run average treatment effect (ATE). The habit-formation component (ATH) is then inferred as ATE minus ATK.

Q: What are the three identifying assumptions and how are they tested? A: Assumption 1 (no effect of treatment on moving rates) and Assumption 2 (balanced habits of subsequent residents) are tested with the data; treatment and control homes enter the mover sample at statistically indistinguishable rates and have similar baseline consumption, supporting Assumption 1. The rental-home falsification test supports Assumption 2: rental homes show a null post-move effect, consistent with renters having balanced habits because the technology channel is inactive in rentals. Assumption 3 (stable technology after a move) is untestable from the data; the authors note that violation of this assumption would imply the post-move effect is a lower bound on ATK, making the technology-adoption estimate conservative.

Q: What are the main quantitative estimates of the decomposition? A: The pre-move (long-run) ATE is -2.1 percent of baseline electricity consumption. The post-move effect (ATK) is -1.1 percent, and the habit-formation component (ATH) is -1.0 percent. Normalizing by the ATE, 51.4 percent (s.e. = 13.1) is attributed to technology adoption and 48.6 percent to habits.

Q: How large is the HER effect in absolute terms during the comparison period? A: During the comparison period, the HER reduced average daily electricity consumption by approximately -1.8 to -2.3 percent in the first year and -1.5 to -2.0 percent in the second year, with 95 percent confidence intervals excluding zero. In levels, these correspond to roughly -0.6 to -0.9 kWh per day — equivalent to using 2 to 4 sixty-watt incandescent bulbs for 5 fewer hours per day.

Q: How persistent is the HER effect during the move period? A: In the first year of the move period the HER continues to produce reductions of -1.7 and -1.4 percent; more than a year after the initial resident’s departure the estimated effect is -1.2 percent. All move-period estimates are statistically significant at conventional levels.

Q: How does the paper explain variation in persistence across social-comparison nudge contexts? A: One year after discontinuation, nudges targeting compliance, charitable giving, savings, and voter turnout retain on average only 4 percent of their initial effect, while nudges targeting energy or water conservation retain 65 percent on average. The paper argues the divergence reflects the relative availability of enabling technologies: households can adopt long-lived, input-efficient technologies (appliances, fixtures) to reduce energy and water use, but analogous technologies to facilitate compliance, donations, or voting are largely unavailable or absent.

Q: How does this paper’s finding about technology adoption compare to Allcott and Rogers (2014)? A: Allcott and Rogers (2014) used participation in utility-sponsored energy-efficiency programs as a proxy for technology adoption and found it explained no more than 2 percent of the HER’s long-run effectiveness. The authors reject this conclusion: their decomposition attributes 51.4 percent to technology, which is estimated precisely enough to statistically reject the 2 percent figure from Allcott and Rogers (2014). They attribute the discrepancy to the imperfect proxy used by Allcott and Rogers and low statistical power in analogous analyses.

Q: What are the cost-benefit implications of accounting for HER-induced technology adoption? A: Assuming monthly HERs for one year, a household electricity price of $0.10/kWh, and benefits accruing over two years, the baseline net benefit (ignoring technology costs) is $32.38 per household (electricity savings of $44.38 minus $12 administration cost). Using a technology cost of $0.03/kWh saved (Gillingham et al. 2018), net benefits fall to $27.14. Using $0.12/kWh saved (Billingsley et al. 2014), net benefits drop to $11.43 — a reduction of up to 65 percent from the baseline estimate. The HER still passes cost-benefit analysis but prior evaluations that ignore technology costs overstate net benefits substantially.

Q: How robust are the decomposition results to alternative sample definitions and specifications? A: The qualitative findings are stable across: alternative sets of control variables (Table A1); mover samples defined by receiving as few as 1 or as many as 5 HERs before moving (Table A2, with pre-move effects of -2.08 and post-move effects of -0.93 to -1.04 across cutoffs); balanced panels requiring fixed observation windows in each period (Table A3); and exclusion of homes showing unusually low consumption in the move period (Table A4, post-move effects of -1.19 to -1.48).

Q: What policy implications does the paper draw for nudge design? A: Policymakers seeking persistent nudge effects should target behaviors that can be augmented by readily available technologies, or pair social-comparison nudges with opportunities to adopt new technologies. In voting contexts, combining social-comparison nudges with opt-in mail-in or online ballot defaults could produce more persistent effects. In savings and charitable giving, pairing social comparisons with automatic contribution-rate defaults (as in Madrian and Shea 2001; Thaler and Benartzi 2004) is predicted to produce longer-lived effects than the nudge alone.

Q: What methodological contribution does the paper offer beyond the HER application? A: The mover-based decomposition is a generalizable research design for separating human capital (habits, skills) from physical capital (technology, infrastructure) as channels of policy effectiveness. The authors suggest it can be applied using other natural separation events — such as student graduation or employee departure — to assess the extent to which nudges build human capital in both recipients and the organizations in which they are embedded.

Technology adoption channel (ATK): The component of the HER’s long-run average treatment effect attributable to increases in the stock of energy-efficient technologies in the home — identified empirically as the post-move HER effect that persists after the treated resident departs and the HER is discontinued.

Habit formation channel (ATH): The component of the HER’s long-run treatment effect attributable to changes in the habits or skills of the resident — inferred as the residual after netting the technology component (ATK) from the total long-run effect (ATE).

Post-move effect: The estimated difference in electricity consumption between treatment and control homes after the initial resident has moved out, the HER has been discontinued, and a new resident has taken occupancy; under the paper’s identifying assumptions this equals ATK.

Balanced-habits assumption: The identifying assumption that treatment assignment did not influence the characteristics or habits of residents who subsequently moved into homes in the experimental sample, so that the habits of incoming residents are comparable across treated and control homes.

Stable-technology assumption: The identifying assumption that energy-efficient technologies adopted in response to the HER remain in the home after the initial resident moves; relaxing this assumption implies the post-move effect is a lower bound on ATK.

Home Energy Report (HER): A mailed social-comparison report that contrasts a recipient household’s electricity consumption with that of similar neighboring households; the treatment studied across all 38 experiments in this paper.

Enabling technologies: Long-lived, input-efficient capital goods (appliances, lighting, insulation) that reduce the marginal cost of conservation and thereby lock in behavioral changes induced by a nudge; their relative abundance in energy and water conservation contexts — versus their absence in voting, giving, or compliance contexts — is the paper’s proposed explanation for cross-context variation in nudge persistence.

Dynamic Regulation with Firm Linkages: Evidence from Texas

Mon, 01 Jan 0001 00:00:00 +0000

This paper evaluates the efficiency of linked environmental regulation, a targeting mechanism whereby inspectors who discover violations at one plant can increase enforcement pressure on other plants sharing the same owner. The central research question is whether linking inspection decisions across co-owned plants adds value over unlinked, plant-level targeting and over random enforcement. The paper develops a new empirical framework of dynamic moral hazard under linked regulation, applies it to Texas environmental enforcement data, and uses the estimated model to evaluate counterfactual regulatory designs.

The empirical setting is the Texas Commission on Environmental Quality (TCEQ), which enforces the Resource Conservation and Recovery Act (RCRA, governing hazardous waste) and the Clean Water Act using a two-dimensional scoring system. A plant-level “site rating” score captures the individual plant’s compliance history, while a firm-wide “person rating” score aggregates the weighted average of plant scores across all plants under the same manager. Both scores feed into a multiplicative penalty escalation rule and a logit-form inspection probability function. The data are an unbalanced panel of 9,792 plants from 2012–2020, with detailed records of inspections, violations, penalties, scores, and ownership. The average plant is inspected with probability 0.289 per year and is linked with approximately 2 other plants through common ownership, though some firms own portfolios exceeding 50 plants.

The model features firms endowed with private types (abatement cost parameters) that may be affiliated within a firm’s portfolio, choosing continuous pollution actions to maximize discounted payoffs net of expected penalties. The regulator observes only scores and minimizes social costs subject to a binding inspection budget. A key computational innovation is “continuation value sufficiency”: because fully solving the portfolio optimization over large plant sets is infeasible due to the curse of dimensionality, each plant’s decision is approximated using three state variables — its own plant score, the firm-wide score, and a scalar summarizing other co-owned plants’ continuation values — governed by an AR(1) transition process. Estimation proceeds in three stages: OLS/logit for inspection and penalty parameters, simulated method of moments for type distribution and curvature parameters, and inversion of the regulator’s first-order conditions to recover sector-specific marginal social harms.

Descriptive evidence confirms three preconditions for linked regulation to add value: violations are positively correlated within firm portfolios, inspections are targeted toward higher-scoring plants on both dimensions, and higher inspection probabilities (instrumented by scores) are associated with fewer violations conditional on plant fixed effects. The coefficient on predicted inspection probability in the deterrence regression (specification 3, plant fixed effects, inspected years only) is −3.920, and an increase in log scores from 0 to 1.5 (roughly the interquartile range) reduces expected violations by approximately 0.5.

Structural estimates show that plant-level and firm-level type variance are similar (σ²_J = 0.209, σ²_F = 0.275), indicating moderate within-firm cost correlation. The curvature parameter y = 0.403 governs diminishing returns to negligence. In counterfactual experiments centered on a 30% budget increase (approximately 10 percentage point rise in per-plant inspection probability), unlinked plant-score-based escalations reduce social costs by 31.9% relative to random inspections. Linked firm-score-based escalations reduce social costs by 41.8% relative to random. The optimal mix — approximately 40% unlinked and 60% linked — reduces social costs by 42.2% relative to random. A back-of-the-envelope cost-benefit calculation calibrating utility-sector violation costs at $3,157 per violation and inspection costs at $740 finds a return of $11.77 in avoided social costs per additional dollar spent on inspections under the optimal mixed regime, versus $8.28 under random inspections.

The scope conditions are specific: the framework applies to RCRA and Clean Water Act plants in Texas, which typically cannot reallocate production across facilities (unlike Clean Air Act firms), so the pollution-substitution channel documented for multi-plant Clean Air Act firms is not modeled. The penalty schedule is taken as fixed; only inspection allocation is treated as a policy choice.

Q: What is linked regulation and why might it improve on unlinked enforcement? A: Linked regulation allows the regulator to increase inspection and penalty pressure on all plants owned by a firm when any one plant accumulates violations. It is efficient when compliance costs (types) are correlated within firms — e.g., due to managerial practices — because a violation at one plant is informative about likely violations at co-owned plants. This correlation means the regulator can target scarce inspection resources toward portfolios that are likely to harbor multiple bad actors, rather than inspecting each plant independently.

Q: How does Texas implement linked regulation in practice? A: Texas uses a two-dimensional scoring system. The plant score (“site rating”) summarizes the individual plant’s violation history over the past five years, normalized by complexity points. The firm score (“person rating”) is the complexity-weighted average of plant scores across all plants under the same manager. Penalties are then multiplied by escalation factors based on both scores: a firm in the “unsatisfactory performer” tier (firm score ≥ 55) faces a 1.1× firm escalation, while a “high performer” (firm score < 0.1) faces a 0.9× multiplier. Because the firm escalation applies to all plants in the portfolio simultaneously, even a small change in firm score can produce large aggregate deterrence effects across a large portfolio.

Q: What descriptive evidence supports the preconditions for linked regulation to add value? A: Three pieces of evidence are presented. First, a scatterplot (Figure 1) shows a positive cross-sectional correlation between a plant’s average violations per inspection and the leave-one-out average violations per inspection of its co-owned plants, indicating within-firm cost correlation. Second, Table 2 logit regressions show that both plant score (coefficient 0.121) and firm score (coefficient 0.062) significantly predict inspection probability, conditional on year and NAICS fixed effects. Third, Table 3 shows that conditional on plant fixed effects, predicted inspection probability is negatively associated with violations (coefficient −3.246 in specification 2, rising to −3.920 in specification 3 restricted to inspected plant-years), confirming dynamic deterrence.

Q: What is the curse of dimensionality problem and how is it resolved? A: In a multi-plant firm, each plant’s optimal action depends on the scores of every other co-owned plant, producing a state space of dimension n_plants + 1. For firms with portfolios of 50+ plants this is computationally infeasible. The paper introduces “continuation value sufficiency”: each plant’s decision is reduced to three state variables — its own score s_j, the firm score s_f, and a scalar W_j aggregating other co-owned plants’ continuation values. Transitions are approximated by plant-specific AR(1) processes. This reduces the portfolio problem from one high-dimensional value function to n_plant separate three-dimensional value functions, each solved independently within an inner fixed-point loop.

Q: How are the type distribution parameters identified? A: The mean type for each NAICS sector θ̄_g is identified by average violations per inspection within that sector — a higher mean type implies more violations conditional on inspection. The plant-level type variance σ²_J is identified by the share of total violation variance occurring across plants within the same firm. The firm-level type variance σ²_F is identified by the share of total violation variance occurring across firms. The curvature parameter y is identified by the responsiveness of violations to changes in predicted inspection probability (the coefficient from specification 3 of Table 3, which equals −3.920 empirically and −6.095 in simulation moments).

Q: What are the main counterfactual results? A: A 30% increase in the inspection budget (approximately +10 percentage points in per-plant inspection probability) is allocated under four regimes. Random inspections reduce violations per plant by 0.31 from a baseline of 0.98. Unlinked (plant-score) escalations reduce social costs by 31.9% more than random. Linked (firm-score) escalations reduce social costs by 41.8% more than random. The optimal mix (approximately 40% unlinked, 60% linked) reduces social costs by 42.2% more than random. In detected violations, all three targeted regimes perform similarly (+0.7% detected violations versus random), meaning the social cost advantage of linked regulation comes through greater undiscovered deterrence rather than through detection rates.

Q: How does the decomposition into static, own-plant, and cross-plant effects clarify the mechanism? A: For unlinked escalations: the static effect accounts for −5.4% of social cost relative to random, own-plant dynamic deterrence accounts for −30.6%, and the cross-plant effect is +4.1% (slightly adverse, because unlinked escalations do not account for portfolio-level incentives). For linked escalations: the static effect is −2.4%, own-plant deterrence is −24.5% (smaller than unlinked because linked escalations are less precisely targeted to individual plant histories), and cross-plant deterrence is −14.9% (large and beneficial). The dominance of cross-plant deterrence under linked escalations is the key mechanism explaining why linking outperforms unlinked targeting.

Q: What does the cost-benefit calculation find? A: Calibrating utility-sector violation social costs at $3,157 per violation (from Kang and Silveira 2021 for California water utilities post-2006) and inspection costs at $740, the paper finds a return of $11.77 in avoided social costs per additional dollar spent on inspections under the optimal linked/unlinked mix, versus $8.28 under random inspections. This suggests a large return to expanding enforcement budgets, with the gain amplified substantially by optimal targeting design.

Q: What are the scope conditions and limitations acknowledged? A: The framework applies to RCRA and Clean Water Act plants in Texas, where firms (e.g., gas station chains) typically cannot reallocate production across facilities, so the pollution-substitution channel documented by Gibson (2019) for Clean Air Act firms is not modeled. The penalty schedule is taken as fixed — only inspection allocation is treated as a policy choice — because Texas’s bylaws are prescriptive about how violations translate into penalties while leaving inspection targeting largely to regulator discretion. Social harm parameters h_g are identified only up to a scale normalization. The paper also does not model why types are correlated within firms (bad managers versus specialization), as the counterfactual results depend only on the degree of correlation, not its source.

Q: How well does the model fit the data? A: The model matches the targeted moments well (Table 5). Mean violations by NAICS sector are closely reproduced (e.g., utility: 0.201 empirical vs. 0.184 simulated; trade: 0.252 vs. 0.236). Responsiveness of violations to inspection probability matches closely (−6.398 empirical vs. −6.095 simulated). A non-targeted fit statistic — the correlation between a plant’s own violation rate and its co-owned plants’ violation rates — is 0.32 in simulation versus 0.26 in the data, which the authors characterize as a good out-of-sample fit given it was not directly targeted in estimation.

Q: How do heterogeneous effects shed light on the distributional consequences of regulation? A: The own-plant deterrence effect is positive for all plants including those with low types that are unlikely to be targeted, but is especially pronounced for high-type plants under unlinked escalations. Under linked escalations, high-type plants are deterred less to the extent they are co-owned with lower-type plants, because firm-score-based targeting aggregates across the portfolio. Cross-plant effects are predictably small under unlinked escalations and larger under linked escalations, especially for firms with high-type portfolios, since those are the firms whose firm scores respond most to individual violations.

Linked regulation: An enforcement mechanism in which the discovery of violations at one plant triggers increased inspection and penalty pressure on all other plants under the same owner. It exploits within-firm correlation in compliance costs to target scarce regulatory resources more efficiently than plant-by-plant escalation alone.

Escalation mechanism: A penalty and inspection design in which plants with worse compliance records — measured by accumulated compliance scores — face disproportionately greater scrutiny and higher penalties per additional violation. The TCEQ’s two-dimensional scoring system is an escalation mechanism operating simultaneously at the individual plant and firm portfolio level.

Plant score / firm score: The plant score (“site rating”) is a normalized index of a single facility’s violation history over the past five years, divided by investigation count and complexity points; the firm score (“person rating”) is the complexity-weighted average of all plant scores across the firm’s portfolio. Higher scores indicate worse compliance records and trigger both higher penalties and higher inspection probabilities.

Continuation value sufficiency: The paper’s solution to the curse of dimensionality in large plant portfolios. Rather than tracking the full joint score state across all co-owned plants, each plant’s optimal action is approximated using three variables — its own score, the aggregate firm score, and a scalar W_j summarizing co-owned plants’ continuation values — with state transitions governed by a plant-specific AR(1) process.

Dynamic moral hazard under linked regulation: The firm’s problem of choosing how much to invest in pollution mitigation at each plant over time, given that current actions affect future scores, future penalties, and — through the firm-wide score — future scrutiny of all co-owned plants. The moral hazard arises because abatement costs are private information not directly observable by the regulator.

Complexity points: A normalization factor in the TCEQ scoring system that adjusts raw violation counts for plant size and sector, enabling comparable compliance histories across heterogeneous facilities. They were introduced in 2012 specifically to prevent mechanically larger facilities from appearing riskier simply due to their scale.

Cross-plant deterrence effect: The reduction in pollution actions at co-owned plants induced by increases in the firm-wide score following a violation at one plant in the portfolio. In the counterfactual decomposition, this effect accounts for −14.9 percentage points of social cost reduction under linked escalations and is the primary mechanism by which linked regulation outperforms unlinked plant-level escalation.

Education and the Margins of Cyclical Adjustment in the Labor Market

Mon, 01 Jan 0001 00:00:00 +0000

Overview

Research question. This paper asks how the cyclical sensitivity of wages varies with workers’ educational attainment, what mechanisms drive the differences, and what the welfare consequences are of ignoring this heterogeneity. The starting point is a well-known asymmetry: less-educated workers have much higher and more volatile job separation rates, yet the standard macroeconomic literature has treated wages as roughly acyclical for a representative worker. Doniger asks whether this employment-centric picture is incomplete—and finds that it is, in a direction opposite to what the employment pattern would suggest.

Data and methodology. The paper uses two primary data sources: the National Longitudinal Survey of Youth 1979 (NLSY), which provides detailed job histories enabling identification of current and completed employer tenure, and the Current Population Survey (CPS) from 1995 to 2020, used both for employment flow statistics and, via biennial Job Tenure Supplements, for replication of the main wage findings. The sample is restricted throughout to males with 0–30 years of potential experience, following the conventions of the user-cost-of-labor (UCL) literature (Kudlyak, 2014; Basu and House, 2016). Workers are grouped into three educational categories: less than high school, high school or some college, and bachelor’s degree or more.

A key methodological contribution is a new, more parsimonious estimator for the cyclical sensitivity of the UCL. Rather than the multi-step indicator-variable approach of Kudlyak (2014), the paper recovers the UCL sensitivity from interaction terms between a flexible function of tenure and the cyclical position at the time of hiring, estimated within an augmented Mincer regression. This estimator admits higher-frequency identification, enables transparent inference via the delta method, and facilitates nonparametric impulse response estimation via the Jorda (2005) local projection method. Cyclical position is measured primarily as the deviation of the unemployment rate from an HP-filtered trend (lambda = 100,000), with robustness checks using the Hamilton (2018) filter and GDP-based detrending.

Main findings — employment. Monthly separation rates from the CPS (1995–2020) show that workers with less than a high school degree separate at a rate of 9.4 percent per month, more than twice the 3.4 percent rate for workers with a bachelor’s degree or more, regardless of cyclical position. The volatility of the separation rate (measured by the time-series standard deviation) is also larger for the least educated (1.7) than for the most educated (0.6). All sub-components of separation-to unemployment, to inactivity, and job-to-job transitions-exhibit the same ordering. In response to a 100 basis point monetary policy contraction (Romer and Romer, 2004 shocks), employment of workers with less than a high school education falls significantly, while employment of college graduates or more is statistically unaffected.

Main findings — wages. Using the NLSY, the cyclical sensitivity of the UCL to a 1 percentage point deviation of the unemployment rate from trend is estimated at approximately −15.5 percent for workers with a bachelor’s degree or more, −4.9 percent for high school or some college workers, and −1.4 percent (statistically indistinguishable from zero) for workers without a high school degree. In contrast, average hourly earnings (AHE) show much smaller and more compressed differences across education groups (−1.4, −1.1, and −1.0 percent respectively). The pattern of increasing procyclicality with education holds for new hires’ wages (NHW) as well but is considerably less stark than for the UCL. Replication in the CPS confirms the ordering: UCL sensitivities are −7.0 percent for college graduates, −2.9 percent for high school or some college, and effectively zero for those without a high school degree.

Mechanism. Counterfactual decompositions show that differences in the cyclical sensitivity of the wage-tenure profile—not just differences in job duration (separation rates)-account for the vast majority of the divergence across education groups. When separation rates are held constant across groups, the UCL sensitivity of the college-educated falls from -15.5 to −13.0 percent; when wage-tenure profile sensitivities are held constant, it falls to −6.3 percent, and the ordering across groups largely disappears. This finding is consistent with implicit contracting theory (Thomas and Worrall, 1988): longer expected employment durations for the more educated make it optimal to defer a greater share of the wage response to shocks over time, rendering near-term rigidities functionally less binding and producing more persistent effects of hiring-period conditions on subsequent wages.

Robustness. After controlling for cyclical sorting in match quality using the Hagedorn and Manovskii (2013) proxies (cumulated market tightness during tenure and leading up to the present job), the UCL sensitivity for college graduates falls modestly to −12.4 percent, confirming that match-quality composition effects account for only a minority of the documented pattern. The monetary policy shock analysis (Romer-Romer shocks identified from Greenbook forecast errors) yields a 35 percent decrease in the UCL for the most educated at the two-year horizon following a 100 basis point contraction, with no discernible effect for the least educated.

Welfare consequences. Using a stylized New Keynesian model extended to two labor varieties with heterogeneous wage flexibility, the paper shows that ignoring the documented heterogeneity leads to underestimating the welfare costs of business cycle fluctuations by more than 15 percent under the baseline calibration (unit Frisch elasticity and unit elasticity of intertemporal substitution). Conditional on this model, the welfare loss due to fluctuations for the least educated is more than 15 times larger than for the most educated. The paper explicitly notes this is a conservative lower bound, because the model assumes pooled household consumption, and admitting idiosyncratic consumption risk would disproportionately burden less-educated workers who bear adjustment on the extensive (employment) rather than intensive (wage) margin.

In depth

Q1. What is the user cost of labor (UCL), and why does the paper use it rather than average hourly earnings or new hires’ wages?

The UCL, formalized by Kudlyak (2014), is the present discounted value of wage payments an employer expects to make to a worker over the duration of the employment relationship, net of the continuation value of retaining that worker. It equals the new hire’s wage plus the expected wage wedge—the discounted stream of future wage differences between workers hired in the current period versus workers hired one period later. Unlike average hourly earnings or new hires’ wages, the UCL captures the persistent effects of macroeconomic conditions at the time of hiring on all future remitted wages, making it the appropriate allocative wage concept from a macroeconomic standpoint. The paper documents that AHE understates the cyclicality of wages for all groups but especially for the most educated, because AHE omits the highly cyclically sensitive expected wage wedge that characterizes college-educated employment relationships.

Q2. How does the paper’s new estimator for the cyclical sensitivity of the UCL differ from the existing method, and what does this enable?

The existing Kudlyak (2014)/Basu and House (2016) method recovers the UCL by estimating a very large set of date-of-hire x current-date indicator interactions, constructing a time series of the UCL, and then analyzing that series—a multi-step procedure that loses covariances across steps and makes cross-sectional disaggregation or high-frequency identification impractical. The new method instead estimates the UCL sensitivity directly from coefficients on the interaction between a flexible tenure function and the cyclical position at hiring, estimated within a single augmented Mincer regression. The UCL semi-elasticity is recovered analytically from these coefficients via a formula that sums discounted weighted differences in the tenure-interaction coefficients across the tenure horizon. This single-step approach allows transparent inference via the delta method, enables fully interacted specifications for heterogeneous subgroups, permits the hiring-date frequency (e.g., weekly in NLSY) to differ from the wage observation frequency (annual or biannual), and permits estimation from repeated cross-sections—all of which were infeasible in the prior approach.

Q3. What are the quantitative magnitudes of the education gradient in UCL cyclicality, and how do they compare across wage measures?

Using the NLSY with unemployment deviations from HP-filtered trend as the cyclical indicator: the UCL sensitivity is −15.5 percent (se 3.86) for workers with a bachelor’s degree or more, −4.9 percent (se 1.52) for high school or some college, and −1.4 percent (se 2.48, statistically insignificant) for those without a high school degree. By contrast, new hires’ wages show sensitivities of −3.4, −1.8, and −1.2 percent respectively, and average hourly earnings show −1.4, −1.1, and −1.0 percent. The gradient is largest and most statistically significant for the UCL, indicating that the bulk of the education gap in cyclical wage sensitivity operates through the persistent effect of hiring-period conditions on subsequent wages rather than through the contemporaneous wage alone.

Q4. What mechanism accounts for the UCL gradient — differential job durations or differential sensitivity of the wage-tenure profile?

The paper decomposes the UCL into the new hire’s wage and the expected wage wedge, and performs counterfactual exercises holding either separation rates or wage-tenure profile sensitivities constant across education groups (Table 3). Holding separation rates constant while allowing wage-tenure profiles to differ reduces the college-educated UCL sensitivity only modestly, from -15.5 to −13.0 percent; holding wage-tenure profile sensitivities constant while allowing separation rates to differ reduces the college-educated sensitivity to −6.3 percent and compresses the education gradient substantially. Thus, differential sensitivity of the wage-tenure profile—the degree to which wages continue to respond to hiring-period conditions over the course of the job-is the primary driver of the UCL gradient, with differential separation rates playing a secondary but non-trivial role. This finding confirms the prediction of Thomas and Worrall (1988) that lower separation rates support greater use of deferred payment and intertemporal risk sharing in optimal wage contracts.

Q5. How does the paper rule out cyclical sorting in match quality as the explanation for the UCL gradient?

Workers hired during recessions may be of systematically lower match quality, producing persistently lower wages not because wages are more cyclically sensitive for the same quality match but because recession hires are worse matches. Using the Hagedorn and Manovskii (2013) proxies for match quality - cumulated market tightness during the worker’s tenure on the present job (mjob) and on all prior jobs leading to it (mctj) - the paper augments the wage regression with full interactions between these proxies and the tenure-cyclicality terms. After controlling for match quality, the UCL sensitivity for college graduates falls from -15.5 to −12.4 percent (se 5.56); the point estimate remains large, statistically significant, and well above the estimates for lower-education groups. Figure 4 shows that match-quality adjustment primarily affects the first two years of the wage-tenure profile, after which the bias from cyclical sorting fades, confirming that scarring in remuneration for college graduates hired in recessions persists beyond what sorting can explain.

Q6. What do monetary policy shocks reveal about the education gradient in wage sensitivity?

Monetary policy shocks (identified from Greenbook forecast errors as in Romer and Romer, 2004) subject all labor markets to the same aggregate demand shock simultaneously, providing a cleaner test of differential responsiveness than cyclical regressions that may conflate demand composition and supply factors. Using Jorda (2005) local projections, a 100 basis point monetary policy contraction is associated with a 35 percent decrease in the UCL for workers with a bachelor’s degree or more at the two-year horizon, with statistically insignificant effects on the UCL of workers without a high school degree. The employment results are symmetric: less-educated workers’ employment falls significantly after a monetary contraction, while college-educated workers’ employment is unaffected. This cross-validation using monetary policy shocks supports the main thesis that more-educated workers absorb aggregate demand variation through the wage margin, while less-educated workers absorb it through the employment margin.

Q7. How does acyclical wages for the least educated affect interpretation of the existing macro literature on wage rigidity?

The aggregate finding of Kudlyak (2014) and Basu and House (2016)-that the UCL is more procyclical than new hires’ wages or average hourly earnings, casting doubt on wage rigidity as an amplification mechanism—holds only for educated workers. The paper finds that the UCL for workers without a high school degree is statistically acyclical by all three wage measures. This result restores a potential role for nominal wage rigidity in generating amplification and persistence of shocks for less-educated labor markets, including in the Diamond-Mortensen-Pisarides class of search models criticized by Kudlyak (2014) and in New Keynesian models criticized by Basu and House (2016). The paper therefore reconciles the literature on wage rigidity with the empirical finding of cyclical employment volatility concentrated among the less educated.

Q8. What is the welfare calculation, and what are its key results and limitations?

The welfare exercise uses a parsimonious New Keynesian model with two labor varieties (capturing more- and less-educated workers) and price and wage rigidities. The model is extended to admit heterogeneous wage flexibility, and the welfare costs of fluctuations are evaluated following the second-order approximation method of Gali et al. (2007). Under the baseline calibration (unit Frisch elasticity, unit elasticity of intertemporal substitution), the heterogeneous-worker economy incurs welfare costs of fluctuations that exceed those of the output-gap-equivalent representative agent economy by more than 15 percent. The welfare loss of the least-educated workers is more than 15 times that of the most educated. The paper explicitly characterizes this as a conservative lower bound: the model assumes pooled household consumption (within varieties), which implies equal consumption sensitivity across education groups, whereas in reality less-educated workers face income loss on the extensive margin without the wage smoothing available to the more educated. Relaxing this assumption, as in Krusell et al. (2009), could yield welfare losses an order of magnitude larger.

Q9. What does the CPS replication add, and what are its limitations relative to the NLSY baseline?

The CPS replication (Table 7) confirms the main ordering: UCL sensitivities are −7.0, −2.9, and approximately 0 percent for college graduates, high school or some college, and less than high school respectively. This rules out the concern that the NLSY findings are artifacts of the single aging cohort that characterizes the NLSY 1979. However, the CPS must be treated as a repeated cross-section because the tenure data are only available biennially and individual-level panel linkage across tenure supplement waves is infeasible. As a result, the CPS estimates cannot include individual fixed effects and must rely more heavily on observable controls (industry, occupation) to absorb cyclical variation in workforce composition. The CPS also precludes the match-quality controls of Hagedorn and Manovskii (2013). Despite these limitations, the main qualitative and directional findings replicate.

Q10. What policy implications does the paper draw for monetary policy?

The paper argues that because less-educated workers bear adjustment to aggregate demand shocks disproportionately through the employment margin while their wages are acyclical, welfare assessments that focus on the aggregate output gap underweight the costs borne by less-educated workers. The paper suggests that re-optimizing the monetary policy rule to account for documented heterogeneity would entail placing greater weight on the unemployment rate of the least-educated when measuring the output gap. More broadly, the K-shaped nature of labor market adjustment across education groups — wage scarring for the educated versus employment volatility for the less educated - implies that policies targeting either margin in isolation will miss welfare costs concentrated in the other group.

Key Concepts

User Cost of Labor (UCL). The allocative wage from the employer’s perspective, defined as the present discounted value of expected future wage payments to a worker hired at date t, net of the continuation value of retaining that worker in the next period. Formally, UCL_t = w_{t,t} + E_t[sum beta^j(1-s)^j (w_{t+j,t} - w_{t+j,t+1})], decomposing into the new hire’s wage and the expected wage wedge. In this paper’s usage, the UCL is the appropriate measure of the cyclical impact of shocks on labor costs because it captures persistent effects of hiring-period conditions on the entire subsequent wage sequence, not just the contemporaneous wage.

Expected Wage Wedge (EWW). The component of the UCL beyond the new hire’s wage: the discounted stream of differences between wages a worker hired at date t will receive in future periods and the wages a worker hired one period later would receive in those same future periods. The EWW is non-zero whenever wages are history-dependent - i.e., whenever current macroeconomic conditions at the time of hiring affect future remitted wages. The paper finds that the EWW is larger, more negative, and more persistent for more-educated workers conditional on being hired during a cyclical downturn.

Self-enforcing implicit wage contract. A labor contract in which the sequence of remitted wages is not pinned down period-by-period by spot-market forces but instead reflects an intertemporal risk-sharing arrangement between employer and worker that is sustained by the mutual benefit of the ongoing employment relationship. In this paper’s framework (drawing on Thomas and Worrall, 1988), lower separation rates make longer planning horizons feasible, which in turn expands the scope for deferring wage adjustments across time - effectively allowing more-educated workers and their employers to smooth the effects of cyclical shocks over longer horizons than is possible for less-educated workers with shorter expected job durations.

Cyclical sorting / match quality bias. The compositional concern that workers hired during recessions may be of systematically different (in this context, lower) match quality than those hired during booms, so that the persistent wage depression observed for recession hires could reflect poor match quality rather than cyclically sensitive wages for equivalent-quality matches. The paper uses the Hagedorn and Manovskii (2013) proxies - cumulated labor market tightness during the current job and prior employment history - to control for cyclical variation in match quality and assess the residual sensitivity of the UCL for average-quality matches.

Extensive versus intensive margin of labor market adjustment. The distinction between adjustment through changes in the number of workers employed (extensive margin: hiring and separation) versus adjustment through changes in wages or hours conditional on employment (intensive margin). A central finding of the paper is that less-educated workers bear cyclical adjustment disproportionately on the extensive margin (more volatile separation rates, employment losses following monetary contractions) while their wages are acyclical, whereas more-educated workers exhibit the reverse: stable employment but highly cyclically sensitive wages, especially as measured by the UCL.

Wage scarring. The persistent negative effect of hiring-period macroeconomic conditions on wages throughout the subsequent employment spell, beyond what is explained by contemporaneous market conditions. In this paper’s context, wage scarring is concentrated among more-educated workers: being hired when the unemployment rate is one percentage point above trend is associated with wages that remain depressed for several years, with the depression being larger and more persistent for college-educated workers than for those with less education. This is demonstrated via the expected wage wedge profiles in Figure 3 and is confirmed to survive controls for match-quality sorting.

Output-gap-equivalent representative agent economy. A conceptual benchmark constructed in the paper’s welfare analysis: a single-worker-type New Keynesian economy whose wage and labor supply elasticities are set equal to the output-elasticity-weighted averages of the two labor variety types in the heterogeneous economy. The paper shows that the heterogeneous-worker economy and this representative-agent benchmark produce identical aggregate output gap and price level paths (under Cobb-Douglas production, earnings elasticities are identical across varieties), but welfare diverges because period utility is more volatile for the variety with more rigid wages. The 15 percent excess welfare cost of the heterogeneous economy relative to this benchmark is the paper’s headline welfare result.

Eliciting Multiple Prior Beliefs

Mon, 01 Jan 0001 00:00:00 +0000

Multiple prior decision models—in which beliefs are represented by a set of probability measures rather than a single measure, generating a probability interval for each event—have become increasingly important in economics, but choice-based incentive-compatible elicitation of probability intervals remains an open problem: existing scoring rules and matching-probability methods cannot recover probability intervals without assuming probabilistic sophistication that is precisely least warranted in settings where multiple priors are most relevant. This paper develops a preference-based identification of a subject’s probability interval for an event, and a method for eliciting it under weak decision-theoretic assumptions with no need for probabilistic sophistication. Three incentivized experiments on artificial and natural sources of uncertainty demonstrate that the elicited intervals are sensitive to the direction and amount of information, are typically consistent with objective probabilities where available, and exhibit a predominance of non-degenerate probability intervals that are wider when there is less information or predictability. On aggregate, the choice-based intervals are similar to stated probability intervals, providing behavioral foundations for the use of stated interval techniques in the field.

In depth

Q1. What is the key identification challenge for multiple prior elicitation?

The key challenge is that existing incentive-compatible elicitation methods—scoring rules and matching-probability approaches—confound a subject’s probability interval with their ambiguity attitude, so they cannot separately identify the probability interval without assuming probabilistic sophistication. Under the popular α-maxmin EU model, the matching probability of an event depends on both the subject’s probability interval and their ambiguity attitude parameter α; even eliciting both the event and its complement’s matching probabilities yields two equations in three unknowns. Probabilistic sophistication is least warranted precisely in settings with deep uncertainty where multiple priors are most relevant, making precision-laden methods unsuitable.

Q2. What is the paper’s elicitation solution?

The paper develops a preference-based method that identifies a subject’s probability interval under weak decision-theoretic assumptions—with no need for probabilistic sophistication—using a series of incentivized choices, and demonstrates its feasibility in three laboratory experiments. The approach comprises two components: (i) a preference-based identification theorem establishing the conditions under which the probability interval can be recovered from observable choices; and (ii) a concrete elicitation procedure that is incentive compatible and does not impose the precision-laden assumption of probabilistic sophistication.

Q3. What do the experiments show?

Three incentivized experiments on artificial and natural sources of uncertainty demonstrate that probability intervals elicited by the method are sensitive to the direction and amount of information, are typically consistent with objective probabilities where available, and predominantly non-degenerate—with intervals wider when there is less information or predictability. The sensitivity to information and consistency with objective probabilities provide external validation that the elicited intervals capture real beliefs rather than noise or confusion. The predominance of non-degenerate intervals (rather than point probabilities) indicates that subjects genuinely hold imprecise beliefs in the relevant settings.

Q4. What is the relationship between choice-based and stated probability intervals?

On aggregate, probability intervals elicited with the choice-based method are similar to those stated by subjects, suggesting that the new method can provide behavioral foundations for the use of stated probability-interval techniques that are widely used in field surveys but previously lacked incentive-compatible grounding. This convergence is informative because stated intervals are cognitively simpler and can be collected at large scale in surveys, while the choice-based intervals are theoretically grounded; the consistency between them justifies the use of simpler stated methods in field applications.

Key concepts

multiple priors : a model of beliefs in which a decision maker’s uncertainty is represented by a set of probability measures rather than a single measure; associated with the Gilboa-Schmeidler (1989) maxmin expected utility model and its generalizations; generates a probability interval for each event. probability interval : the interval [p(E), p̄(E)] of probability values a subject’s set of priors assigns to event E; non-degenerate (with width > 0) when the subject’s beliefs are genuinely imprecise. incentive-compatible elicitation : an elicitation procedure in which subjects’ optimal strategy is to report their true beliefs; for Bayesian single-prior beliefs, achieved by scoring rules and matching-probability methods, but these fail for multiple priors. probabilistic sophistication : the assumption that a multiple-prior agent’s set of priors is generated by precise probabilistic beliefs; existing methods require this assumption to disentangle the probability interval from ambiguity attitude, but the paper’s method does not.

Financial Intermediation and Aggregate Demand: A Sufficient Statistics Approach

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a sufficient statistics approach to measuring the aggregate demand effects of financial intermediation disturbances — shocks to the ability of financial intermediaries to supply credit. The central contribution is characterizing, in a general class of models with heterogeneous firms and financial frictions, the aggregate demand impact of a disruption to intermediary balance sheets as a function of a small set of sufficient statistics observable from data: the elasticity of investment to intermediary net worth, the share of investment financed through intermediaries, and the sensitivity of asset prices to intermediary capacity. The approach does not require full model estimation, allowing model-free measurement of the aggregate demand loss from identified intermediary distress episodes. Applied to the 2008–2009 financial crisis, the paper estimates that the shock to financial intermediary balance sheets generated an aggregate demand reduction of 3–4 percentage points of GDP — substantially larger than estimates from reduced-form regressions that do not account for general equilibrium propagation.

In depth

Q1. What are the key sufficient statistics?

The three sufficient statistics are: (1) the elasticity of investment to intermediary net worth — how much investment falls per dollar of balance sheet loss; (2) the share of investment financed through intermediaries — how broadly the balance sheet shock propagates; (3) the sensitivity of asset prices to intermediary capacity — how much collateral values fall when intermediaries are distressed. Together these three moments summarize the aggregate demand impact of a balance sheet shock without requiring the researcher to specify the full structural model.

Q2. Why does the sufficient statistics approach give larger estimates than reduced-form regressions?

Reduced-form regressions typically compare investment of firms exposed to distressed versus healthy intermediaries, capturing the partial equilibrium direct effect of credit supply reduction; the sufficient statistics approach accounts for the general equilibrium propagation — the fall in asset prices and investment that affects even firms not directly borrowing from distressed intermediaries. The 3–4 percentage point estimate includes these spillovers; the reduced-form estimate misses them.

Q3. What is the policy implication?

The larger aggregate demand estimate implies that recapitalizing intermediaries during financial crises generates larger macroeconomic benefits than direct-effect estimates would suggest, strengthening the case for bank bailouts, TARP-style capital injections, and central bank emergency lending as counter-recessionary tools. The sufficient statistics framework also provides a natural way to compare intervention magnitudes: a policy that restores $X of intermediary capital generates an aggregate demand boost proportional to the measured elasticity.

Key concepts

sufficient statistics for financial intermediation : the small set of model-free moments (investment elasticity to net worth, intermediary financing share, asset price sensitivity) that summarize the aggregate demand impact of intermediary distress, derived in this paper from a general class of heterogeneous-firm models.

general equilibrium propagation : the amplification of an intermediary balance sheet shock through asset price declines and economy-wide investment responses, which the sufficient statistics approach captures and reduced-form regressions miss; the source of the larger 3–4 pp GDP estimate relative to partial equilibrium benchmarks.

Firm Quality Dynamics and the Slippery Slope of Credit Intervention

Mon, 01 Jan 0001 00:00:00 +0000

Crises have cleansing effects—low-quality firms face greater financial shortfalls and invest less than high-quality firms—but public credit support dampens these effects by reducing financing cost differentials, distorting the firm quality distribution downward and reducing total productivity. This trade-off between preserving output capacity and distorting quality determines the optimal size of intervention. The distortionary effects are self-perpetuating: a downward bias in quality necessitates interventions of greater scale in future crises, implying further distortions—a “slippery slope.” The distortions are amplified by expectations: because low-quality firms expect underpriced government funding in future crises, their Tobin’s q is biased upward, leading them to overinvest even in normal times, while high-quality firms may underinvest. A low interest rate environment exacerbates the distortionary effects because the low yield on savings discourages firms from accumulating precautionary internal liquidity against crises.

In depth

Q1. What are the cleansing effects of crises and how does credit intervention dampen them?

Crises have cleansing effects because low-quality firms face tighter financial constraints and have lower Tobin’s q, causing them to invest less than high-quality firms; public credit support reduces this differential, preserving overall production capacity but distorting the quality distribution downward. The model follows the limited-commitment literature (Kehoe-Levine, Kiyotaki-Moore, Rampini-Viswanathan): firms differ in productive capital quality that also serves as collateral. Government intervention is valued because the government has superior enforcement ability compared to private investors, but its credit support cannot be perfectly priced by quality—due to informational limits or political constraints—so it pulls financing costs of high- and low-quality firms closer together, dampening the cleansing mechanism.

Q2. What is the “slippery slope” mechanism?

The slippery slope arises because the downward bias in the quality distribution induced by one intervention necessitates larger interventions in future crises, generating a ratchet toward ever-larger public credit support. After intervention, high-quality firms accumulate capital less rapidly than they would absent intervention, while low-quality firms’ capital shares remain higher than in the laissez-faire equilibrium. The resulting lower aggregate productivity means that future crises are more severe in terms of output loss, requiring a larger optimal intervention, which in turn further distorts the quality distribution.

Q3. How do expectations of future intervention amplify the distortions?

Because low-quality firms expect underpriced credit support in future crises, their Tobin’s q is biased upward, motivating them to overinvest even in normal times; simultaneously, high-quality firms may underinvest because their Tobin’s q may fall below the first-best level. The self-perpetuating distortion thus operates through both the crisis-time reallocation channel and the pre-crisis investment channel, amplifying the divergence from the efficient allocation relative to a setting with no anticipation effects.

Q4. Why does a low interest rate environment exacerbate the distortionary effects?

A low interest rate environment exacerbates the distortionary effects of credit intervention because the low yield on savings discourages high-quality firms from accumulating precautionary internal liquidity against crises, causing them to invest less in crises and requiring a greater scale of credit support. Low-quality firms, expecting underpriced government funding, have even less incentive to self-insure through savings when interest rates are low, further worsening the quality distribution. The paper’s findings echo cautions against ultra-low interest rates (Brunnermeier and Koby, 2018; Quadrini, 2020) by providing a distinct mechanism operating through firm quality dynamics.

Q5. Can intervention be welfare-improving despite the distortions?

The paper shows that when carefully designed, intervention can improve welfare even though it generates distortionary effects on the firm quality distribution—the trade-off between preserving production capacity and distorting quality determines the optimal size of intervention. This framing does not suggest intervention should be avoided, but that its optimal scale requires balancing the quantity-preserving benefit against the quality-distorting cost. The paper previously circulated as “The Distortionary Effects of Central Bank Direct Lending on Firm Quality Dynamics.”

Key concepts

cleansing effect of crises : the tendency for crises to reduce the investment of low-quality firms relative to high-quality firms through tighter financial constraints, reallocating capital toward higher-productivity uses; credit intervention dampens this by reducing the financing cost differential. slippery slope of intervention : the self-perpetuating dynamic in which intervention-induced downward distortion of the quality distribution necessitates larger interventions in future crises, generating a ratchet toward ever-larger public credit support. credit mispricing : the inability of public credit support to differentiate financing costs by firm quality, arising from informational limits or political constraints on discriminatory treatment; the proximate source of the quality-distribution distortion.

Gendered Spheres of Learning and Household Decision-Making over Fertility

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates whether information asymmetries within households about maternal health risk can explain persistent spousal disagreement over fertility in a high-fertility, high-maternal-mortality setting. The authors develop a theoretical model and conduct a randomized field experiment among approximately 500 couples in peri-urban Lusaka, Zambia, where the lifetime risk of maternal death is 1 in 59 women and the maternal mortality ratio is 398 deaths per 100,000 live births.

The central mechanism is a communication barrier that arises from conflicting fertility preferences between spouses. When husbands have higher desired fertility than wives (4.43 vs. 4.19 children on average in the study sample), wives who are better informed about maternal health risk lack the incentive to credibly transmit that information to their husbands. Strategic communication concerns — not a generically lower propensity of men to learn from women — drive this asymmetry. The model predicts a pooling equilibrium in which no informative communication flows from wives to husbands when preference divergence is sufficiently large.

The experiment randomized whether the maternal mortality information curriculum was delivered to the husband or the wife in each couple, with both spouses in all arms also receiving a family planning curriculum. This design isolates the incremental effect of the maternal mortality information and permits identification of direct versus spillover effects within the household.

Consistent with the model, treated husbands significantly update their beliefs about maternal health risk factors, and their wives also update — information flows from husbands to wives. By contrast, treated wives update their own beliefs, but their husbands do not update at all. The test that spillover effects are symmetric is rejected (p-value = 0.097 for risk factors index; p-value < 0.001 for direct vs. indirect effects on men). The communication asymmetry is most pronounced among husbands who, at baseline, want a child as soon as possible — precisely the households with the greatest preference conflict.

Both treatment arms reduce fertility. Households in which the husband is treated experience a 43% reduction in the probability of having a child or being pregnant in the year following the intervention. The fertility reduction is strongest when the wife faces higher ex ante risk based on her birth history, consistent with the model’s prediction that treatment effects are concentrated among households with high maternal health costs.

The transfers evidence is the key differentiator between the two arms. When the wife is treated, fertility declines but is accompanied by a significant reduction in transfers from husband to wife, consistent with the wife updating her own beliefs without being able to convey them to her husband, who then reduces compensation. When the husband is treated, fertility declines without the same reduction in transfers — and treated husbands report higher communication with their spouse about family planning and higher relationship satisfaction. This combination is consistent with the husband treatment resolving the information gap directly, enabling efficient contracting, whereas the wife treatment leaves the information asymmetry in place.

The study is conducted in informal settlements of Lusaka, a prime-age urban sample in which the average woman is 28 years old with 2.6 children at baseline. Scope conditions: results apply to a setting with very high maternal mortality, large baseline spousal fertility gaps, and strong traditional beliefs (55.5% of men cite marital infidelity as a leading cause of maternal complications). Generalizability to lower-risk or lower-preference-gap settings is explicitly circumscribed by the model’s comparative statics.

Q: What is the baseline gender gap in knowledge of maternal health risk? A: Men are less likely than women to identify high parity (72.0% vs. 77.7%) and advanced maternal age (74.3% vs. 84.6%) as risk factors. In seven hypothetical scenarios rating complication likelihood on a 0–10 scale, men report lower scores than women in six out of seven cases. Despite Zambia’s 1-in-59 lifetime maternal mortality risk, only 27.6% of men (vs. 53.4% of women) report having attempted to discuss maternal health risk with their spouse.

Q: What drives the gender gap in knowledge? A: The authors argue the gap stems from “gendered spheres of direct and indirect knowledge accumulation of maternal labor and delivery outcomes.” Women are embedded in social networks where maternal mortality episodes are more salient: 11.0% of women report knowing a close friend who died giving birth, vs. 6.8% of men knowing a close friend whose wife died. The gap widens with social distance to the victim, suggesting women’s networks give them systematically more exposure to maternal mortality events.

Q: How does the model explain the failure of within-household communication? A: The model places husband and wife preferences as minimizing the distance between realized fertility and their respective net fertility optima (ideal fertility minus weighted maternal health cost). When the husband’s ideal fertility is high enough, he makes transfers to induce the wife to bear more children than her private optimum. Given these incentives, a wife who is informed about high health costs has an interest in exaggerating the cost to extract larger transfers. Because the husband anticipates this, no informative communication occurs in equilibrium — the only equilibrium is a pooling equilibrium where the wife’s message is uninformative regardless of her true cost realization.

Q: What is the specific asymmetry in belief updating observed in the experiment? A: Among treated husbands, both husbands and their wives update beliefs about maternal risk factors — information flows from husband to wife. Among treated wives, only the wife updates; her husband does not. The Wald test rejects equal direct and indirect effects on men at p < 0.001 and rejects symmetric spillovers at p = 0.097 for the risk factors index. There is no symmetric restriction binding for women’s updating across arms.

Q: How large is the fertility effect and which arm drives it? A: Households in which the husband is treated experience a 43% reduction in the probability of having a child or being pregnant in the year following the intervention. This effect is described as of the same order of magnitude as other household-level interventions shown to reduce pregnancy (citing Ashraf, Field, and Lee 2014). The fertility reduction is strongest among households where the woman faces higher ex ante risk based on birth history, consistent with the model’s Prediction 5 that effects are concentrated where theta_j is high.

Q: How do transfers differ between the wife-treated and husband-treated arms? A: When the wife is treated, the fertility decline is accompanied by a significant reduction in transfers from husband to wife. When the husband is treated, the fertility decline is not accompanied by a similar reduction in transfers. The authors interpret this pattern as: wife treatment leaves the husband uninformed, so he reduces transfers when he observes her reducing fertility without understanding why; husband treatment resolves the information gap, allowing efficient renegotiation without penalizing the wife.

Q: Which husbands fail to update beliefs even when their wife is treated? A: Husbands who at baseline want a child “as soon as possible” do not update their beliefs in response to their wife’s treatment status. These men also reduce transfers to their wife more than other groups when she is treated. In the model, these are precisely the households with the highest conflict of interest (high alpha_H), where the pooling equilibrium prediction is sharpest.

Q: What is the role of traditional beliefs about maternal mortality? A: 55.5% of men and 42.0% of women report (without prompting) marital infidelity as a leading cause of maternal labor and delivery complications — greater weight than assigned to lack of healthcare and poor health status combined. This stigma directly reduces women’s willingness to raise concerns about birth complications with their spouse, reinforcing the communication barrier the model formalizes.

Q: What are the welfare implications of targeting men vs. women with information? A: The fertility reduction from husband treatment is not inferior to that from wife treatment, but husband treatment also produces improvements in marital surplus — treated husbands report higher communication with spouse about family planning, higher relationship satisfaction, and greater closeness — whereas wife treatment reduces transfers to the wife, indicating she bears a financial cost. The authors argue male-targeted information can reduce unmet need for family planning while enhancing rather than exacerbating household conflict.

Q: Does this paper provide field experimental evidence on strategic communication models? A: The authors claim this is the first field experimental evidence directly testing models of strategic communication (Crawford and Sobel 1982; Mailath 1987; Crawford 1998, 2019), wherein persistent preference differences and conflict of interest impede communication and beliefs updating. Prior tests of these models were conducted in the lab; this paper provides the first real-world behavioral test with consequential decisions (fertility) in a high-stakes setting.

Q: What is the unmet need for family planning in the study sample? A: Overall, 32% of women in the sample report not using modern contraceptives at baseline. Of the 33% of women who want no more children, 27% are not using any modern contraceptive (8% of the overall sample). Of the 52% of women who wish to delay giving birth by at least one year, 23% are not using any modern contraceptive (12% of the overall sample).

Q: How does the model characterize the husband’s partial internalization of maternal health costs? A: The husband’s utility function includes the maternal health cost theta_j scaled by delta (0 ≤ delta ≤ 1), capturing how much weight he places on his wife’s risk. When delta is sufficiently high and the husband’s ideal fertility (alpha_H) is sufficiently low, or when his disutility of transfers (gamma) is sufficiently low, informative communication can occur after the husband is treated. When delta is low, the husband discounts his wife’s risk and communication barriers are more severe regardless of treatment.

Maternal health cost (theta): A random variable representing the welfare cost borne by the wife from childbearing, including mortality risk and morbidity. In Zambia, distributed with a higher mean than the worldwide distribution. Enters the wife’s utility directly and the husband’s utility only scaled by delta, his degree of internalization of her cost.

Gendered spheres of learning: The paper’s term for the systematic differential in experiential exposure to maternal mortality outcomes between men and women, arising from gender-segregated social networks. Women witness maternal mortality events more directly through closer social ties, while men’s networks provide systematically less exposure.

Communication barrier (pooling equilibrium): The equilibrium outcome in the model where no informative signal is transmitted from an informed wife to her uninformed husband about the true realization of maternal health cost. Arises because the wife’s incentives to misreport are independent of the true cost realization, making any message uninformative when preference conflict is sufficiently large.

Intra-household information spillover: The transmission of information learned by one spouse to the other as a consequence of the treated spouse’s belief update. The paper documents asymmetric spillovers: information flows from treated husbands to their wives, but not from treated wives to their husbands.

Husband’s demand for children (alpha_H): The husband’s ideal fertility level, which governs the degree of preference conflict within the household. Baseline husband desire for a child as soon as possible serves as the empirical proxy for high alpha_H and is the key moderator of spillover and transfer effects.

Degree of internalization (delta): The parameter in the husband’s utility function (0 ≤ delta ≤ 1) capturing how much weight he places on his wife’s maternal health cost. When delta is high and gamma (disutility of transfers) is low, communication can occur in equilibrium after the husband is treated.

Unmet need for family planning: Women who wish to space or limit births but are not using modern contraception. In the study sample, 32% of women report not using modern contraceptives at baseline, with substantial shares among both those wanting no more children and those wishing to delay.

Homeownership, Polarization, and Inequality

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks why job polarization and income inequality are higher in large U.S. cities, and proposes a novel housing-market mechanism that operates independently of — but interacts with — the skill-biased technical change (SBTC) explanations dominant in the existing literature.

The core argument is that large cities have experienced faster growth in house prices relative to both wages (price-wage ratio) and rents (price-rent ratio) since 1980. This excess price growth has priced middle-income households out of homeownership in expensive cities. Because low-income households cannot afford to own anywhere and high-income households can afford to own everywhere, it is specifically middle-income (middle-skilled) households whose location choice becomes entangled with their tenure choice. These households increasingly sort toward smaller, more affordable cities where they can purchase a home. This selective out-migration hollows out the middle of the income distribution in large cities, producing greater employment polarization and income inequality there.

Empirically, the paper uses Census and ACS data from 1980 to 2019 covering 465 commuting zones (CZs). Polarization is measured following Autor and Dorn (2013) by assigning 3-digit occupations to income percentiles fixed at 1980 levels; inequality is measured by the Gini coefficient and variance of log annual wages. Housing costs are captured by hedonic price and rent indices and three derived ratios. OLS and IV results (instrumented using the interaction of land unavailability and long-run changes in real interest rates) show that doubling of prices is associated with a 1 percentage point decline in the middle-skilled employment share; doubling of the price-rent ratio is associated with an 11.3 percentage point decline; doubling of the price-wage ratio with a 5.3 percentage point decline. Inequality follows the same pattern: doubling prices raises 100x the variance of log wages by 2.3 points; doubling the price-rent ratio raises it by 11.7 points; doubling the price-wage ratio by 7.7 points.

The migration mechanism is documented using 2001–2019 CPS ASEC data, which — uniquely among available sources — reports reasons for moving. A doubling of the price index, price-wage ratio, or price-rent ratio in the origin state relative to the destination raises the probability that a middle-income (2nd–4th quintile) household moves for housing-related reasons by approximately 5–10 percentage points in absolute terms, implying a 50–80% relative increase compared with low- or high-income households making a housing-related move.

The theoretical framework extends the standard spatial equilibrium (Rosen-Roback) model with two additions: skill heterogeneity and housing tenure choice. Households face a minimum house size constraint and a payment-to-income (PTI) constraint (calibrated at lambda = 0.308). These constraints create distinct skill thresholds for homeownership that vary by city; the interaction between location and tenure choices applies only to middle-skilled households who can afford ownership in cheap but not expensive cities.

In the quantitative model, calibrated separately for 1980 and 2019 with two locations (top 30 CZs vs. the rest), counterfactual experiments show that holding price-wage ratios at their 1980 levels reduces the excess polarization gap between large and small CZs by 93% and the excess inequality gap by 40%. Holding price-rent ratios constant reduces the polarization gap by 96% and the inequality gap by 27%. By contrast, shutting down SBTC entirely reduces the polarization gap by only 54% and the inequality gap by 73%. These results establish that while SBTC is an important driver, its effect on polarization and inequality is substantially amplified by faster house price growth in large cities; without the housing affordability channel, the effect of SBTC on disproportionate polarization would be 63–81% smaller and on the inequality gap 18–36% smaller.

Q: What is the paper’s central research question? A: The paper asks why job polarization and income inequality are systematically higher in large U.S. cities than in small ones. Prior literature attributed this to skill-biased technical change, external labor demand shocks, or IT-driven displacement of routine jobs; this paper proposes a complementary, housing-market-based explanation that does not rely on features of the production technology.

Q: What is the core mechanism linking house prices to polarization? A: When price-wage and price-rent ratios are higher in large cities, middle-income households face binding minimum-size and payment-to-income constraints that prevent them from owning a home there but not in cheaper cities. Because homeownership carries financial advantages, these households sort toward smaller, more affordable cities. Low-income households cannot afford ownership anywhere and high-income households can afford it anywhere, so only the middle group’s location choice is distorted by tenure considerations. This selective out-migration hollows out the middle of the income distribution in expensive large cities.

Q: What empirical patterns in CZ-level data motivate the paper? A: Doubling CZ size is associated with a 1.9 percentage point greater fall in the middle-skilled employment share and a 2.7 point higher growth in 100x the variance of log wages from 1980 to 2019. Larger CZs also experienced 3.4% higher price growth, 3.1% higher price-wage ratio growth, and a 10% greater increase in price-rent ratios. These associations persist after controlling for initial CZ size and other characteristics.

Q: What do the OLS and IV results show about house prices and polarization? A: A doubling of house prices is associated with a 1 percentage point decline in the middle-skilled share; a doubling of the price-rent ratio with an 11.3 percentage point decline; and a doubling of the price-wage ratio with a 5.3 percentage point decline. IV results using the interaction of land unavailability and the change in real interest rates as an instrument confirm the negative relationship remains statistically significant, suggesting a causal interpretation is plausible.

Q: What do the OLS and IV results show about house prices and income inequality? A: A doubling of prices is associated with a 2.3 point increase in 100x the variance of log wages; a doubling of the price-rent ratio with an 11.7 point increase; and a doubling of the price-wage ratio with a 7.7 point increase. IV results suggest a causal relationship between price growth and income inequality at the CZ level.

Q: What evidence does the paper provide for the migration mechanism? A: Using 2001–2019 CPS ASEC data (which reports stated reasons for moving, unlike the ACS), the paper estimates logit regressions of interstate migration for housing-related reasons. A doubling of the price index in the origin state relative to the destination raises the probability of a housing-related move for middle-income (2nd–4th quintile) households by 5–6 percentage points; a doubling of the price-wage ratio raises it by 6–7 percentage points; and a doubling of the price-rent ratio raises it by 7–10 percentage points. These effects imply a 50–80% relative increase in housing-related migration probability for the middle quintiles compared with the bottom or top quintile. Housing-related movers constitute over 12% of all interstate migrants in the sample.

Q: What is the key finding about homeownership rates? A: There is no statistically significant relationship between the change in homeownership rates and the growth in prices, price-rent, or price-wage ratios from 1980 to 2019. This is consistent with the model’s mechanism, in which middle-income households who cannot afford ownership in large cities move away rather than simply switching to renting there — so aggregate local ownership rates need not fall.

Q: How does the theoretical model generate the polarization result? A: The model extends the Rosen-Roback spatial equilibrium framework with skill heterogeneity and housing tenure choice. Two skill thresholds — one for minimum-size-constrained ownership and one for unconstrained ownership — interact with the price-wage and price-rent ratios of each city. Proposition 1 proves that a city with higher price-wage and price-rent ratios will have a lower middle-skilled share, because middle-skilled workers (those who can afford to own in cheap but not expensive cities) are drawn to cheaper locations. Proposition 2 shows that in a world with only renters or only owners, skill shares would be identical across cities regardless of price differences — the polarization result requires heterogeneity in tenure choice.

Q: What does the no-SBTC counterfactual show? A: Holding the parameters governing local returns to skills at their 1980 levels (shutting down skill-biased technical change) reduces the difference in the decline in the middle-skilled share between large and small CZs by 54% and the gap in the increase in the variance of log wages by 73%. This is broadly consistent with prior literature attributing the bulk of disproportionate polarization and inequality in big cities to SBTC.

Q: What do the constant price-ratio counterfactuals show? A: When price-wage ratios are held at 1980 levels (but SBTC is allowed to operate), the excess polarization gap between large and small CZs falls by 93% and the excess inequality gap by 40%. When price-rent ratios are held at 1980 levels, the polarization gap falls by 96% and the inequality gap by 27%. When both are held constant simultaneously, the polarization gap falls by 89% and the inequality gap by 27%. These results show that the effect of SBTC on polarization would be 63–81% smaller in the absence of the housing affordability amplification channel.

Q: Who are the largest losers from rising price-wage ratios in large cities? A: The counterfactual welfare analysis identifies middle-skilled workers with skill levels between approximately 0.29 and 0.80 as the primary losers. In the counterfactual with fixed price-wage ratios, workers with skills from 0.29 to 0.57 who previously could not afford ownership in large cities are now able to own there, and those with skills from 0.57 to 0.80 spend a smaller share of income on housing. This group either lost homeownership opportunities or was induced to move to less productive CZs by the actual price growth that occurred.

Q: How is the quantitative model calibrated and structured? A: The model is calibrated separately for 1980 and 2019 as two stationary spatial equilibria. It features two locations (the top 30 CZs, which account for 49.3% of employment, and the remaining CZs). Key parameters include a Frechet elasticity of 6.1, an agglomeration externality of 0.04, a PTI constraint of 0.308, and an annual discount factor of 0.96. Land shares differ between large and small CZs (0.3965 vs. 0.2239). The model finds that the price-rent ratio was relatively stable in large cities but fell in small ones, while the price-wage ratio increased much more in large CZs — both indicators point to purchasing a home becoming relatively more expensive in large CZs.

Q: What are the paper’s policy implications? A: Zoning reforms and other policies that increase housing supply in large, unaffordable cities could produce a more efficient spatial allocation of labor, greater aggregate productivity, and more economically diverse — less polarized and less unequal — cities, while also reducing the wealth gap between owners and renters. Policies that promote homeownership by reducing the cost of owning without raising housing supply may reduce local polarization and inequality but could lower aggregate output and do not necessarily increase homeownership rates.

Q: How does this paper relate to existing explanations for city-level polarization? A: The paper’s housing-market mechanism is explicitly complementary to SBTC-based explanations (Baum-Snow, Freedman, and Pavan, 2018; Cerina et al., 2023), external demand shock explanations (Davis, Mengus, and Michalski, 2020), and IT-displacement explanations (Eeckhout, Hedtrich, and Pinheiro, 2024). The paper’s key added contribution is that even if SBTC were the primary driver of disproportionate polarization, its measured effect would be substantially smaller in the absence of faster house price growth in large cities — the housing market amplifies rather than replaces the technology channel.

Job polarization (city-level): The hollowing out of middle-income employment shares in a commuting zone, measured as the change in the share of workers in occupations assigned to the 21st–80th income percentile (using the 1980 occupation-to-percentile mapping fixed over time). In this paper, polarization is greater in cities where price-wage and price-rent ratios grew faster, attributed to selective out-migration of middle-skilled households.

Price-wage ratio: The ratio of hedonic house prices to median annual wages in a commuting zone, constructed from Census and ACS data. A higher price-wage ratio tightens the payment-to-income constraint on potential homebuyers and is the primary driver of the skill threshold for homeownership in the model.

Price-rent ratio: The ratio of hedonic house prices to rents in a commuting zone. In the model, a higher price-rent ratio reduces the financial advantage of owning over renting, raising the skill threshold at which ownership becomes optimal. The paper treats price-rent and price-wage ratios as distinct channels that both independently amplify polarization.

Housing tenure choice: The household decision to own or rent, modeled as a discrete choice made at the start of life that interacts with location choice. Ownership requires satisfying both a minimum house size constraint and a payment-to-income (PTI) constraint (lambda = 0.308). The interaction between tenure and location choices is the paper’s key model innovation; it exists only for middle-skilled workers whose income is sufficient for ownership in cheap but not expensive cities.

Skill threshold for homeownership (s*_i): The minimum skill level at which a worker in city i chooses to own rather than rent, defined by Lemma 2. This threshold is decreasing in local labor productivity and increasing in price-wage and price-rent ratios. Workers with skill below s*_i in all cities always rent; those with skill above s*_i in all cities always own; those in between face city-dependent tenure choice that distorts their location decision.

Skill-biased technical change (SBTC): In the paper’s quantitative model, SBTC is represented by faster growth in the skill dispersion parameter (alpha_it) in large CZs, reflecting differential productivity growth concentrated at the top of the skill distribution. The paper finds SBTC accounts for 54% of the polarization gap and 73% of the inequality gap in its counterfactual, but argues its effect is amplified 4–5x by the housing affordability channel.

Payment-to-income (PTI) constraint: The constraint that a homebuyer cannot spend more than a fraction lambda (calibrated at 0.308) of annual labor earnings on the annual housing payment (user cost times price times quantity). This constraint, together with the minimum house size, determines the income threshold for ownership and makes location and tenure choices interdependent for middle-skilled workers.

Identification and Estimation of Dynamic Random Coefficient Models

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies linear panel data models where regression coefficients are individual-specific (random coefficients) and regressors may be predetermined — that is, sequentially exogenous rather than strictly exogenous, as occurs when a lagged dependent variable appears on the right-hand side. The canonical example is the AR(1) model Yit = gamma_i + beta_i * Yi,t-1 + epsilon_it, where both the intercept and the autoregressive coefficient vary across individuals. The setting is short panels (small T), which rules out learning about individual-level coefficient values.

The paper’s central finding, building on Chamberlain (1993, 2022), is that the mean of the coefficient distribution is not point-identified in this dynamic setting. Chamberlain established this for discrete regressors; the paper’s Proposition 1 extends the non-identification result to continuous regressors under stronger assumptions. The paper then characterizes finite lower and upper bounds for the mean, variance, and CDF of the random coefficient distribution. The identification strategy recasts the problem as an infinite-dimensional linear program and exploits the dual representation of that program (following Galichon and Henry (2009) and Schennach (2014)) to derive tractable closed-form bounds for the mean and optimization-based bounds for the variance and CDF.

For the mean parameter, the bounds take a closed-form expression involving the individual OLS estimator, the pooled OLS estimator, and cross-sectional moments of the data. The bounds remain finite even when the data are unbounded, provided certain moments of the data are finite. Tighter (refined) bounds are available when instrumental variables are brought in as additional unconditional moment restrictions. A numerical illustration shows how the outer identified set for E(beta_i) with a true value of 0.5 shrinks as T increases: at T=3 the outer set is approximately [0.216, 0.617]; at T=5 it narrows to approximately [0.306, 0.613]; the corresponding sharp identified sets (available for T=3 through T=5) range from [0.401, 0.593] at T=3 to [0.473, 0.532] at T=5.

The paper proposes computationally tractable inference procedures matched to each parameter. For mean parameters, the closed-form bounds permit a delta-method asymptotic approach augmented with Stoye’s (2020) smooth approximation to handle cases where the sample analog of the bound width can be negative (due to overidentification or mild misspecification). The resulting confidence intervals are valid and robust to overidentification. For the variance and CDF of the coefficient distribution, the paper uses the Andrews and Shi (2017) procedure for inference on a continuum of moment inequalities, which remains computationally feasible.

The empirical application estimates a generalization of Guvenen’s (2007, 2009) lifecycle earnings models using the Panel Study of Income Dynamics (PSID). Where Guvenen compared a restricted income profile (RIP, homogeneous persistence rho) against a heterogeneous income profile (HIP, heterogeneous time trend beta_i), this paper allows persistence rho itself to vary across households (rho_i). The key empirical findings are: (1) under both the RIP and HIP specifications, the estimated average earnings persistence E(rho_i) is significantly below 1; (2) the two specifications produce similar mean-persistence estimates once heterogeneity in rho_i is permitted, suggesting that misspecifying HIP as RIP or vice versa may not cause serious model misspecification when earnings persistence is allowed to vary; (3) the identified sets for the variance of rho_i provide evidence of genuine heterogeneity in earnings persistence across households, implying that households face different levels of earnings risk, which in turn contributes to heterogeneity in their consumption and savings behavior.

Q: Why is the mean of the random coefficient not point-identified in a short dynamic panel? A: Chamberlain (1993, 2022) first established this non-identification for discrete regressors. The paper’s Proposition 1 extends the result to continuous regressors under stronger assumptions. The fundamental obstacle is Lemma 1: E(beta_i) is point-identified if and only if there exists an unbiased estimator of beta_i in the individual time series, and no such estimator exists in short panels where T is small relative to the number of individual parameters.

Q: How does the paper characterize the identified set for the mean parameter? A: The identification problem is recast as an infinite-dimensional linear program. Using the dual representation (Galichon and Henry, 2009; Schennach, 2014), Theorem 1 yields a closed-form interval [L, U] = [BR - (1/2)sqrt(ERDR), BR + (1/2)sqrt(ERDR)], where BR is a weighted average of the individual OLS estimator and the pooled OLS estimator, ER is a non-negative term capturing cross-sectional variation in design matrices, and DR is a non-negative term related to residual variation. The bounds are finite whenever the relevant moments of the data are finite, even with unbounded data.

Q: How are the bounds tightened using instruments? A: Proposition 2 introduces refined bounds [LS, US] by incorporating additional unconditional moment restrictions from instruments Sit. The refined bounds use a larger set of restrictions and are weakly tighter than the baseline bounds. The empirical application employs up to 59 regressors with homogeneous coefficients (handled by Proposition 3), and instruments from lagged earnings levels and differences, substantially increasing the number of moment conditions.

Q: How are the variance and CDF of the coefficient distribution identified? A: Theorem 2 provides a general duality result for any parameter theta of the coefficient distribution. The lower bound is the maximum of E[min_{b} {m(Wi,b) + sum_k lambda_k phi_k(Wi,b)}] over Lagrange multipliers lambda, and the upper bound is the minimum of the corresponding maximum. Proposition 5 and Proposition 6 specialize this to the second moment (variance) of beta_i, with the upper bound requiring an eigenvalue assumption (Assumption 9) that the smallest eigenvalue of the individual design matrix R’R is bounded away from zero. Proposition 7 derives lower and upper bounds for the CDF P(e’Bi <= c) using a two-step optimization that separates the support into two regions.

Q: What guarantees computational tractability of the optimization problems? A: Proposition 4 establishes that GL(lambda, w) is globally concave in lambda for every w, and GU(lambda, w) is globally convex in lambda for every w. This means the optimization problems for the lower and upper bounds are concave maximization and convex minimization problems respectively, which can be solved with standard convex optimization methods.

Q: How does the inference procedure for mean parameters handle overidentification and misspecification? A: In finite samples, the sample analog of the bound-width term D_hat_S can be negative, which would make the estimated bounds degenerate. The paper adopts Stoye’s (2020) approach using the smooth approximation s(x,y) = sqrt((xy + sqrt((xy)^2 + r^2))/2). The (1-alpha)-level confidence interval combines a standard bound-based interval with an interval for a pseudo-true parameter mu*_e, ensuring validity under both correct specification and mild overidentification or misspecification.

Q: How does this paper’s approach to inference on the variance and CDF differ from that for the mean? A: For the mean, closed-form bounds permit a straightforward delta-method asymptotic argument and explicit confidence intervals. For the variance and CDF, the paper uses the Andrews and Shi (2017) procedure for inference on a continuum of moment inequalities, constructing a test statistic TAS(theta) = sup_{lambda} max{sqrt(N)(mu_hat_GL - theta)/sigma_hat_GL, sqrt(N)(theta - mu_hat_GU)/sigma_hat_GU}^2, 0, with the confidence set being the set of theta values not rejected. This procedure is computationally more demanding but remains feasible.

Q: What are the main empirical findings from the PSID application? A: In both the RIP and HIP specifications extended to allow heterogeneous persistence rho_i, the estimated average earnings persistence E(rho_i) is significantly below 1. Both specifications produce similar mean-persistence estimates once rho_i heterogeneity is permitted, suggesting that the HIP vs. RIP misspecification debate may be less consequential when persistence itself varies across households. The identified sets for the variance of rho_i provide evidence of genuine unobserved heterogeneity in earnings persistence.

Q: What is the economic significance of heterogeneous earnings persistence? A: Heterogeneity in earnings persistence rho_i means households face different levels of earnings risk: a household with high rho_i experiences earnings shocks that are more persistent, reducing its ability to smooth consumption over time and strengthening its motive for precautionary savings. The paper argues this heterogeneity contributes directly to heterogeneity in consumption and savings behavior, making rho_i a first-order parameter in lifecycle consumption models such as those of Hall and Mishkin (1982), Blundell, Pistaferri, and Preston (2008), and Arellano, Blundell, and Bonhomme (2017).

Q: How does the paper situate itself relative to Guvenen (2007, 2009)? A: Guvenen showed that allowing for heterogeneity in the time trend of earnings (HIP: heterogeneous income profile) yields estimated persistence significantly below 1, whereas imposing no such heterogeneity (RIP: restricted income profile) yields persistence near 1. This paper generalizes both models by additionally allowing persistence itself to vary across households (rho_i). The finding that both HIP and RIP deliver similar E(rho_i) estimates significantly below 1 suggests that Guvenen’s contrast may be partly an artifact of restricting persistence to be homogeneous.

Q: What is the scope of the identification results? A: The results apply to short panels (small T, large N), accommodate discrete, continuous, and unbounded data, and require the idiosyncratic error epsilon_it to be mean-independent of the full history of strictly exogenous regressors and of the current history of predetermined regressors. The bounds for the mean are finite under finite moment conditions on the data. The bounds for the variance additionally require the eigenvalue assumption (Assumption 9). The paper notes that the results extend to probit and logit models with individual-specific coefficients, panel VAR models, and systems of panel data regressions, though these extensions are not developed in detail.

Dynamic random coefficient model: A linear panel data model in which both the intercept and slope coefficients are individual-specific (gamma_i, beta_i), the regressor is predetermined (sequentially exogenous rather than strictly exogenous), and T is small — so individual coefficient values cannot be estimated from the time series alone.

Partial identification: The property that a parameter of interest (such as E(beta_i)) cannot be consistently estimated from the data (it is not point-identified), but finite lower and upper bounds on its value can be characterized. The paper shows this is the generic situation for dynamic random coefficient models in short panels.

Dual representation of infinite-dimensional linear programs: The technique, following Galichon and Henry (2009) and Schennach (2014), of converting an infinite-dimensional linear programming problem (which arises when data or coefficients are continuous) into an equivalent dual problem that yields tractable closed-form or convex-optimization-based bounds.

Refined bounds (instrument-augmented bounds): Tighter identified sets for the mean parameter obtained by incorporating additional unconditional moment restrictions from instruments Sit, beyond the baseline moment conditions. These correspond to Proposition 2 and make the identification interval weakly narrower.

Sequential exogeneity (predetermined regressor): The assumption E(epsilon_it | gamma_i, beta_i, Zi1,…,ZiT, Xi1,…,Xit) = 0, which allows the regressor Xit (e.g., Yi,t-1) to be correlated with future errors but not current or past errors. This is weaker than strict exogeneity and is what makes the model dynamic and identification challenging.

Heterogeneous income profile (HIP) vs. restricted income profile (RIP): In Guvenen’s framework, HIP allows the time trend of earnings to vary across individuals (heterogeneous beta_i), while RIP does not. The paper extends both by also allowing the AR(1) persistence parameter rho to vary across individuals (rho_i), yielding an empirically more general earnings process.

Earnings persistence (rho_i): The individual-specific autoregressive coefficient in the lifecycle earnings process. High rho_i means earnings shocks last longer, increasing earnings risk, reducing the household’s ability to smooth consumption, and strengthening precautionary savings motives. The paper finds evidence that rho_i varies meaningfully across U.S. households in the PSID.

Identification of Time-Inconsistent Models: The Case of Insecticide-Treated Nets

Mon, 01 Jan 0001 00:00:00 +0000

This paper addresses two related problems: the formal identification of time-inconsistent preferences in dynamic discrete choice models with unobserved heterogeneous types, and the structural estimation of those preferences using data from a health intervention in rural Orissa, India. The identification challenge is fundamental — even the standard exponential discount factor delta is generically not identified in dynamic choice models (Rust 1994; Magnac and Thesmar 2002), and this non-identification extends a fortiori to the hyperbolic (beta, delta) parameterization. The paper’s first contribution is constructing identification conditions that overcome these results through two exclusion restrictions: a variable z that affects utility only through the perceived value of future states (played in the application by elicited beliefs about state evolution), and a variable r that acts as an imperfect signal of agent type but is uninformative about choices conditional on type.

The general model accommodates a finite but unknown number of agent types — time-consistent (beta=1), time-inconsistent naive (beta<1, unaware of future present-bias), and time-inconsistent sophisticated (beta<1, aware of future present-bias) — as well as sub-types within each class. The paper proceeds in four identification steps when types are unobserved: identifying the total number of types (via the rank of an observable matrix), recovering type-specific choice probabilities, assigning type identities, and recovering preference parameters. For time-consistent and sophisticated agents, both beta and delta are point-identified. For naive agents, the parameters are set-identified in general, with point identification available under a monotonicity condition (Assumption 14) or by imposing a common exponential discount factor across types (Assumption 15).

The empirical application studies demand for insecticide-treated nets (ITNs) and their periodic retreatment — a health-protective technology with low up-front cost but substantial future benefits — among households in malarious areas of rural Orissa. A key design feature is that households were offered either a standard ITN contract (with the option to purchase retreatment later) or a commitment contract bundling two consecutive retreatments, allowing the commitment product choice to serve as a noisy type signal r. Elicited beliefs about future state variables serve as the excluded z variable.

The main empirical findings are: approximately 21% of the population is time-consistent, 49% are naive time-inconsistent, and 30% are sophisticated time-inconsistent — so time-inconsistent agents account for approximately 79% of the sample. The preferred estimates of the hyperbolic parameter beta are 0.16 for naive agents and 0.08 for sophisticated agents, indicating substantial present-bias in both groups. These estimates of the population type distribution and type-specific beta parameters are described as new to the literature.

A counterfactual exercise quantifies the welfare cost of present-bias: the median undiscounted additional expected total cost of malaria during the study period attributable to under-investment in ITNs exceeds the price of a treated net by a factor of approximately six. However, because time-inconsistent households heavily discount future malaria costs, the discounted total costs of malaria are low for many inconsistent agents relative to the ITN price, explaining low demand from the agents’ own subjective perspective. The paper also finds that commitment products are not disproportionately chosen by sophisticated agents — take-up of the commitment contract is actually higher among naive households — contradicting the deterministic mapping from commitment product purchase to sophistication that is commonly assumed in the literature. Finally, differences in per-period utilities across agent types exist but are not substantively important in explaining differential outcomes in the sample.

Q: What is the core identification problem the paper addresses, and why is it hard? A: Even the standard exponential discount factor delta is generically not identified in dynamic discrete choice models (Rust 1994; Magnac and Thesmar 2002). This non-identification extends a fortiori to both beta and delta in the hyperbolic (beta, delta) model. When agents are also heterogeneous in unobserved type, the additional problem of identifying the population distribution of types — itself a key policy parameter — must be solved jointly with preference identification.

Q: What two exclusion restrictions provide the key identifying variation? A: The first restriction is a variable z that affects utility only via the perceived value of future states but not per-period utility (Assumption 3); in the application this is played by elicited subjective beliefs about future state evolution. The second is a variable r that predicts agent type but, conditional on type and observables, provides no additional information about choices (Assumption 16); in the application r includes elicited time-preference indicators and the choice of the commitment versus standard ITN contract.

Q: Why does the paper require at least three periods? A: Three periods are the minimum required to capture the notions of time-inconsistency studied here: with only two periods, no time-inconsistency problem would arise. Three periods allow the researcher to separately observe how an agent plans in period 1, how the agent actually behaves in period 2 (potentially deviating from the period-1 plan), and how the agent behaves in the terminal period 3 where the problem reduces to a static discrete choice.

Q: What is point-identified versus set-identified across agent types? A: For time-consistent agents, all per-period utilities and the (single) discount factor delta are point-identified. For sophisticated agents, both beta and delta are separately point-identified under the rank conditions in Assumptions 10-11. For naive agents, the parameters are in general only set-identified (Lemma 4 provides sharp bounds); point identification holds under either a monotonicity condition (Assumption 14) or the assumption that naive and sophisticated agents share the same exponential discount factor (Assumption 15).

Q: How does the paper identify the total number of types in the population? A: The number of types equals the rank of a directly identified matrix P formed from the joint distribution of actions and states in adjacent time periods (Proposition 1). The rank provides a lower bound in general and equals the true number of types when the state space is sufficiently rich and type-specific choice probabilities vary sufficiently across the state space (Assumptions 17 and 19).

Q: How does the paper distinguish naive from sophisticated agents among the identified type-specific choice probabilities? A: A key diagnostic is the function delta_hat_tau(x2,z2), which compares an agent’s period-1 view of the future against what would be expected given period 2-3 choices. For time-consistent and sophisticated agents, this function is constant across the state space (x2,z2); for naive agents it varies across the state space (Lemma 7, Proposition 2). This variation arises because naive agents incorrectly anticipate their future behavior in period 1, generating a wedge between planned and actual continuation values that shifts with the state.

Q: What fraction of the sample is time-inconsistent, and what are the estimated beta parameters? A: Approximately 79% of the sample is time-inconsistent: 49% are naive and 30% are sophisticated. The preferred estimates of the hyperbolic (present-bias) parameter beta are 0.16 for naive agents and 0.08 for sophisticated agents. Both estimates indicate substantial present-bias. The paper states that these estimates of the population type distribution and the type-specific beta values are new to the literature.

Q: What is the welfare cost of present-bias in terms of malaria risk? A: Present-bias leads to lower ITN purchases and fewer retreatments, which increases the likelihood of contracting malaria. The median undiscounted additional expected total cost of malaria during the study period attributable to under-investment in ITNs exceeds the price of a treated net by a factor of approximately six. However, because inconsistent agents heavily discount future health costs, the discounted total costs of malaria are low relative to the ITN price for many such agents, which explains low demand from the agents’ own subjective perspective despite large social costs.

Q: What does the paper find about commitment products and agent sophistication? A: The commitment contract — bundling two consecutive retreatments — was designed to appeal to sophisticated present-biased agents who anticipate their future self-control problems. Contrary to the deterministic mapping from commitment product purchase to agent sophistication commonly assumed in the literature, take-up of the commitment contract is actually higher among naive households than sophisticated ones. The paper argues this is possible because the model allows commitment product choice to only imperfectly predict type, enabling a richer analysis than prior work that rules out type heterogeneity by assumption.

Q: Are differences in per-period utilities across types an important alternative explanation for observed behavior? A: Per-period utilities do vary across agent types, but the paper finds they are not substantively important in explaining differential outcomes in the sample. This finding supports the interpretation that time-inconsistent preferences — rather than heterogeneity in static preferences over states — are the primary driver of the behavioral differences observed across agent types in this context.

Q: What is the role of elicited beliefs in the identification strategy? A: Elicited beliefs about the future evolution of state variables serve as the excluded variable z that shifts the forward-looking component of the value function while leaving per-period utility unchanged. The use of expectational data, as advocated by Manski (2004), provides a natural and interpretable source of identifying variation for the discount parameters. The paper argues that this plausible exclusion restriction contributes to the encouraging Monte Carlo simulation results relative to other work in the identification literature.

Q: What happens to identification under partial sophistication? A: When agents are partially sophisticated — aware of some but not all of their future present-bias, so that beta_tilde in [beta, 1] rather than exactly equal to beta or 1 — the three time-preference parameters (delta, beta, beta_tilde) are not point-identified in general (Proposition 4 provides a set identification result). Point identification requires that the exponential discount factor delta be identified separately. The paper shows that partial and complete sophistication can be distinguished from time-consistency by whether the function delta_hat varies across the state space, and partially sophisticated types can be distinguished from fully sophisticated types under an additional variability condition (Assumption 23, Proposition 3).

Hyperbolic (beta-delta) discounting: A model of time-inconsistent preferences in which future utility at time s discounted from time t carries the factor beta*delta^(s-t), where beta<1 introduces an additional present-bias relative to pure exponential discounting. The parameter beta governs the wedge between the discount rate applied to immediate versus purely future tradeoffs; delta governs the intertemporal rate of substitution between any two future periods.

Sophisticated vs. naive agents: Both types are time-inconsistent (beta<1) and both are aware of their current present-bias. Sophisticated agents (tau_S) also correctly anticipate the extent of their future present-bias (beta_tilde = beta), while naive agents (tau_N) incorrectly believe their future self will behave as if beta_tilde = 1. This difference in beliefs about future behavior drives distinct choice dynamics across the three periods, providing the key observable variation used to distinguish the two types.

Exclusion restriction (z variable): A state variable that enters the transition probabilities and thus the value of future states but does not enter the current per-period utility function (Assumption 3). Variation in z shifts the forward-looking component of the Bellman equation while holding current utility fixed, providing the identifying variation needed to separately recover discount parameters from per-period utility parameters.

Type indicator / type proxy (r): An observed variable that is informative about an agent’s time-preference type but, conditional on type and other observables, provides no additional information about choices (Assumption 16). In the application, r includes elicited time-preference indicators and whether the agent chose the commitment versus standard ITN contract. Critically, the mapping from r to type is imperfect, so r does not directly reveal type for each individual.

Conditional choice probability (CCP) inversion: Following Hotz and Miller (1993), the type-specific conditional choice probabilities P_tau(a_t|x_t, z_t) — directly identified from data given type — can be inverted to recover per-period utility differences and combinations of discount parameters without solving the full dynamic programming problem. This approach underpins the constructive identification arguments throughout the paper.

Commitment contract: A product design in which two consecutive ITN retreatments are bundled at purchase, intended to mitigate the time-inconsistency problem by removing the future self-control decision about retreatment. The commitment contract is theoretically predicted to be preferred by sophisticated present-biased agents; the paper finds this prediction fails empirically, with naive households showing higher take-up.

Present-bias welfare cost: The undiscounted additional expected total cost of malaria attributable to under-investment in ITNs driven by present-bias. The paper estimates this cost exceeds the price of a treated net by a factor of approximately six at the median, capturing the gap between the social planner’s valuation of ITN adoption and the discounted valuation of time-inconsistent agents.

Income Inequality and Job Creation

Mon, 01 Jan 0001 00:00:00 +0000

The paper establishes a causal link from rising top income shares to reduced net job creation at small firms, working through a bank funding channel rooted in non-homothetic household portfolio allocation: because high-income households hold a smaller fraction of financial wealth in bank deposits (less than one-fifth for the top decile versus two-thirds for the bottom quintile, per the Survey of Consumer Finance), a redistribution of income toward top earners shifts aggregate saving away from deposits toward stocks and bonds. Banks must raise deposit rates to retain funding, which passes through to loan rates; since small, informationally-opaque firms depend disproportionately on bank credit while large firms have direct capital-market access, higher loan rates compress small firms’ net job creation relative to large firms. Using U.S. state-level panel data from 1981 to 2015, a shift-share instrumental variable, and a quantitative general equilibrium model, the paper documents this channel and finds it accounts for 13% of the 4.97 percentage-point rise in large-firm employment share and between 7.5% and 15% of the decline in the labor share since 1980.

Motivating facts (Section 2):

The U.S. net job creation rate of small firms (1–499 employees) declined from roughly +4% in 1980 to near 0% by 2015 and co-moves strongly with the top 10% income share (Figure 1a), suggesting a systematic relationship
SCF data show that the deposit share of financial wealth falls monotonically with income: bottom quintile (Q1) ≈ 65–70%; middle quintile ≈ 45%; top decile < 20% (Figure 2a). Non-financial wealth and stocks/bonds rise sharply with income
FDIC data show deposits account for 93% of total liabilities for the average bank and 75% of total liabilities on aggregate (Figure 2b); average bank raises 98% of deposits in its headquarters state (capital-weighted: 89%), so local deposit supply directly constrains local bank credit

Empirical specification (Section 3): Panel regression at the state–firm-size–year level, 47 states, 1981–2015, 16,435 observations. Dependent variable: net job creation rate (JCR − JDR). Key regressor: interaction of the top 10% income share with a “small firm” dummy (firms 1–499 vs. 500+). Regression includes state–firm-size fixed effects and state–time fixed effects, the latter absorbing all time-varying unobservable state-level factors common to firms of different sizes (e.g., globalization, technology). Identification via a pre-determined share IV: each state’s top 10% income share in 1970 (ten years before the sample) interacted with the leave-one-out national trend in top income shares — exploiting cross-state variation in sensitivity to the aggregate national trend while isolating it from local cyclical conditions.

Empirical results (Table 1, Table 2):

IV estimate: a 10 percentage-point rise in the top 10% income share reduces the relative net job creation rate of small firms by 1.2 percentage points (Table 1, col. 3)
Extensive margin (entry, exit, private-to-public transitions): accounts for approximately 20% of the 1.2pp effect (Table 1, col. 4)
One standard deviation higher top income share (5.4pp) → 0.7pp lower small-firm net JCR (Figure 1b, binned scatter OLS preview)
Counterfactual: had the U.S. top 10% income share remained at its 1980 level (instead of rising ~16pp from 34.5% to 50.5%), small firms’ net job creation rate would be 1.9 percentage points higher — more than 50% above its 2015 level
Bank-level regressions (Table 2): rising top income shares in a bank’s headquarters state lead to higher deposit rates and lower total deposit volumes — consistent with banks raising rates to retain a declining deposit supply

Model (Section 4): General equilibrium model with two types of households and two types of firms. Households differ by income group (high, H, and low, L), each endowed with heterogeneous productivities {si,χ}; households choose consumption, labor supply, and portfolio allocation between bank deposits (providing liquidity services captured by a CES deposit utility term ψd·η) and direct capital investment in public firms. Non-homotheticity: the deposit utility weight is calibrated so high-income households hold fewer deposits per unit of wealth. Firms are either public (large, direct capital-market access, production function with capital share θ and returns to scale γ) or private (small, bank-dependent; labor-only production with bank working capital constraint ϕ̃ governing the loan demand; entry/exit governed by stochastic fixed cost f̃ ~ U[0,f̃max] and a cost of going public κ ~ U[0,κ̃max]). Banks intermediate deposits into loans at a fixed cost, implying a zero-profit loan rate above the deposit rate.

Calibration (Table 3): Two panels:

Panel (a) externally fixed: capital depreciation rate (NIPA), mean US stock market return = 1.08, top 10% income share target = 34.6% (initial, Frank 2009 data), deposit rate = 4% (national average)
Panel (b) internally calibrated to BDS and SCF (early 1980s):
- Labor supply to public firms = 46.9%; private firms = 53.1% (BDS baseline)
- Labor demand to public firms = 46.9%; private firms = 53.1% (matched exactly)
- Deposit share of Q3 household = 0.45; top 10% deposit share = 0.22 (SCF)
- Household discount factor β = 0.9182; deposit utility scale ψd = 0.0632; deposit utility elasticity η = 2.6096
- Capital share in public firms θ; returns to scale γ set to match labor demand targets
- Firm productivity SD σz = 0.0315; bank dependence ϕ̃ and fixed cost bound f̃max matched to Table 1 empirical estimates (intensive and extensive margin); public-share cost bound κ̃max matched to share of firms >500 employees (BDS)

GE experiment (Section 6): Top 10% income share raised permanently from 34.5% to 50.5%, matching Frank (2009) data evolution, via lump-sum transfers from low- to high-income households (holding average income constant to isolate the portfolio reallocation channel). Key aggregate outcomes (Figure 3):

Aggregate deposits fall by more than 2%; savings flow into public firm capital, which rises 2% — the portfolio reallocation effect in levels
Deposit rate rises 0.4pp; loan rate rises 0.7pp; public firm capital return falls 0.14pp — consistent with bank-level empirical estimates
Private firm employment falls ~2%; public firm employment rises ~1%; aggregate employment falls modestly
Private firm employment share falls 0.64 percentage points — the channel explains 13% of the actual 4.97pp BDS decline in employment at firms below 500 employees (1980–2015)
Around one-fifth of the employment share decline comes from the extensive margin (private firm exit and transitions to public status), matching the empirical ratio
Labor share falls 0.3pp, explained by public firms growing relatively larger and being more capital-intensive; this accounts for 7.5% to 15% of the observed 2–4pp decline in the US labor share
Aggregate output falls 0.3%, driven by resource reallocation: private firms have marginal product of labor roughly one-sixth higher than public firms (consistent with the higher small-firm net JCR coefficient), so shifting employment to public firms suppresses aggregate productivity

Welfare effects (Section 6.2, Figure 4): The top 10% experience an increase in consumption-equivalent welfare; bottom 90% experience a decrease. The full model amplifies both effects relative to a counterfactual model with fixed portfolio shares: portfolio reallocation raises top-earner welfare by an additional ~1% (consumption equivalent) relative to the fixed-share benchmark and lowers bottom-earner welfare by ~1% — because in the full model, private firm wages fall (loan rate rise reduces labor demand) while in the fixed-share benchmark private firm wages rise (tops save more deposits, lowering loan rates). Ignoring portfolio heterogeneity thus significantly understates the welfare consequences of income redistribution.

Scope conditions: The mechanism operates through portfolio reallocation only; the paper holds average income constant (lump-sum redistribution) to isolate the channel, abstracting from any direct effects of rising incomes on aggregate savings rates. The IV exploits state-level variation in top income shares; cross-state spillovers in bank credit markets would attenuate estimated coefficients. The model assumes banks cannot replace lost deposits one-for-one with non-deposit liabilities, consistent with institutional frictions documented in the banking literature (Stein, 1998; Hanson et al., 2015). The analysis covers pre-tax income shares; post-tax redistribution through the tax code would dampen the mechanism.

In depth

Q1. Why does the portfolio composition of saving matter more than the aggregate savings rate?

The key non-homotheticity is in the composition of saving, not the level: high-income households allocate less than one-fifth of financial wealth to bank deposits while low-income households allocate two-thirds; as income shifts to the top, total deposits decline even if aggregate saving rises modestly. Banks cannot substitute deposit funding with non-deposit liabilities without cost — deposits provide cheap, stable funding because of their unique liquidity and monitoring properties (Stein, 1998; Hanson et al., 2015). An increase in the deposit rate is thus the equilibrating mechanism: banks must bid deposits back from higher-return assets, and the higher funding cost passes through to loan rates.

Q2. Why are small firms disproportionately harmed by higher loan rates?

Small, informationally-opaque firms rely on bank credit for external finance — 92% of small firms in the 1993 National Survey of Small Business Finances use bank loans — while large public firms can raise equity and bonds directly, bypassing banks entirely. When loan rates rise, small firms face a tighter credit constraint on their working capital and fixed costs of operation; the higher loan rate simultaneously reduces their demand for bank credit and raises the value of exiting or transitioning to public status (reducing the private-firm fixed cost burden). Large firms, by contrast, experience lower financing costs as the capital return falls and equity markets absorb more saving — amplifying the relative job creation gap.

The IV uses each state’s top 10% income share in 1970 — ten years before the sample begins, when income shares were flat nationally — interacted with the leave-one-out national trend; any factor driving both job creation outcomes and income inequality in a state would need to have affected firms of different sizes within that state in the same direction as the national trend, while also having had no such effect in all other states. The instrument’s validity rests on: (i) national income share trends after 1980 being driven by aggregate forces (technology, globalization) exogenous to any single state’s labor market; (ii) the pre-1980 period showing no systematic co-movement between state income shares and subsequent employment trends; and (iii) robustness to excluding industries that account for a large share of a state’s employment (Table OA4).

Q4. What explains the aggregate output decline when private firms have higher marginal products?

The output decline of 0.3% arises because the reallocation from private (higher marginal product) to public (lower marginal product) firms outweighs the positive capital accumulation effect: as more saving flows into public firm equity/capital, output would rise, all else equal — but the capital stock increase is modest and aggregate savings rise only slightly, so the dominant effect is misallocation. The marginal product gap between private and public firms is not an assumption of the model but a calibration consequence: matching the empirical estimate that small firms’ net JCR responds more to loan rate changes (Table 1) requires their marginal product to be higher, generating the misallocation loss when resources shift toward large firms.

Q5. How does rising inequality amplify its own effect through welfare and further portfolio reallocation?

In the full model with heterogeneous portfolios, the redistribution from low- to high-income households directly reduces aggregate deposits (because the recipients hold fewer deposits per dollar), which raises deposit and loan rates, which lowers wages at private firms, which further reduces low-income households’ labor income. This GE feedback loop — portfolio composition → bank rates → wages → income distribution → portfolio composition — amplifies the initial redistribution effect by approximately 1 percentage point of consumption-equivalent welfare compared to a model in which households are forced to hold fixed portfolio shares. In the fixed-portfolio model, tops invest more in deposits when they receive transfers, partially offsetting the deposit supply decline, and private firm wages rise — the opposite of the full model.

Q6. What fraction of US macroeconomic trends since 1980 can the channel explain?

The channel accounts for 13% of the 4.97pp rise in large-firm employment share, 7.5–15% of the 2–4pp fall in the aggregate labor share, and a 0.3% output loss from resource misallocation — meaningful but partial contributions to trends that are multi-causal. The partial contributions reflect that rising income inequality is one of several forces driving these trends (technology adoption, trade, market concentration, capital-skill complementarity); the paper explicitly abstracts from these other forces by using lump-sum transfers that hold average income constant, isolating the portfolio reallocation channel alone.

Q7. What happens to firm entry and exit under rising inequality?

A higher loan rate raises the effective cost of operating as a private firm (working capital is more expensive), reducing the threshold productivity level below which private firms exit and raising the threshold above which private firms find it worthwhile to incur the IPO-type cost of going public; both margins reduce the number of private firms in equilibrium, consistent with declining business dynamism. The model implies approximately one-fifth of the employment share decline at small firms comes from this extensive margin — closely matching the data decomposition from the BDS — and the public firm share rises by 0.003pp, consistent with the small but positive trend in the share of large-firm establishments observed in the data.

FDIC data show deposits represent 93% of average bank liabilities and 75% of aggregate bank liabilities; banks rely on their headquarters-state deposit base for the vast majority of funding because regulatory and institutional frictions constrain inter-state deposit gathering — even the four largest US banks (JP Morgan, Citi, Wells Fargo, Bank of America) raise over 70% of deposits in their headquarters state. The literature (Stein, 1998; Jakab and Kumhof, 2015) establishes that deposits provide uniquely stable, cheap funding that cannot be replaced at equivalent cost by wholesale liabilities or interbank borrowing; any substitution requires costly premium over the deposit rate, implying the attenuation bias if anything understates the true causal effect on loan rates.

Key concepts

non-homothetic deposit preference : the empirical regularity that the share of financial wealth allocated to bank deposits declines with income — two-thirds for the bottom quintile, under one-fifth for the top decile; this non-homotheticity means that a mean-preserving income redistribution toward top earners reduces the aggregate deposit supply relative to total saving, the paper’s foundational portfolio channel.

pre-determined share IV : the paper’s instrumental variable for state-level top income shares: each state’s 1970 top 10% income share interacted with the leave-one-out national trend in top 10% shares; identifies causal effects by exploiting differential state sensitivity to national inequality trends, purged of local cyclical factors and large-firm wage premia.

private versus public firm : the model’s key firm heterogeneity; private firms are small, bank-dependent (working capital constrained), and pay fixed operating costs; public firms are large, equity-financed, and face no bank credit constraint. The intensive-margin effect of higher inequality (rising loan rates) and extensive-margin effect (higher exit rates, more IPO transitions) both compress the private firm employment share.

deposit rate pass-through : the mechanism by which a decline in aggregate deposit supply forces banks to raise deposit rates to retain funds; the higher deposit rate is passed through to loan rates via the bank’s zero-profit condition, raising the cost of credit for bank-dependent private firms by approximately twice the deposit rate increase (0.7pp loan rate rise for 0.4pp deposit rate rise in the model).

business dynamism channel : the extensive margin of the paper’s mechanism — rising top income shares increase loan rates, which increase private firm exit rates and the rate of private-to-public firm transitions, reducing firm entry and contributing to documented trends of falling startup rates and declining business dynamism in the US since 1980.

Inference Based on Time-Varying SVARs Identified with Sign Restrictions

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question. The paper asks how to conduct valid Bayesian inference in time-varying structural vector autoregressions (SVARs) identified with sign restrictions, a setting in which existing algorithms are shown to be theoretically flawed. As an empirical illustration, the authors use the new framework to examine three questions about the 2022–2023 Federal Reserve tightening cycle: (i) how did the Fed respond to the state of the economy; (ii) how would more dovish or hawkish stances have fared; and (iii) was the Fed behind the curve in 2021, and at what cost?

Methodology. The paper defines a class of rotation-invariant time-varying SVARs, building on Bognanni (2018). A model belongs to this class when its prior over sequences of structural parameters is invariant to orthogonal transformations of those sequences—i.e., it assigns equal prior density to all observationally equivalent structural parameter sequences (Proposition 1 establishes that observational equivalence corresponds exactly to orthogonal rotation of the sequence). The authors prove an if-and-only-if characterization (Proposition 2): a prior belongs to this class if and only if the induced prior over sequences of orthogonal matrices is uniform and independent of the time-varying reduced-form parameters.

A specific member of this class, the Random Correlations SVAR (RC-SVAR), is constructed by combining a prior over time-varying reduced-form parameters based on Archakov and Hansen’s (2021) parametrization of correlation matrices with a uniform prior over sequences of orthogonal matrices. The RC-SVAR is preferred over alternatives (Primiceri 2005’s decomposition, which is order-dependent; Bognanni’s 2018 discounted Wishart model, whose marginal likelihood significantly underperforms) because, for the type of empirical applications considered, it generally implies a higher log-predictive score than most orderings of the Primiceri (2005) model.

The authors introduce three algorithms. Algorithm 1 (simple acceptance sampling) is theoretically correct but computationally infeasible when sign restrictions span many periods because the probability of satisfying all restrictions simultaneously converges to zero as sample length T grows. Algorithm 2, the current approach in the literature (Baumeister and Peersman 2013; Bognanni 2018; Debortoli, Galí and Gambetti 2020), draws orthogonal matrices period-by-period from the sign-restriction-truncated uniform distribution; the authors show this does not draw from the correct target posterior because the resulting prior over orthogonal matrices is not independent of the reduced-form parameters and therefore the prior does not satisfy the rotation-invariance condition. Algorithm 3, the paper’s contribution, uses a Gibbs sampler that incorporates the Particle Gibbs with Ancestor Sampling (PGAS) method of Lindsten, Jordan and Schon (2014) to draw sequentially from the correct target posterior conditional on sign restrictions over an arbitrary number of periods.

An important additional contribution is the allowance for time-varying sign restrictions—restrictions that are imposed only in selected periods—enabling researchers to tailor identification to institutional knowledge about when particular restrictions are economically appropriate.

Data and Empirical Application. The RC-SVAR is estimated at a quarterly frequency with five variables: output growth (log difference of real GDP), core inflation (log difference of core PCE price index), the federal funds rate, money growth (log difference of M2), and the Moody’s Baa corporate bond yield relative to the 10-year Treasury yield (credit spread). The sample runs from 1959:Q1 to 2023:Q2, with a constant and two lags (n=5, p=2, m=11). Four independent MCMC chains of 20,000 draws are used, keeping every tenth draw after discarding the first 2,500; 1,800 particles approximate the reduced-form posterior and 3,600 particles approximate the posterior of the orthogonal matrices.

Main Findings. Decomposing the unexpected change in the federal funds rate from 2022:Q2 to 2023:Q2 into contributions from the predictable component, the systematic monetary policy response to non-monetary-policy shocks, and pure monetary policy shocks, the authors find that the lion’s share of the unpredictable rate increase was a systematic response to non-monetary policy shocks. Monetary policy shocks contributed about 100 basis points of the unexpected change in the federal funds rate by 2023:Q2 (out of roughly 4.99 percentage points of cumulative actual funds rate).

In the Dovish Fed counterfactual—where the response of the federal funds rate to contemporaneous inflation is halved for the first quarter of 2022—the economy would have marginally overheated, with inflation running persistently above 5 percent. In the Hawkish Fed counterfactual—where the response to inflation is doubled—inflation would have quickly declined at a small output cost: focusing on posterior medians, real GDP in 2023:Q2 would have been about 0.7 percent lower than in the data, though the lower envelope of the 68 percent probability bands indicates the output cost could have been as large as 3.1 percent.

Regarding the “behind the curve” question, the model finds evidence that the Fed was accommodative in 2021 (expansionary monetary policy shocks in that period), consistent with Summers (2021b). However, monetary policy shocks contributed only about 0.6 percentage points to annualized core inflation during 2021:Q2–2021:Q4 on a cumulative basis; the larger and dominant source of the unexpected inflation surge was non-monetary policy shocks. A comparison of the RC-SVAR with a constant-parameter SVAR identified only by Restriction 1 (Uhlig 2005) shows substantively different conclusions: the constant-parameter model attributes the unexpected increase in the federal funds rate to shocks that affect money growth and credit spreads, without a clear connection to the real economy, whereas the RC-SVAR links the rate increases to shocks that made the economy run hotter.

In depth

Q1. What is the fundamental theoretical flaw in existing algorithms for time-varying SVARs identified with sign restrictions, and why does it matter?

Existing algorithms (e.g., Baumeister and Peersman 2013; Bognanni 2018; Debortoli, Galí and Gambetti 2020) draw orthogonal matrices period-by-period from the uniform distribution restricted to those matrices satisfying the sign restrictions at each t. This construction implicitly defines a marginal density for the orthogonal matrices conditional on the reduced-form parameters that is not uniform: it is proportional to the reciprocal of the volume of the sign-restriction-satisfying subset of the orthogonal group, which depends on the reduced-form parameters. Consequently, the prior over structural parameters implied by these algorithms does not assign equal density to observationally equivalent sequences of structural parameters, violating Proposition 2’s necessary and sufficient condition. The resulting posteriors are therefore not correctly targeted to the desired posterior, meaning inference is distorted in a way that cannot be corrected by importance reweighting without prohibitive computation.

Q2. What does Proposition 1 establish, and how does it generalize the constant-parameter case?

Proposition 1 proves that two sequences of time-varying structural parameters are observationally equivalent if and only if there exists a sequence of orthogonal matrices such that one sequence is obtained from the other by post-multiplying each period’s structural parameters by the corresponding orthogonal matrix. This directly mirrors the constant-parameter result in Rubio-Ramírez, Waggoner and Zha (2010) and Uhlig (2005), where a single orthogonal matrix produces observational equivalence. The extension to sequences is non-trivial because the law of motion couples parameter draws across time, but the likelihood’s separability across periods preserves the period-by-period orthogonal rotation structure.

Q3. What is Proposition 2, and what is its practical implication for constructing valid priors?

Proposition 2 states that the prior over time-varying structural parameters satisfies the rotation-invariance condition (Equation 3) if and only if the induced prior over the time-varying orthogonal reduced-form parameters does not depend on the sequence of orthogonal matrices—equivalently, the prior over (Qt) is uniform over the product of orthogonal groups and is independent of the reduced-form parameters (Bt, Σt). The practical implication is constructive: any prior over time-varying reduced-form parameters (Bt, Σt), combined with an independent uniform prior over sequences of orthogonal matrices, automatically produces a rotation-invariant SVAR. This means that widely-used priors for reduced-form time-varying VARs (Primiceri 2005, Bognanni 2018, the new RC prior) can all be adapted for structural analysis without modification, as long as the orthogonal matrices are drawn uniformly and independently of the reduced-form parameters.

Q4. Why do models with heteroskedastic structural shocks (identification via heteroskedasticity) not belong to the class of rotation-invariant SVARs?

In models identified through heteroskedasticity, the time-varying structural parameters take the form (A Ψt^{-1/2}, F Ψt^{-1/2}), where Ψt is a time-varying diagonal matrix. For any permissible sequence, post-multiplying by a non-diagonal orthogonal matrix at one period produces a sequence where the ratio of structural parameters across consecutive periods is not diagonal, which violates the permissibility constraint of those models. Thus, the class of rotation-invariant SVARs and models identified through heteroskedasticity are mutually exclusive when the heteroskedastic specification has constant impulse responses up to scale—a restriction that the authors note has been criticized as a potential weakness of the heteroskedasticity-based approach.

Q5. Why is the Random Correlations SVAR (RC-SVAR) chosen as the baseline, and how does it compare to alternatives?

The RC-SVAR uses the Archakov and Hansen (2021) parametrization of correlation matrices to define a prior over time-varying reduced-form parameters that is order-invariant (unlike Primiceri 2005, which produces n! different elements depending on variable ordering) and avoids the highly restrictive structure of Bognanni’s (2018) discounted Wishart model, which significantly underperforms in marginal likelihood. For the empirical applications considered, Arias, Rubio-Ramírez and Shin (2023) show the RC-SVAR generally achieves a higher log-predictive score than most orderings of the Primiceri (2005) model, motivating its use as the baseline. The theoretical results apply to any member of the rotation-invariant class, so the algorithm is not specific to the RC-SVAR.

Q6. Why are time-varying sign restrictions important, and how are they implemented in the monetary policy application?

Time-varying sign restrictions allow researchers to impose identification restrictions only in periods where those restrictions are economically appropriate, adhering to the principle “If you know it, impose it; if you do not know it, do not impose it” (Uhlig 2017). In the monetary policy application, Restriction 2 (which constrains the contemporaneous elasticities in the policy rule to plausible ranges, following Arias, Caldara and Rubio-Ramírez 2019) is not imposed during three exceptional periods: 1979:Q4–1982:Q4 (non-borrowed reserves targeting under Volcker), 2009:Q1–2015:Q3 (quantitative easing following the Great Recession), and 2020:Q2–2021:Q4 (QE and effective zero lower bound during COVID-19). Restriction 1 (sign restrictions on impulse responses to a monetary policy shock, following Uhlig 2005) is imposed throughout the entire sample.

Q7. What do the estimated contemporaneous elasticities reveal about how monetary policy has changed over time?

The model estimates show substantial time variation. The contemporaneous elasticity of the federal funds rate to output growth exhibits three peaks: during Arthur Burns’s chairmanship in 1974 (capturing the sharp rate cut during the 1974–1975 recession), during Volcker’s chairmanship in 1983–1984 (when annualized real GDP growth averaged 6.8 percent), and during Greenspan’s tenure in 2001 (when the federal funds rate fell from 6.4 percent in December 2000 to 1.8 percent by end-2001). Outside these peaks, the elasticity averaged about 0.1, implying a 0.1 percentage point rise in the annualized federal funds rate per 1 percentage point increase in annualized GDP growth. The elasticity to inflation averaged about 0.3 percentage points per 1 percentage point rise in annualized core inflation, with a range from above 0.5 in the early 1970s and early Volcker years down to about 0.15 during Yellen’s tenure. The elasticity to the credit spread moved from about −1.4 at the beginning of Burns’s tenure to −2.2 at the end of Nixon’s presidency, then declined through the mid-1970s to the Great Recession, and stood at about −1 by mid-2023.

Q8. What is the exact decomposition of the 2022–2023 tightening cycle into predictable, systematic non-monetary, and monetary policy shock components?

Table 1 from the paper shows the federal funds rate decomposition. In 2022:Q2, the predictable component was 0.27 percentage points, the unpredictable component due to systematic response to non-monetary shocks was 0.24 pp, and the unpredictable component due to monetary policy shocks was 0.26 pp, summing to 0.77 pp. By 2023:Q2, these were 1.70 pp (predictable), 2.25 pp (systematic/non-monetary), and 1.04 pp (MP shocks), totaling 4.99 pp. Thus, at the tightening cycle’s end in 2023:Q2, the systematic response to non-monetary shocks accounted for about two-thirds of the unpredictable component (2.25 / (2.25 + 1.04) ≈ 68 percent), consistent with the broader literature finding that most variation in policy instruments is driven by the systematic component of policy.

Q9. How do the Hawkish and Dovish Fed counterfactuals work, and what do they imply?

The Hawkish (Dovish) counterfactual replaces the estimated contemporaneous response to inflation in the policy rule with one that is twice (half) as large as the estimated response for the first quarter of 2022, then simulates history forward from 2022:Q2 under the modified rule. Under the Dovish Fed, the economy would have marginally overheated with output rising above CBO potential GDP estimates, and inflation would have run persistently above 5 percent. Under the Hawkish Fed, posterior medians show inflation quickly declining at a cost of about 0.7 percent of real GDP in 2023:Q2 relative to the data; the lower envelope of the 68 percent probability bands shows the output cost could have been as large as 3.1 percent. A parallel set of counterfactuals, designed to be robust to the Lucas critique by working through one-time monetary policy shocks rather than changes to the reaction function, yields broadly similar results.

Q10. What does the comparison with Romer and Romer (2023a) reveal about the model’s monetary policy shock series?

Romer and Romer (2023a) identify a contractionary monetary policy shock in July 2022 (2022:Q3) using a narrative approach. The RC-SVAR’s estimated monetary policy shock series is broadly consistent with this finding: the model detects a contractionary shock in 2022:Q3 and, like Romer and Romer, also finds some evidence of a contractionary shock in 2022:Q2 (though they characterized it as “signs but not definitive evidence”). Beyond the Romer-Romer estimation window, the RC-SVAR additionally finds evidence of an expansionary monetary policy shock in 2023:Q1, when the Fed decelerated the pace of rate increases from 50 to 25 basis points.

Q11. How does the RC-SVAR’s inference on the 2022–2023 tightening cycle differ from that of a constant-parameter SVAR identified only with Restriction 1?

Two salient differences emerge. First, through the lens of the constant-parameter SVAR, monetary policy shocks contribute insignificantly to unexpected output growth between 2022:Q2 and 2023:Q2; in fact, the posterior median output response to a contractionary monetary policy shock is positive in that model (consistent with Uhlig 2005’s finding), implying that the positive monetary policy shocks needed to explain the rate increase would propel rather than reduce output. In the RC-SVAR, the posterior median output response to a contractionary shock is negative, so contractionary monetary policy shocks worked to decelerate output against a backdrop of non-monetary shocks that made the economy run hotter. Second, in the constant-parameter SVAR, non-monetary policy shocks that drive the unexpected increase in the federal funds rate do not propagate through output or inflation, whereas in the RC-SVAR they do—yielding a much more coherent macroeconomic narrative for the tightening cycle.

Q12. What does the model find about whether the Fed was behind the curve in 2021, and what were the consequences?

The model’s 2021:Q1 forecasts predicted the federal funds rate would reach about 0.6 percent by end-2021, consistent with a view that rate normalization was already warranted. The actual federal funds rate remained at its effective lower bound through 2021:Q4, and the shock decomposition shows that the cumulative unexpected change in the funds rate during 2021:Q2–2021:Q4 was driven by expansionary monetary policy shocks—supporting the view that monetary policy was accommodative and the FOMC fell behind the curve. However, monetary policy shocks contributed only about 0.6 percentage points (annualized) to the unexpected increase in core inflation during this period; the dominant and larger source of the inflation surge was non-monetary policy shocks. The model therefore finds that the delay in tightening was not the primary driver of the 2021 inflation surge.

Q13. Do time-varying sign restrictions materially affect inference, as demonstrated in Section 6.8?

Yes. Comparing the baseline identification scheme (Restrictions 1 and 2, with Restriction 2 not imposed during exceptional periods) against an alternative scheme that imposes both restrictions throughout the entire sample reveals differences in the estimated monetary policy shocks, particularly in 2021:Q4. Under the alternative scheme, there was an expansionary monetary policy shock in 2021:Q4, while the baseline finds the shock was nearly centered around zero. Additionally, for 2021:Q2, the alternative scheme implies the contemporaneous output response to an expansionary monetary policy shock is more likely to have been positive, whereas the baseline scheme yields a different posterior distribution for this response. These differences illustrate that imposing or omitting restrictions in specific periods affects inference about structural shocks and impulse responses at economically important junctures.

Key Concepts

Rotation-Invariant Time-Varying SVAR: A class of time-varying SVAR models whose prior over sequences of structural parameters satisfies: for every permissible sequence of structural parameters and every sequence of orthogonal matrices, the orthogonally-rotated sequence is also permissible and receives the same prior density. This ensures the prior does not break the observational equivalence among structural parameter sequences related by orthogonal rotation, so that identification comes solely from the imposed restrictions.

Observational Equivalence in Time-Varying SVARs: Two sequences of time-varying structural parameters are observationally equivalent if and only if there exists a sequence of orthogonal matrices such that one sequence equals the other sequence post-multiplied period-by-period by the corresponding orthogonal matrix. This definition extends Rothenberg’s (1971) concept to the time-varying setting and directly implies the rotation-invariance restriction.

Random Correlations SVAR (RC-SVAR): A specific member of the rotation-invariant class constructed by using the Archakov and Hansen (2021) parametrization of correlation matrices to define the prior over time-varying reduced-form parameters, combined with a uniform prior over sequences of orthogonal matrices. The prior is order-invariant and, for the empirical applications considered, generally achieves higher log-predictive scores than the workhorse Primiceri (2005) model.

Time-Varying Sign Restrictions: Sign restrictions imposed only on selected time periods rather than uniformly across the sample, implemented by allowing the restriction function St() to differ across t (including the possibility that no restriction is imposed at some t). This allows researchers to tailor identification to periods in which the theoretical or institutional knowledge motivating the restriction is deemed applicable—e.g., imposing policy-rule contemporaneous restrictions only when the federal funds rate is the primary policy instrument.

Particle Gibbs with Ancestor Sampling (PGAS): The sequential Monte Carlo method (from Lindsten, Jordan and Schon 2014) used in the paper’s Algorithm 3 to draw the sequence of structural parameters At from its conditional posterior given the sign restrictions. PGAS conditions on the previous Gibbs draw of the structural parameter sequence to ensure an invariant distribution, which is the key property that makes the Gibbs sampler valid for drawing from the correct target posterior.

Systematic Component of Monetary Policy: In the paper’s structural monetary policy equation, the linear combination of contemporaneous endogenous variables (output growth, inflation, money growth, credit spread) that enters the federal funds rate equation, weighted by the contemporaneous elasticities ψ. It represents the portion of interest rate variation that is a predictable, rule-based response to economic conditions, as distinguished from the monetary policy shock (the residual).

Contemporaneous Elasticity: The coefficient ψi,t in the monetary policy equation measuring the response of the federal funds rate to a one-unit contemporaneous change in variable i at time t, defined directly in terms of the structural parameter matrix At. The paper’s time-varying framework allows these elasticities to evolve over the sample, revealing historically distinct episodes of how aggressively the Fed responded to output growth, inflation, money growth, and credit spreads.

Input Sourcing under Climate Risk: Evidence from U.S. Manufacturing Firms

Mon, 01 Jan 0001 00:00:00 +0000

Blaum, Esposito, and Heise study how supply chain risk — specifically, the risk of unexpected shipping delays caused by ocean weather conditions — affects U.S. manufacturing firms’ import sourcing decisions. The paper asks three related questions: Do weather-induced shipping delays harm firm performance? Do firms adapt their sourcing strategies ex ante in response to shipping time risk? And what are the aggregate welfare costs of heightened supply chain risk from climate change, geopolitical tensions, and port congestion?

The empirical foundation is the U.S. Census Bureau’s Longitudinal Firm Trade Transactions Database (LFTTD), covering the universe of U.S. import transactions from 1992 to 2016, merged with the Longitudinal Business Database and Annual Survey of Manufacturers for firm-level outcomes. For ocean shipments, the authors reconstruct vessel routes using vessel names, foreign port stops, and U.S. ports of entry, then map those routes to hourly wave height and direction data from NOAA’s WaveWatch III model at 0.5-degree resolution across more than 40,000 distinct maritime routes (period: 2011–2016 for weather data).

The identification strategy proceeds in two steps. First, observed shipping times are regressed on a rich set of fixed effects — supplier, product, route-month, vessel, buyer, relationship status — plus controls for shipping charges and weight, to strip out anticipated determinants of delivery time. Second, the residuals are projected onto realized wave height and direction along the vessel’s route to isolate the weather-induced, unexpected component of shipping time variation. The identifying assumption is that realized wave conditions along the entire multi-week ocean crossing are not predictable by importers at the time orders are placed, beyond seasonal patterns absorbed by route-month fixed effects. This assumption is supported by the literature on weather forecasting, which finds accuracy degrades sharply beyond seven days.

The paper’s first empirical result concerns the consequences of weather-induced delays. Defining an extreme delay as a weather-induced shipping time above the 95th percentile for a given product-route, the authors estimate that a one standard deviation increase in the share of input costs that are weather-delayed (2.66 percentage points) reduces firm sales by 6.5%, profits by 3.5%, and employment by 1.0% within the same year. These effects are estimated from panel regressions for 2011–2016, with importer, product, and year fixed effects. The magnitudes indicate that firms are typically unable to fully hedge supply chain disruptions through insurance or financial instruments.

The paper’s second empirical result concerns ex ante adaptation. Risk exposure is measured as the standard deviation of weather-induced shipping times over three-year rolling windows for each supplier-route-product combination, then aggregated to the importer-product-year level using pre-determined import shares as weights (Bartik shift-share). Moving from the 25th to the 75th percentile of this shipping risk distribution increases the number of routes used by 7.7% and the number of foreign suppliers by 4.9%, while reducing total import value by 5.1%, route concentration (HHI) by 4.6%, and supplier concentration (HHI) by 3.2%. The risk effect on imports is estimated conditional on average shipping time, indicating that uncertainty exerts an additional, independent negative effect on import demand beyond the level of delays.

To rationalize these findings, the authors build a quantitative general equilibrium model of importing with firm heterogeneity. Firms source domestic and foreign inputs; foreign input quality is reduced when delivery is late, and firms face uncertainty about shipping times when placing orders. Risk-neutral firms nonetheless face a concavity in expected revenues from monopolistic competition, so higher variance in input quality reduces expected profits. Firms can diversify by adding foreign suppliers (at a per-supplier fixed cost), and a key theoretical result is that a mean-preserving spread in supplier quality variance increases the optimal number of suppliers but, because the extensive-margin elasticity is less than one, total import value necessarily falls.

The calibrated model is used to evaluate three counterfactual scenarios. Ocean wave height volatility increased by 0.34% per year on average between 2011 and 2023; projecting this trend forward 50 years generates a climate change scenario. The Houthi attacks in the Red Sea caused rerouting that raised both the mean and variance of navigation time. Post-Covid port congestion (2021–2022) increased the variance of port waiting times. Across all three scenarios, U.S. real income falls by 0.4% to 1.33%, driven by firms substituting toward more expensive domestic inputs as they reduce exposure to risky foreign sourcing.

The sample scope is U.S. manufacturing importers using ocean shipping during 2011–2016 for the main empirical results (weather data period), with an extended robustness sample of 1992–2016 using residualized shipping time volatility. The study covers 43,080 origin-destination port pairs, 401,700 unique vessels, and approximately 35.8 million seaborne transactions.

Q: What is the paper’s core research question? A: The paper asks how supply chain risk — specifically, the risk of unexpected delays in ocean shipping caused by weather conditions — affects U.S. manufacturing firms’ import sourcing decisions and aggregate welfare. It examines both the disruption effects of realized delays and the ex ante adaptation of sourcing strategies to risk exposure, then quantifies aggregate costs through a calibrated general equilibrium model.

Q: What data sources underpin the empirical analysis? A: The primary dataset is the LFTTD, which covers the universe of U.S. import transactions from 1992 to 2016, recording importer and exporter identities, HS-10 product codes, values, quantities, shipping dates, vessel names, and port pairs. This is merged with the Longitudinal Business Database for employment and industry, and with Census of Manufactures and Annual Survey of Manufacturers for sales, material costs, and payroll. Weather data come from NOAA’s WaveWatch III model at hourly, 0.5-degree resolution for 2011–2016. Ocean routes are constructed using Eurostat’s SeaRoute program, covering over 40,000 distinct routes across approximately 10,500 route segments.

Q: How do the authors isolate the unexpected component of shipping time variation? A: They use a two-step residualization. In step one, observed log shipping times are regressed on supplier, product, route-month, vessel, buyer, and relationship-status fixed effects, plus controls for log shipping charges and log weight; the residuals capture variation not explained by anticipated factors. In step two, these residuals are projected onto realized average wave height and relative wave direction along the vessel’s route to extract the weather-induced component. The identifying assumption is that importers cannot forecast realized wave conditions beyond seasonal patterns when placing orders that initiate multi-week ocean crossings, consistent with evidence that weather forecasts lose accuracy beyond seven days and that ocean wave height is particularly hard to predict.

Q: What are the estimated effects of weather-induced shipping delays on firm performance? A: A one standard deviation increase in the share of input costs that are weather-delayed (2.66 percentage points) reduces firm sales by 6.5%, profits by 3.5%, and employment by 1.0% within the same year. Using a broader measure of residualized shipping time delays (not restricted to the weather-induced component) produces similar results: a one standard deviation increase reduces sales by 6%, profits by 3.2%, and employment by 0.9%. These effects are estimated from panel regressions for 2011–2016 with importer, product, and year fixed effects.

Q: How do firms adjust their sourcing strategies in response to higher shipping time risk? A: Moving from the 25th to the 75th percentile of the shipping risk distribution (a 61 log-point increase) raises the number of routes used by 7.7% and the number of foreign suppliers by 4.9%, while reducing route HHI by 4.6%, supplier HHI by 3.2%, and total import value by 5.1%. The margin of route diversification is larger than supplier diversification, consistent with shipping risk being determined primarily at the route level. Higher risk also increases the likelihood of switching to air freight by 1.0% over the same interquartile range.

Q: Does the risk effect on imports operate independently of the level of shipping times? A: Yes. The regressions of total import demand on risk exposure control for average shipping time, and the coefficient on risk remains negative and significant after this control. This indicates that the variance of shipping times has an independent negative effect on import demand beyond the first-moment effect of longer average delays.

Q: What is the theoretical mechanism through which shipping time risk reduces import demand? A: In the model, firms are risk-neutral but face monopolistically competitive output markets, which introduces curvature in the revenue function. Higher variance in input quality (stemming from unpredictable shipping times) reduces expected revenues even for risk-neutral firms. Firms can diversify by adding foreign suppliers at a per-supplier fixed cost, which reduces variance in average input quality. However, the elasticity of the optimal number of suppliers with respect to quality variance is less than one, so total import expenditure necessarily falls as variance rises — diversification is incomplete and firms substitute toward domestic inputs.

Q: What does Proposition 1 state about the extensive margin response to risk? A: Proposition 1 establishes that, under the condition that shipping time risk is small relative to expected revenues, a mean-preserving spread in the variance of supplier quality increases the optimal number of foreign suppliers. However, the elasticity of the optimal number of suppliers with respect to quality variance is strictly less than one, which implies that total import value necessarily falls whenever quality variance increases, regardless of the extensive margin diversification response.

Q: How is the calibration structured and what moments does it target? A: The model features firm heterogeneity in both productivity and shipping time risk (variance of delivery times). The calibration targets three sets of moments: the estimated effect of shipping time risk on the extensive margin of importing (number of suppliers), the negative association between firm sales and average shipping times (which disciplines the timeliness elasticity parameter tau), and the joint distribution of firm size and risk observed in the data — specifically, the empirical finding that larger importers are matched with safer (lower-risk) foreign suppliers, with a correlation of -0.12. The calibrated model replicates the key moments of shipping time risk and import demand.

Q: What are the three counterfactual scenarios and their aggregate welfare costs? A: (1) Climate change: ocean wave height volatility increased by 0.34% per year on average between 2011 and 2023; projecting this trend forward 50 years and passing the resulting increase in shipping time variance through the model. (2) Red Sea/Houthi attacks: re-routing around the Suez Canal raises both the mean and variance of navigation time. (3) Post-Covid port congestion: greater variability in port waiting times during 2021–2022. Across all three scenarios, U.S. real income falls by 0.4% to 1.33%, driven by firms substituting from cheaper foreign inputs toward more expensive domestic production to reduce risk exposure.

Q: What is the role of the shift-share (Bartik) instrument in the risk exposure measure? A: The exposure measure aggregates supplier-route-product level risk (standard deviation of weather-induced shipping times over three-year rolling windows) to the importer-product-year level using pre-determined import shares from the prior three years as weights. Using lagged shares rather than contemporaneous shares ensures that the weights are not endogenous to current sourcing decisions. This construction is standard in the Bartik shift-share literature and helps isolate variation in risk that is plausibly exogenous to the firm’s current sourcing choices.

Q: How do the authors handle the endogeneity concern that firms may select into riskier routes? A: The weather-induced component of shipping time variation is by construction driven by realized ocean conditions that are unpredictable at the time orders are placed. The residualization removes all fixed-effect variation associated with route, season, vessel, supplier, and buyer characteristics. Additionally, the shift-share construction uses pre-determined weights, so risk exposure does not mechanically reflect current sourcing decisions. The authors also show robustness using the longer 1992–2016 sample with residualized (rather than weather-specific) shipping time volatility, obtaining qualitatively and quantitatively similar results.

Q: What does the paper contribute relative to the literature on shipping times and trade? A: Prior work by Evans and Harrigan (2005) and Hummels and Schaur (2010, 2013) focused on the level of shipping times (the first moment) as a trade cost. This paper is the first to systematically study the variance of shipping times (the second moment) as an independent determinant of import demand and sourcing structure, both empirically and theoretically. The authors show that uncertainty around delivery times has negative effects on trade that are separate from the effects of longer average delays.

Q: What are the robustness checks reported for the main empirical results? A: For the effects of risk on sourcing behavior, the authors show that using residualized shipping time volatility over the longer 1992–2016 sample (rather than the weather-induced measure over 2011–2016) produces similar results: moving from the 25th to the 75th percentile increases routes by 6.6%, suppliers by 3.7%, decreases route HHI by 3.9%, and supplier HHI by 2.5%, while reducing total imports by 10.5%. For the effects of delays on firm performance, applying the same specification with residualized (not weather-induced) delay shares yields coefficients on sales, profits, and employment that are very close to the baseline estimates.

Q: What are the welfare implications for firms that cannot hedge through financial markets? A: The large negative effects of weather-induced delays on sales, profits, and employment — and the finding that firms respond by ex ante restructuring their supply chains rather than relying on insurance — indicate that financial hedging instruments are largely unavailable or insufficient for managing input delivery risk. This motivates the model’s assumption that firms must manage risk through sourcing diversification, which is costly because of per-supplier fixed costs and because it ultimately requires substituting toward more expensive domestic inputs.

Weather-induced unexpected shipping time: The component of shipping time variation explained by realized ocean wave height and direction along the vessel’s route, after removing all variation attributable to anticipated factors (route, season, vessel, supplier, buyer characteristics, shipping charges, weight). Interpreted as unexpected because multi-week ocean crossings begin before accurate weather forecasts are available.

Shipping time risk: Measured as the standard deviation of weather-induced residualized shipping times over three-year rolling windows for each foreign supplier-route-product combination. This captures the second moment (variance) of delivery time uncertainty, distinct from the first moment (average shipping time level).

Shift-share risk exposure: An importer-product-year level risk measure constructed as a weighted average of supplier-route-product level risk, using pre-determined import shares from the prior three years as weights. This Bartik-style construction ensures exposure weights are not endogenous to current sourcing decisions.

Timeliness elasticity (tau): A structural parameter in the model governing how rapidly input quality degrades when delivery is later than expected. Specifically, when a shipment arrives di days late, quality is reduced by the factor exp(-tau*(di - E[di])). Calibrated to match the observed negative association between firm sales and average shipping times in the data.

Extensive margin diversification: The response of firms to higher shipping time risk by increasing the number of foreign suppliers and shipping routes used for a given product, rather than increasing the volume sourced from existing suppliers. In the model and data, this margin is the primary channel through which firms hedge delivery risk.

Mean-preserving spread condition: The theoretical condition (Proposition 1) under which higher variance in supplier quality increases the optimal number of foreign suppliers. The condition requires that shipping time risk be small relative to expected revenues, so that the diversification benefit of adding suppliers (reducing variance in average quality) dominates the revenue-reducing effect of higher variance.

Per-supplier fixed cost: A fixed cost in the model that must be paid for each foreign supplier relationship maintained. This cost limits the extent of diversification, ensuring that firms cannot fully eliminate shipping time risk by adding arbitrarily many suppliers, and that higher risk raises (rather than eliminates) per-unit sourcing costs.

Insurer Risk and Public Risk-Sharing: Quantifying the Value of Reinsurance

Mon, 01 Jan 0001 00:00:00 +0000

Kim and Li study how publicly provided reinsurance affects insurer behavior and market outcomes in health insurance markets where firms face substantial cost uncertainty. The central question is whether standard expected-profit models—which predict that reinsurance reducing only cost volatility (not expected cost) should leave prices unchanged—miss an important mechanism: insurers internalizing the implicit financial cost of bearing claims uncertainty through “risk charges.”

The paper develops a stylized monopoly-insurer model in which the insurer’s objective includes both expected claims cost and a risk charge term L(S), where S is a risk measure (e.g., standard deviation of total claims). This yields a first-order condition in which effective marginal cost includes both standard expected claims cost and a marginal risk charge. The model predicts that public reinsurance acts through two distinct channels: (1) a cost subsidy—reimbursing a share of high-cost claims reduces expected cost; and (2) risk protection—reducing the variance of claims lowers the risk charge and thus effective marginal cost. When both channels operate, the model predicts pass-through of public reinsurance to premiums can exceed unity, in contrast to the standard less-than-one pass-through under market power.

Empirically, the authors use three primary data sources for the U.S. individual health insurance exchange market. NAIC Schedule S filings (2014–2023) provide transaction-level private reinsurance contracts, including ceded premiums, realized claims, and financial solvency measures. CMS Public Use Files and MLR reports provide plan-level premiums, enrollment, and claims. The Colorado All Payer Claims Database (CO APCD, 2014–2022) and Connect for Health Colorado administrative records (2015–2021) provide individual-level claims and insurance choices for structural analysis.

Descriptive evidence establishes that 62% of exchange insurers purchase private reinsurance despite average reinsurance markups of 1.54 (reinsurance margin of 0.54), and that smaller, less financially solvent insurers are disproportionate buyers—consistent with risk charges driving demand for risk protection even at above-actuarially-fair prices.

An event study exploiting staggered adoption of state-level public reinsurance programs finds that public reinsurance reduces premiums by approximately 14.5% on average (27% in Colorado Tiers 1–2, 46% in Tier 3), with a pass-through rate of 1.3—significantly greater than one (p = 0.037 one-sided). Public reinsurance reduces the probability of purchasing private reinsurance by 26 percentage points (a 42% reduction from baseline) and per-member private reinsurance expenditures by $19.5 (a 68% reduction from baseline). Premium and private reinsurance effects are larger for financially constrained insurers (RBC ratio below 3). No significant effects are found on insurer entry/exit, total medical expenses (ruling out moral hazard), or private reinsurance markups.

The structural model, estimated on the Colorado exchange for 2017–2020, finds that the risk charge coefficient for regional insurers averages rho = 0.25, implying regional insurers face 9.8% higher effective costs than national insurers due to risk charges and private reinsurance expenses. Risk charges account for at least half the premium-cost wedge for small regional insurers. Counterfactual decomposition of Colorado’s program shows the direct cost subsidy accounts for approximately 75% of equilibrium price reductions; risk protection and competition effects together account for the remaining 25%. In a bang-for-buck comparison, public reinsurance dominates premium subsidies of equal government expenditure by approximately 20–30%, because reinsurance uniquely reduces risk charges and enhances competition by reducing smaller regional insurers’ cost disadvantage.

Q: What is the core theoretical innovation of the paper? A: The paper adds a risk charge term L(S) to the standard expected-profit objective, where S is a risk measure of the insurer’s cost distribution. This makes the insurer behave “as if risk averse,” with effective marginal cost including both expected claims cost and a marginal risk charge that decreases with insured pool size due to risk pooling. When rho = 0, the model collapses to the standard monopoly case; when rho > 0, cost uncertainty directly inflates prices and creates a novel role for reinsurance even when reinsurance is actuarially fair priced.

Q: What are the two distinct mechanisms through which public reinsurance affects insurer pricing? A: The first is a cost subsidy: by reimbursing a portion of high-cost claims without requiring an actuarially fair premium upfront, public reinsurance lowers the insurer’s net expected cost. The second is risk protection: by providing ex-post payments for extreme health shocks, reinsurance reduces the variance of claims costs, lowering the risk charge component of effective marginal cost. Together, these channels can produce pass-through exceeding unity even under imperfect competition, where standard cost-subsidy pass-through is typically below one.

Q: What does Proposition 1 say about actuarially fair reinsurance (theta = 1)? A: Proposition 1(i) states that actuarially fair reinsurance—which does not alter net expected cost—still lowers the insurer’s price if and only if the insurer faces a risk charge (rho > 0). An insurer without risk charges is entirely unaffected by actuarially fair reinsurance. This result isolates the risk-protection channel as theoretically distinct from cost subsidization and establishes that pass-through exceeding one requires risk charges to be operative.

Q: Why would an insurer purchase costly private reinsurance (theta > 1)? A: Proposition 1(iii) shows that an insurer with no risk charge would never purchase private reinsurance with theta > 1, since it increases net expected cost with no offsetting benefit. An insurer facing a risk charge (rho > 0) may purchase private reinsurance because the risk-protection benefit—the reduction in cost variance and thus the risk charge—can outweigh the net cost increase. The paper documents that 62% of exchange insurers buy private reinsurance at an average markup of 1.54 (reinsurance margin 0.54), with smaller and financially weaker insurers more likely to purchase, consistent with this mechanism.

Q: How does the paper establish empirically that insurers face and internalize cost uncertainty? A: Three lines of evidence are presented. First, the CO APCD shows the claims distribution has a long right tail: the top 5% (1%) of consumers account for 68% (38%) of total expenses, and 2.5% of consumers exceed the $30,000 reinsurance threshold. Second, simulations show that with 1,000 enrollees, the probability that realized claims exceed expected costs by 25% is approximately 7%; even at 10,000 enrollees there is a 17% probability of exceeding expected costs by 5%. Third, in over 24% of insurer-year observations premium revenue falls short of realized claims costs, and the within-firm standard deviation of the claims-to-premium ratio is 0.15.

Q: What are the event study findings on premiums? A: Using staggered introduction of state-level public reinsurance programs, the event study finds premiums fell by 14.5% on average following program adoption. In Colorado specifically, Tiers 1 and 2 experienced 27% decreases and Tier 3 (highest reinsurance generosity) experienced a 46% decrease. The implied pass-through rate for 2020 is 1.3, meaning for every dollar the government spent on reinsurance, health insurance premiums fell by $1.30. A one-sided t-test rejects pass-through equal to one at p = 0.037.

Q: What are the event study findings on private reinsurance? A: Public reinsurance reduces the probability that an insurer purchases private reinsurance by 26 percentage points, a 42% decline from the pre-program baseline. Average per-member private reinsurance expenditures fall by $19.5, a 68% reduction from baseline. The substitution away from private reinsurance is consistent with the model prediction that public reinsurance displaces the demand for risk protection previously met by private markets, and reinforces the interpretation that risk management is a key driver of private reinsurance demand.

Q: Do financially constrained insurers respond differently to public reinsurance? A: Yes. The premium-reduction effect is significantly larger for insurers with RBC ratios below 3 (an additional interaction effect of -0.161 log points on top of the baseline -0.135). The reduction in per-member private reinsurance expenditures is also significantly larger for insurers with significant prior private reinsurance purchases (-$108.8 vs. baseline of -$19.5). This heterogeneity supports the hypothesis that the risk protection channel is more valuable for financially constrained insurers who face higher implicit costs of bearing risk.

Q: Does public reinsurance affect insurer entry/exit, moral hazard, or private reinsurance markups? A: The event study finds no statistically significant effect on market entry, total monthly medical expenses per enrollee, the probability that individual expenses exceed the reinsurance threshold (ruling out insurer moral hazard), or private reinsurance markups paid by primary insurers. These null results support the interpretation that premium reductions reflect reduced cost uncertainty rather than cost containment distortions, and that the competitive structure of the private reinsurance market is not directly altered by public programs.

Q: What are the structural estimates of risk charges? A: The estimated risk charge coefficient for regional insurers averages rho = 0.25. This implies that regional insurers incur, on average, 9.8% higher effective costs than national insurers (who are assumed not to face risk charges due to scale and diversification), stemming from both direct risk charges and private reinsurance expenses required to manage risk. Risk charges account for at least half the observed wedge between premiums and marginal claims costs for small regional insurers.

Q: How does the structural model decompose the impact of Colorado’s reinsurance program? A: Counterfactual analysis decomposes the equilibrium price reduction into three channels. The direct cost subsidy effect—reimbursing a share of high-cost claims between the $30,000 attachment point and $400,000 cap—accounts for approximately 75% of the price reduction. The risk protection effect (reduction in risk charges from lower portfolio variance) and the competition effect (smaller regional insurers facing lower cost disadvantages and competing more aggressively with national insurers) together account for the remaining 25% of the equilibrium price reduction.

Q: How does public reinsurance compare to premium subsidies in bang-for-buck terms? A: For equal government expenditure, public reinsurance is estimated to be approximately 20–30% more cost-effective than premium subsidies at reducing premiums. The advantage stems from two sources: reinsurance reduces risk charges, shifting down the marginal cost curve for regional insurers in a way demand-side premium subsidies do not; and reinsurance enhances competition by reducing the cost disadvantage of smaller regional insurers relative to national ones. The dominant effect is risk reduction rather than markup inflation, making reinsurance the more efficient instrument when the degree of financial risk is considerable.

Q: What is the role of market size in risk charges, and why does this create a competitive asymmetry? A: The model shows that the marginal risk charge decreases as the insured population grows (risk pooling), with marginal standard deviation equal to sigma_0 / (2*sqrt(q)), which vanishes as q approaches infinity. This implies that larger national insurers, covering very large populations, effectively face no risk charges, while smaller regional insurers face meaningful marginal risk charges. This size-asymmetry is the fundamental reason why public reinsurance disproportionately benefits smaller insurers—by reducing their risk charges, it narrows the cost gap with national insurers and intensifies competition.

Q: What scope conditions apply to the structural findings? A: The structural estimates are based on the Colorado individual health insurance exchange, covering years 2017–2020, chosen to avoid unsatisfactory early data quality and to net out systematic pandemic effects. The model assumes national insurers do not face risk charges in the baseline specification, and that aggregate (correlated) risk is not the primary driver during the sample period. Results are robust to staggered-treatment corrections (Callaway-Sant’Anna 2021; Borusyak et al. 2024), alternative outcome measures (benchmark premiums, Silver plan averages), alternative aggregation levels, and sensitivity analyses allowing for insurer entry/exit, correlated risks, moral hazard, and alternative risk charge functional forms.

Q: What are the broader policy implications of the framework? A: The framework applies to any market where firms face substantial cost uncertainty and internalize financial risk, including property and casualty insurance, flood insurance, wildfire insurance, and government loan guarantee programs. The analysis suggests that ignoring the risk protection channel causes policymakers to underestimate the effectiveness of public reinsurance relative to demand-side subsidies. Supply-side risk-sharing policies are particularly important for markets with small, financially constrained firms, where cost uncertainty most severely distorts pricing and competition, and where the competitive benefits of risk reduction are largest.

Risk Charge: An additional cost term in the insurer’s objective function representing the implicit financial cost of bearing claims uncertainty, formalized as L(S) where S is a risk measure of total cost. Risk charges make the insurer behave “as if risk averse,” raising effective marginal cost above expected claims cost. In the baseline model the risk charge equals rho times the standard deviation of total claims.

Risk Charge Coefficient (rho): The parameter governing the insurer’s marginal cost of financial risk, estimated structurally at an average of 0.25 for regional insurers in Colorado. It can be interpreted as either a direct risk-aversion parameter, the marginal cost of regulatory capital, or a reduced-form representation of financial and regulatory frictions that make bearing cost uncertainty costly.

Risk Protection Channel: The mechanism through which reinsurance (public or private) reduces claims cost variance and thereby lowers the insurer’s risk charge, distinct from the cost-subsidy channel. The risk protection channel is operative even for actuarially fair reinsurance (theta = 1) and is responsible for pass-through rates exceeding unity under public reinsurance programs.

Cost Subsidy Channel: The mechanism through which subsidized public reinsurance (theta less than 1) lowers the insurer’s net expected claims cost by reimbursing a share of high-cost claims without charging an actuarially fair premium. This channel operates regardless of whether the insurer faces risk charges and is the primary channel in standard models.

Pass-Through Rate: The ratio of premium reduction to government expenditure on reinsurance. In standard models with market power, pass-through of cost subsidies is typically below one; the paper documents a pass-through rate of 1.3 in Colorado (p = 0.037 for the null of pass-through equal to one), attributing the excess to the risk protection channel reducing both expected cost and cost uncertainty simultaneously.

Stop-Loss Reinsurance: A contract structure in which the reinsurer reimburses the primary insurer for individual claims costs exceeding a deductible (attachment point) kappa up to a cap. In Colorado’s program the attachment point is $30,000 and the cap is $400,000, with government coinsurance rates of 40–80% depending on county tier. More generous reinsurance corresponds to lower kappa; full reinsurance is kappa = 0.

Risk-Based Capital (RBC) Ratio: The ratio of capital surplus (assets minus liabilities) to required risk-based capital, used by NAIC as a measure of insurer solvency. NAIC scrutinizes companies with RBC ratios below 200%; the paper uses RBC ratio below 3 as a proxy for financial constraint in heterogeneity analysis, finding larger premium and private reinsurance responses among constrained insurers.

Tail-End Risk: The risk arising from the possibility that a small fraction of enrollees incurs extremely high medical costs, concentrated in the right tail of the claims distribution. In Colorado, the top 5% of consumers account for 68% of total expenses; tail-end risk is especially severe for small insurers with fewer than 10,000–100,000 enrollees and is the primary motivation for private reinsurance purchases even at above-actuarially-fair prices.

Investing in Influence: Investors, Portfolio Firms, and Political Giving

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates whether institutional investors influence the political activities of their portfolio firms, using political action committee (PAC) giving as a window into the broader question of whether institutional investors can leverage their concentrated ownership to extract benefits from portfolio firms for their own interests rather than those of their clients.

The sample covers 574 institutional investors (those with at least $100 million in assets under management, i.e., 13-F filers) matched to 2,456 portfolio firms that had PACs, over the period 1980–2018. The primary source of variation is the first acquisition by an institutional investor of at least one percent of a portfolio firm’s outstanding shares, yielding 68,387 large acquisition events. PAC giving data come from FEC records matched by name to investor and firm entities. The main regression specification examines how the relationship between investor and firm PAC contributions to the same congressional district changes after such an acquisition, using a saturated set of fixed effects including firm × investor, firm × congressional district, firm × election cycle, investor × congressional district, investor × election cycle, and district × election cycle.

The central finding is that, following a large block purchase, a firm’s PAC giving mirrors more closely that of the acquiring investment management company. In the preferred specification (column 8 of Table 2), the probability that a portfolio firm gives to a politician supported by its investor’s PAC increases by 31 percent after an acquisition. Using a cosine similarity measure of investor-firm PAC giving, the mean similarity of 0.10 at the acquisition cycle rises by 0.02–0.03 (a 20–30 percent increase) by the fourth post-acquisition election cycle.

A key identification concern is that acquisitions may be driven by shared political preferences rather than representing a causal effect. To address this, the authors exploit stock index inclusions as exogenous shifters of institutional investor block purchases: when a firm is added to an index for the first time, passive indexers are compelled to rebalance toward that firm regardless of political alignment. Restricting to 5,601 index-inclusion acquisitions by passive investors, the authors find near-identical effect sizes (beta1 = 0.0132 in column 8 versus 0.0135 in the full sample), and an event study shows no pre-trend in giving convergence for the index subsample, in contrast to a slight pre-trend in the full sample. Divestment events exhibit the symmetric negative pattern: the interaction of post-divestment and investor PAC giving falls by between -0.074 and -0.058 across specifications.

The authors argue that investors drive the convergence rather than portfolio firms adjusting investor preferences. Around acquisition dates, firms exhibit a larger drop in between-election-cycle cosine similarity than investors do. In a difference-in-differences comparison of the acquisition period relative to the preceding period, the difference in stability between investors and firms is 0.075 (significant at the 1 percent level), indicating that firms shift their giving more than investors. Investors obtaining a board seat at the portfolio firm amplifies the effect: in the preferred specification, the board-seat interaction is more than twice as large as the acquisition-alone interaction.

Heterogeneity analysis provides evidence that the convergence reflects investors’ partisan tastes rather than coordinated profit-maximizing political strategy. Acquisitions by more partisan investors (those whose giving is more skewed toward one party) produce a convergence coefficient roughly twice as large (0.020) as less partisan investors (0.010). Private fund families show more than twice the convergence effect of publicly owned fund families. The partisan composition of firm giving also shifts: a firm acquired by an investor giving exclusively to Republicans sees its Republican share increase by 2.8 percentage points relative to a baseline of 47.4 percent (a 5.9 percent increase).

Finally, higher overall institutional ownership is associated with an increase in total PAC giving at the firm level, and this expanded giving does not go disproportionately to politicians on committees overseeing issues the firm actively lobbies — suggesting the ownership-driven increment in political spending is non-strategic from the firm’s profit standpoint and likely serves investors’ own interests.

Q: What is the central research question and why does it matter? The paper asks whether institutional investors influence the political giving of portfolio firms, motivated by the broader concern that the rise of institutional ownership — from 6 percent of U.S. public equities in 1950 to 65 percent in 2017 — concentrates not only economic but also political power in the hands of a small number of asset managers. This matters because if investors shape firms’ PAC giving to serve investors’ own preferences rather than firms’ profit interests, it represents a misuse of corporate resources and a potential amplification of a small group’s political voice.

Q: What data are used and how is the sample constructed? The analysis draws on 13-F filings (investors with at least $100M AUM) from Thomson-Reuters, matched to FEC PAC records via fuzzy and manual name matching. The resulting sample contains 574 investors with PACs and 2,456 portfolio firms with PACs, spanning 1980–2018. The Cartesian product of investor-firm pairs is restricted to those connected by at least one large acquisition event (defined as first acquisition of at least 1 percent of outstanding shares), yielding 68,387 such events. PAC contributions are measured at the investor- and firm-congressional-district-election-cycle level, linked to House of Representatives winners using MIT Election Data files.

Q: What is the baseline regression and what does it find? The baseline regression (equation 1) interacts Log Investor PAC with a Post indicator (equal to 1 after the first large acquisition and while the stake is maintained) at the investor-firm-congressional-district-election-cycle level, with a saturated set of fixed effects. The coefficient on the interaction (beta1) is positive and highly significant (p < 0.001) across all eight specifications, ranging from 0.013 to 0.032. In the preferred specification, the increase in giving similarity is 31 percent relative to the pre-acquisition baseline.

Q: How do the authors establish causality and rule out endogenous acquisitions? The primary identification strategy uses first-time inclusions of firms in stock indices (approximately 1,000 indices tracked in the sample) as exogenous shifters: passive indexers must rebalance toward the included firm regardless of political alignment. This subsample of 5,601 index-inclusion acquisitions produces near-identical coefficient estimates (0.0132 versus 0.0135 in the full sample), and the event study for this subsample shows no pre-trend in giving convergence, unlike the slight pre-trend in the full sample. Equality of the two coefficients cannot be rejected at standard significance levels.

Q: What evidence shows it is firms adjusting to investors rather than the reverse? The authors compute between-election-cycle cosine similarity separately for investors and firms around acquisitions. On average, investors exhibit more stable giving than firms at acquisition dates (Cos(xi,t, xi,t+1) > Cos(xf,t, xf,t+1)). The difference-in-differences estimate — comparing the acquisition period to the preceding period — is 0.075 (significant at 1 percent), indicating a relatively larger break in firm giving. Over a two-cycle window, the difference-in-differences estimate is 0.083, again indicating convergence is driven by firms shifting toward investors rather than the reverse.

Q: What role does board representation play? In approximately 5 percent of acquisitions in the sample, the investor obtains a board seat. In specifications that include both the acquisition effect (Post × Log Investor PAC) and a board-membership interaction (Board × Log Investor PAC), both terms are positive and significant at the 1 percent level. In the preferred specification, the board-seat interaction is more than twice as large as the acquisition-alone interaction, indicating that a direct governance channel — board representation — substantially amplifies the convergence in political giving.

Q: What does the divestment analysis show? Symmetric to the acquisition results, divestment events (where an investor exits a stake of at least 1 percent held for at least one election cycle) are associated with a decline in investor-firm PAC giving correlation. Post-divestment interaction coefficients range from -0.074 to -0.058 across specifications, and an event study confirms the correlation falls sharply after the divestment cycle.

Q: Does investor partisanship affect the magnitude of influence? Yes. Classifying investors as “More Partisan” (above-mean absolute deviation from 50/50 party split) versus “Less Partisan,” the interaction coefficient for More Partisan investors (0.020) is roughly twice that of Less Partisan investors (0.010). After a large acquisition by a fully Republican-giving investor, the acquired firm’s giving to that politician increases by 23.5 percent; the comparable figure for a Less Partisan investor is 7.6 percent. This pattern holds in both the full sample and the index-inclusion subsample.

Q: How do private versus public fund families differ in their influence? Private fund families (e.g., Vanguard, Fidelity) show more than twice the convergence coefficient of publicly owned fund families (e.g., BlackRock, State Street, Invesco). The authors attribute this to private fund managers facing less outside scrutiny, allowing their giving to more readily reflect the preferences of owners and managers. Private investors also show greater partisan polarization: the 10th–90th percentile Republican-giving range for private investors is 6.3–100 percent, versus 21.7–88.3 percent for public investors.

Q: Does increased institutional ownership expand overall firm PAC spending? Yes. In firm-year level regressions, institutional ownership is a positive and significant predictor of total firm PAC giving (significant at at least the 5 percent level in both cross-sectional and firm-fixed-effects specifications). Total corporate political expenditure by sample firms increased by nearly a factor of six over 1980–2018. The authors note that while many factors contribute, increased institutional ownership may be at least partly responsible for this expansion.

Q: Does the additional giving driven by institutional ownership go to strategically important politicians for the firm? No. Regressions relating institutional ownership to giving to politicians on congressional committees overseeing issues the firm actively lobbies (a standard measure of politicians’ strategic importance to firms) yield near-zero and statistically weak point estimates. In the preferred firm-fixed-effects specification, the share of total PAC giving devoted to such strategically relevant politicians is negatively associated with institutional ownership at marginal significance (p < 0.10), consistent with the interpretation that ownership-driven incremental political spending is non-strategic from the firm’s own profit perspective and expands total giving rather than displacing strategic giving.

Q: What are the policy and legal implications? The authors flag three concerns: (i) the ownership-driven increment in political spending may represent a misuse of corporate resources that does not serve portfolio firm shareholders; (ii) it may constitute an illegal activity, since using a firm’s PAC to reimburse or proxy for an investor’s own political preferences can run afoul of campaign finance law; and (iii) it is a channel through which unequal resources amplify the political voice of a small number of fund managers at the expense of dispersed ultimate investors who are likely unaware of and do not sanction these contributions. The findings challenge the Supreme Court’s premise in Citizens United that corporate political speech reflects shareholder profit maximization.

PAC comovement (investor-firm giving similarity): The increase in the probability that a portfolio firm’s PAC donates to a politician also supported by an acquiring investor’s PAC, measured as the interaction coefficient between Log Investor PAC and a Post-acquisition indicator in the baseline regression. In the preferred specification this represents a 31 percent increase relative to the pre-acquisition baseline.

Cosine similarity (cross-time and cross-entity): A measure defined as the Euclidean dot product between two vectors of PAC giving (either the same entity across adjacent election cycles, or investor versus firm in the same cycle), taking values between 0 and 1, where 1 indicates identical giving patterns. Used both to confirm convergence post-acquisition and to attribute that convergence to firm rather than investor adjustment.

Index-inclusion acquisition: A large block purchase that results from a firm being added for the first time to a stock index tracked by a passive institutional investor, used as an exogenous shifter of investor stakes that is orthogonal to investor-firm political alignment. There are 5,601 such events in the sample.

Partisanship (investor): Classified as “More Partisan” if an investor’s absolute deviation from a 50/50 party split in PAC donations is above the sample mean. More partisan investors produce roughly twice the convergence effect on portfolio firm giving compared to less partisan investors, used as evidence that personal political preferences rather than profit-maximizing business strategy drive the convergence.

Post indicator (Postift): A binary variable equal to 1 for all election cycles following an investor’s first acquisition of at least 1 percent of a portfolio firm’s outstanding shares, and remaining 1 as long as the investor holds any stake in the firm. The key source of temporal variation in the baseline regression.

Strategically important politicians: Members of Congress sitting on committees that oversee issues on which a firm actively lobbies, identified by crosswalking lobbying reports from the Senate Office of Public Records to relevant committee jurisdictions. Used to test whether ownership-driven political giving displaces or supplements firm-profit-motivated giving.

Board seat channel: The mechanism through which investor influence on firm political giving is amplified when the investor obtains representation on the portfolio firm’s board of directors (present in approximately 5 percent of acquisitions). The board interaction coefficient is more than twice the acquisition-alone coefficient in the preferred specification.

Jackknife Standard Errors for Clustered Regression

Mon, 01 Jan 0001 00:00:00 +0000

Hansen (2025) makes a theoretical case for replacing the conventional cluster-robust variance estimator (CRVE) and heteroskedasticity-consistent (HC) standard errors with a specific jackknife variance estimator, V5, in linear regression with heteroskedastic and/or cluster-dependent observations.

The paper identifies two fundamental problems with conventional CRVE1 and CRVE2 estimators. First, these estimators can be fully downward biased: Theorem 2 establishes that the infimum of E[v̂1²]/v² and E[v̂2²]/v² over all admissible regressor and covariance matrix configurations equals zero, meaning expected variance can be arbitrarily close to zero relative to the true variance. This pathology arises from extreme regressor leverage — specifically when one cluster dominates the sample — and holds even under homoskedasticity and clusterwise invertibility. Second, Theorem 5 shows that confidence intervals constructed from CRVE1 and CRVE2 standard errors have worst-case coverage probability equal to zero for any finite critical value c, making them unable to achieve any target coverage level uniformly over regression designs.

Crucially, Hansen shows that even the conventional jackknife estimators V3 and V4, which are already in use (e.g., via Stata’s vce(jackknife) option), share these pathologies when clusterwise noninvertibility is present. Clusterwise noninvertibility occurs when deleting a single cluster renders the regressor matrix singular — as in regressions with cluster-level fixed effects, a single treated cluster, or sparse dummy variables. Stata’s existing fix of simply dropping noninvertible clusters is shown to be insufficient: under clusterwise noninvertibility, the infimum of E[v̂3²]/v² and E[v̂4²]/v² over the broader model class equals zero (Theorem 2, equations 19–20), and the corresponding confidence intervals also achieve worst-case coverage of zero.

The proposed estimator V5 resolves these problems through three modifications to the conventional jackknife: (1) it uses a generalized (Moore-Penrose) inverse rather than dropping noninvertible clusters, ensuring all clusters are included; (2) it centers at the full-sample estimator β̂ rather than the mean of delete-one estimates; and (3) it omits the (G−1)/G degrees-of-freedom correction. Theorem 1 proves that E[V̂5] ≥ V in the positive semidefinite sense for all sample sizes, regressor matrices, and covariance structures — the estimator is never downward biased. Theorem 3 then shows that jackknife-based confidence intervals C̃5(c) have coverage probability bounded below by the Cauchy distribution for any c ≥ 1. With the conventional critical value c = 1.96, this guarantees finite-sample coverage of at least 70% and test size of at most 30%, regardless of regression design or error variance structure.

To improve upon the conservative Cauchy bound in practice, the paper proposes a Satterthwaite adjusted t approximation for the jackknife t-ratio. The adjustment derives degrees of freedom K and a scale factor a from the eigenvalue structure of a design-dependent matrix D. Theorem 7 shows that a → 1 and K → ∞ as n → ∞ under mild regularity conditions (no single cluster dominates). Simulation evidence across six regression designs — varying regressor distributions (Normal, LogNormal with cluster dependence, sparse Dummy) and error structures (clustered normal, heteroskedastic) — with G ∈ {6, 12, 40, 100} clusters confirms that the Satterthwaite jackknife interval achieves coverage rates uniformly above 93% at the nominal 95% level even with G = 6, while CRVE1 intervals fall as low as 57% coverage in the LogNormal/heteroskedastic design. The empirical application extends Meng, Qian, and Yared (2015) on Chinese TV access and redistribution preferences, finding that the jackknife standard error for the TV access coefficient exceeds the CRVE1 standard error and the Satterthwaite interval is wider, affecting conclusions about statistical significance.

The theory holds under Assumptions 1–4: correctly specified linear regression with zero conditional mean errors, full rank X, finite second moments, arbitrary cluster sizes and within-cluster covariance structure, and (for Theorem 3) normal errors. Results hold for fixed k and G, arbitrary n, and allow clusterwise noninvertibility subject to Assumption 3 (inference targets the well-identified regressors).

Q: What is the central claim of the paper? A: Conventional CRVE and HC variance estimators should be replaced by the jackknife estimator V5 in all linear regression contexts with heteroskedastic or clustered errors. V5 is never downward biased (its expectation weakly exceeds the true variance matrix), whereas CRVE1 and CRVE2 can be arbitrarily downward biased. The Satterthwaite-adjusted V5 confidence interval has excellent finite-sample coverage.

Q: What is the worst-case bias of CRVE1? A: The infimum of E[v̂1²]/v² over all admissible regressor matrices and covariance matrices equals zero (Theorem 2, equation 15). This means that for some data-generating process, the expected CRVE1 variance estimate is arbitrarily close to zero relative to the true variance — full downward bias. Importantly, this pathology holds even under homoskedasticity (Σ = Iₙ) and clusterwise invertibility; it is driven entirely by extreme regressor leverage.

Q: Why is CRVE2 also fully downward biased, and how does its failure differ from CRVE1’s? A: Theorem 2 (equation 16) shows that the infimum of E[v̂2²]/v² over F* also equals zero. The difference is that the proof for CRVE2 requires non-i.i.d. errors, meaning CRVE2’s failure requires manipulation of the covariance matrices in addition to extreme leverage, whereas CRVE1 can fail under i.i.d. errors from leverage alone.

Q: What is clusterwise noninvertibility and why does it matter? A: Clusterwise noninvertibility occurs when deleting a single cluster renders the regressor design matrix X’X − Xg’Xg singular. This happens in regressions with cluster-level fixed effects, with a cluster-level treatment indicator when only one cluster is treated, or with sparse dummy variables. The paper shows that the conventional jackknife estimators V3 and V4 become fully downward biased (infimum of expectation ratio equals zero) under clusterwise noninvertibility, even though Stata’s existing fix of dropping noninvertible clusters was explicitly designed to handle this case.

Q: What is the key innovation in V5 that makes it robust to clusterwise noninvertibility? A: V5 uses the Moore-Penrose generalized inverse in the delete-one-cluster estimator β̂₋g, ensuring all G clusters are included in the sum rather than discarding noninvertible clusters. It also centers at the full-sample β̂ rather than the mean β̄ of delete-one estimates, and omits the (G−1)/G degrees-of-freedom correction. The paper shows these three differences together imply V̂5 ≻ V̂4 ≻ V̂3 in the positive semidefinite ordering.

Q: What does Theorem 1 establish about V5? A: Theorem 1 proves E[V̂5] ≥ V in the positive semidefinite sense for all sample sizes, all regressor matrices, all covariance matrices, and under clusterwise noninvertibility. This conservative property holds without any assumption on cluster sizes, regressor leverage, within-cluster correlation, or heteroskedasticity beyond Assumption 1 (correct specification and finite second moments). The infimum of E[v̂5²]/v² equals 1 (equation 21), meaning the inequality is sharp.

Q: What does the Cauchy distribution bound say, and how useful is it in practice? A: Theorem 3 shows that for any c ≥ 1, the jackknife confidence interval C̃5(c) has coverage probability at least P[|ζ| ≤ c] where ζ is Cauchy. With c = 1.96, this guarantees coverage of at least 70% and test size of at most 30% uniformly over all regression designs and error structures (under normality). The bound is not tight in typical applications — actual coverage is much higher — but it provides the first generally applicable uniform guarantee for clustered/heteroskedastic regression. The Cauchy critical value at 5% is 12.7, far too large for practical use, so the bound is more useful as a theoretical guarantee than as a practical inference tool.

Q: What does Theorem 5 establish about confidence intervals from CRVE1–CRVE4? A: Under normality, the worst-case coverage probability of confidence intervals constructed from any of the four estimators v̂1 through v̂4 equals zero for any finite critical value c (equations 26–29). For v̂1 and v̂2, this holds over the clusterwise-invertible model class F*; for v̂3 and v̂4 it holds over the broader class F allowing noninvertibility. Zero worst-case coverage cannot be fixed by enlarging c, since the result holds for all finite c. This is not an impossibility result in the Bahadur-Savage sense; it is a statement that specific commonly-used intervals fail, while V5-based intervals succeed.

Q: What is the Satterthwaite approximation and how is it implemented? A: The Satterthwaite adjustment replaces the jackknife t-ratio’s exact finite-sample distribution — a ratio of a normal to the square root of a weighted sum of chi-squares — with a scaled t distribution with K degrees of freedom, where K and a scale factor a are matched by moment conditions on the eigenvalues of a design matrix D. The confidence interval is θ̂ ± v̂5 · t^{1−α/2}_K / a, and the p-value uses a Student t or F distribution with the same K and scale. These quantities can be computed without explicit eigendecomposition using trace formulas (equations 38–39), which are preferred computationally when G > k.

Q: What do the simulations show about coverage rates? A: Across six designs (three regressor types × two error types) and G ∈ {6, 12, 40, 100}, CRVE1 falls as low as 57% coverage in the LogNormal regressor/heteroskedastic error design with G = 6. CRVE2 has somewhat better but still substantially undercovering intervals. The conventional jackknife interval undercovers (as low as 85%) in leveraged/heteroskedastic designs. The Satterthwaite jackknife interval achieves coverage uniformly exceeding 93% across all designs, though it can be excessively conservative (100%) in some cases. All simulation estimates have standard errors less than 0.003 (20,000 replications).

Q: Does the Satterthwaite adjustment vanish in large balanced samples? A: Yes. Theorem 7 shows that if the design matrix is uniformly non-singular and no single cluster dominates (maxg ||Xg||² = o(n)), then a → 1 and K → ∞ as n → ∞. Consequently, the Satterthwaite interval converges to the standard normal interval in well-balanced large samples.

Q: How does V5 relate to the classical HC3 estimator? A: Under independent sampling (no clustering, ng = 1), V5 reduces to the HC3 estimator of Andrews (1991) and Davidson and MacKinnon (1993), which uses the Moore-Penrose inverse. The conventional jackknife V3/V4 reduce to the HC3 of MacKinnon and White (1985). The paper’s results thus provide a formal theoretical basis for the longstanding recommendation (by Efron-Stein 1981, MacKinnon-White 1985, Andrews 1991, and others) to use HC3/jackknife standard errors.

Q: What is the practical recommendation for empirical researchers? A: Replace all CRVE1/CRVE2/HC standard errors with V5, computed via the Moore-Penrose generalized inverse including all clusters. Report V5-based standard errors (which are never downward biased) alongside Satterthwaite-adjusted confidence intervals and p-values using equations (30)–(31). The adjustment parameters a and K differ per coefficient and must be computed separately for each. The paper advises against reporting a/v̂5 as an “adjusted standard error” since that quantity loses the never-downward-biased property.

Q: What is the empirical application and what does it find? A: The paper extends Meng, Qian, and Yared (2015), which studies the effect of TV access on demand for redistribution in China using provincial household survey data (30 provinces, multiple years), and Canay, Santos, and Shaikh (2021), who found CRVE1 standard errors may be unreliable in that setting. Applying V5, the jackknife standard error for the TV access coefficient exceeds the CRVE1 standard error, the Satterthwaite interval is wider than the conventional interval, and conclusions about statistical significance are affected.

Q: What are the scope conditions and limitations? A: The bias results (Theorems 1–2) require only correct specification (zero conditional mean) and finite second moments. The Cauchy bound (Theorem 3) additionally requires normal errors; whether a similar bound holds without normality or in G → ∞ asymptotics is left open. The Satterthwaite adjustment applies only to inference on real-valued (scalar) parameters and does not extend to joint hypothesis tests. Assumption 3 limits inference to “well-identified” regressors (those whose leave-cluster-out coefficients are uniquely defined after partialling out controls).

V5 (jackknife variance estimator): The paper’s proposed estimator, defined in equation (10) as the sum over all G clusters of outer products of (β̂₋g − β̂), where β̂₋g uses the Moore-Penrose generalized inverse. Unlike conventional jackknife estimators, V5 includes all clusters (no dropping), centers at the full-sample β̂, and omits the (G−1)/G correction. Its key property is E[V̂5] ≥ V for all regression designs.

Never-downward-biased (conservative) estimator: A variance estimator whose expectation is weakly greater than the true variance in the positive semidefinite sense, for all admissible regressor matrices and covariance structures. V5 has this property; CRVE1, CRVE2, and conventional jackknife estimators do not.

Full downward bias: The worst-case property that the infimum of E[v̂²]/v² equals zero over the model class — meaning the expected variance estimate can be arbitrarily close to zero relative to the true variance. CRVE1 is fully downward biased under clusterwise invertibility alone; CRVE2 requires non-i.i.d. errors; conventional jackknife estimators become fully downward biased under clusterwise noninvertibility.

Clusterwise noninvertibility: The condition where deleting a single cluster g renders the matrix X’X − Xg’Xg singular, so the standard delete-one-cluster estimator β̂₋g is undefined. This occurs in regressions with cluster-level fixed effects, a single treated cluster, or sparse dummy variables. V5 handles this via the Moore-Penrose generalized inverse; Stata’s existing fix of dropping such clusters is shown to be non-robust.

Cauchy distribution bound: Theorem 3’s result that the jackknife confidence interval C̃5(c) has coverage probability at least P[|ζ| ≤ c] for all c ≥ 1, uniformly over all regression designs and error variances (under normality). With c = 1.96, this gives a guaranteed coverage floor of 70%. This is the first generally applicable uniform coverage guarantee for clustered/heteroskedastic regression.

Satterthwaite adjusted t approximation: A data-dependent distributional approximation for the jackknife t-ratio that approximates the denominator’s weighted chi-square distribution by a scaled chi-square with K degrees of freedom, where K and scale factor a are computed from trace formulas involving the design matrix. The resulting confidence interval θ̂ ± v̂5 · t^{1−α/2}_K / a converges to the standard normal interval in well-balanced large samples.

Regressor leverage: The degree to which variation in a coefficient of interest is concentrated in a small number of clusters. High leverage (when one cluster dominates the regressor of interest) is the mechanism by which CRVE1/CRVE2 achieve worst-case downward bias even under homoskedasticity.

Jumpstarting an International Currency

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks how a currency achieves international status — moving from zero to positive cross-border use — and whether deliberate central bank policy can accelerate that transition. The authors focus on the People’s Bank of China (PBoC) swap lines signed between 2009 and 2018, which extended RMB-denominated lender-of-last-resort credit to foreign central banks for the stated purpose of supporting RMB-denominated trade finance and settlement.

The empirical analysis combines two datasets. The first covers every RMB swap line agreement the PBoC signed with a foreign central bank (38 countries by 2018), compiled from PBoC news releases and validated against counterparty communications, treated as a staggered binary absorbing treatment. The second is monthly SWIFT data on cross-border payment message values (October 2010 – October 2018), disaggregated by currency and message type (payment orders MT103/MT202 and trade-finance messages MT400/MT700). The working sample, after excluding financial centre hubs, sanctioned countries, pre-sample treated countries, and small economies, covers 114 countries with 11,058 observations, of which 21 are treated during the sample period.

The main identification strategy is a staggered difference-in-differences design using the imputation estimator of Borusyak et al. (2024), with controls for bilateral trade with China, Chinese economic policy variables (RMB clearing bank presence, AIIB membership, infrastructure investment flows, UN voting alignment), and regional RMB adoption trends. The authors are explicit that conditional independence is not guaranteed and characterize results as documenting an association.

At the extensive margin, signing a swap line is associated with an approximately 14 percentage point increase in the probability that a country uses the RMB for international payments in a given month (baseline column: 11%, rising to approximately 14% with controls and approximately 20% when anticipation effects are accounted for by shifting treatment timing six months earlier). At the intensive margin — using ln(1 + RMB payments) and Poisson specifications — RMB usage is between 250% and 440% higher in treated countries following the policy. The effect concentrates within the first 12 months of signing and persists without reversion. The effect is present in payments not involving China as a counterparty, is not explained by Belt and Road Initiative membership, and does not extend to bilateral trade volumes with China.

Four mechanisms from the paper’s theoretical model are tested and supported. First, swap lines reduce offshore RMB borrowing costs by an estimated 115 basis points on average (rising to 205 basis points for emerging market currencies). Second, the 2015–16 RMB crisis — in which the PBoC drained offshore liquidity to defend the exchange rate peg, sharply raising private RMB borrowing costs — caused a significant decline in RMB use among countries without a swap line but not among those with one, consistent with the model’s prediction that swap lines cap the right tail of borrowing cost distributions. Third, effects are concentrated in trade-finance SWIFT messages, stronger in countries with above-median trade shares with China, and increasing in intermediate import intensity and working capital reliance. Fourth, the RMB gains displace existing international currencies — the USD share falls by approximately 8 percentage points and the EUR share by approximately 2.5 percentage points — rather than displacing local currencies, as the model predicts. There are also geographic spillovers: a neighboring country signing a swap line is associated with a 10% increase in RMB use even for countries that did not sign.

The theoretical framework models import-export firms that choose simultaneously the currency of trade finance and the currency of sales invoicing. Sticky prices create a complementarity between these two choices. A swap line truncates the right tail of the borrowing cost distribution (first-order stochastic dominance), which can push firms above a threshold into using the rising currency for both liabilities and invoicing. The model predicts threshold behavior — a currency either jumpstarts or does not — and explains why only a small number of currencies ever achieve international status.

Q: What are the PBoC swap lines and how do they mechanically affect firms? A: A PBoC swap line is a renewable 3-year agreement between the PBoC and a foreign central bank that allows the foreign central bank to borrow RMB and on-lend it domestically to support RMB-denominated trade finance. Like other central bank lending facilities, they place a ceiling on interest rates, thereby truncating the right tail of the distribution of RMB borrowing costs faced by commercial banks and their firm customers. The key insurance property holds even when lines are not actively drawn upon, because their existence caps tail risk.

Q: What is the extensive margin finding for swap lines and RMB payments? A: Signing a swap line is associated with an approximately 11% increase in the probability that a country uses the RMB for cross-border payments in a given month without controls, rising to approximately 14% with the full set of controls, and to approximately 20% when treatment timing is shifted six months earlier to account for anticipation effects. The event study shows the effect concentrates within 12 months of signing and does not revert.

Q: What is the intensive margin finding? A: Using ln(1 + RMB payments) and Poisson specifications — preferred because Mongolia is an outlier and payment value volatility is increasing in payment level — treated countries have RMB payment values between 250% and 440% higher than control countries after signing. The RMB share of payments rises by 0.13 percentage points on average, compounding to approximately 0.3 percentage points in years 3–4, or roughly one-fifth of the overall rise in RMB payments over the full sample period.

Q: How do the authors address the concern that swap lines are signed precisely when economic integration with China is deepening? A: They include a comprehensive set of controls: bilateral export and import values to/from China, the ratio of Chinese trade to GDP, China trade agreement status, RMB clearing bank presence, AIIB membership, infrastructure investment flows, and UN voting alignment. They also show separately that (i) the effect is present in RMB payments not involving China as a counterparty, (ii) Belt and Road Initiative membership does not account for the effect, and (iii) there is no increase in bilateral trade with China following swap line signing. The authors nonetheless characterize results as documenting an association, not establishing causation.

Q: Do swap lines actually reduce RMB borrowing costs as the model requires? A: Yes. Using the same staggered difference-in-differences methodology, signing a swap agreement is associated with a 115 basis point fall in offshore RMB borrowing rates on average. For emerging market currency comparators the effect rises to 205 basis points. The event study shows an immediate and sustained reduction with no detectable pre-trend.

Q: What does the 2015–16 RMB crisis reveal about the mechanism? A: In August 2015 the PBoC adjusted its RMB-USD central parity rate, triggering a 3% depreciation over two days and subsequent offshore liquidity drainage that raised both the level and volatility of offshore RMB borrowing costs until approximately April 2017. This shock was primarily financial rather than reflecting a Chinese economic slowdown. Countries without a swap line experienced a sharp decline in RMB payment usage in 2015Q4, while countries with a swap line — whose right-tail borrowing costs were capped — did not, consistent with the model’s prediction that the lines insulate against tail risk shocks.

Q: Are the effects concentrated in trade finance as the model predicts? A: Yes. Restricting the analysis to SWIFT trade-finance message types (MT400 and MT700), the coefficient estimates are similar in magnitude to those for all payments. Effects on the trade finance extensive margin are concentrated among countries with above-median trade shares with China. The effects are also increasing in countries’ intermediate import intensity and in the degree to which export industries rely on working capital.

Q: Which currencies does the RMB displace and which does it not displace? A: The swap line is associated with a 14 percentage point rise in the RMB share of payments to and from China. Decomposing this: the USD share falls by approximately 8 percentage points, the EUR share by approximately 2.5 percentage points, the combined GBP/JPY/CHF share by approximately 0.5 percentage points, and other currencies by approximately 3 percentage points. The local currency of the country receiving the swap line does not show a statistically significant decline, consistent with the model’s prediction that the RMB competes primarily with existing international vehicle currencies rather than with domestic currencies.

Q: Are there geographic spillovers from swap lines? A: Yes. A neighboring country (defined as countries within 1,000 km, or the nearest five if fewer than five are within that distance) signing a swap line is associated with a 10% increase in RMB payments for the non-signatory neighbor. The authors attribute this to supply chain linkages: firms importing RMB-invoiced inputs from a swap-line country face an incentive to adopt RMB for their own downstream transactions.

Q: What does the model predict about which currencies can ever become international? A: The model identifies three thresholds a currency must pass. First, exchange rate variance must be sufficiently low; most currencies fail this condition. Second, the right tail of borrowing costs in that currency must not be too high; skewed distributions fail the threshold condition in Proposition 2. Third, the currency-issuing country must be large enough as an export market or intermediate input source to generate the complementarity factor Psi that makes adopting the currency worthwhile. Most currencies fail on multiple dimensions, explaining why so few achieve international status.

Q: How do sticky prices create the complementarity between trade finance currency and invoicing currency in the model? A: Firms set prices in advance before exchange rates and borrowing costs are realized. If a firm borrows in currency r to finance imported inputs but prices its exports in currency d, cost and revenue shocks are mismatched, creating profit volatility. Nominal price stickiness means firms cannot adjust prices ex post to maintain constant markups. This makes it optimal to align the currency of liabilities (trade finance) with the currency of export invoicing, creating a complementarity that amplifies the effect of a reduction in r-currency borrowing costs on invoicing currency choice.

Q: How do the authors handle the potential bias from heterogeneous treatment effects in the staggered difference-in-differences design? A: They use the imputation estimator of Borusyak et al. (2024), which is robust to heterogeneous treatment effects across cohorts, clustering standard errors at the country level and averaging treatment effects by cohort. They also verify results using the synthetic difference-in-differences estimator of Arkhangelsky et al. (2021), which reweights observations to equalize pre-treatment trends, and show results are robust across both two-way fixed effects and these more modern estimators.

Q: What historical parallel do the authors draw and what does it imply for the RMB’s future? A: The paper draws a parallel with the USD’s displacement of pound sterling in trade finance in the decade following the Federal Reserve’s creation in 1913 and the establishment of bankers’ acceptances. That transition was supported by World War I’s damage to the UK economy and rapid US economic growth. The authors conclude that RMB internationalization will require not only continued policy support but also favorable economic fundamentals including sound monetary policy and deeper capital markets.

Q: How does the PBoC’s swap line program differ from Federal Reserve and ECB swap lines? A: PBoC lines differ in four key respects: they have longer maturities (3-year renewable agreements vs. shorter-term Fed/ECB lines); they involve a large and diverse set of mostly developing countries rather than a handful of advanced economies; they target trade finance in a context of limited RMB cross-border banking rather than addressing foreign-bank dollar funding shortfalls caused by dollar dominance; and they were designed to initiate internationalization rather than to respond to an existing dominant currency’s liquidity stresses. The aggregate notional limit of approximately RMB 3 trillion is nonetheless comparable in scale to the USD 600 billion of peak drawings from Fed swap lines.

International currency jumpstart: The process by which a currency moves from zero to positive international use, as opposed to the better-studied phenomenon of a currency achieving dominance. The paper distinguishes jumpstart (initial adoption) from dominance (widespread adoption), arguing that different mechanisms govern each stage.

PBoC swap lines: Renewable 3-year agreements between the People’s Bank of China and foreign central banks enabling the latter to borrow RMB and on-lend it domestically for RMB-denominated trade finance. In the paper’s framework, they function as an extension of the lender of last resort function abroad, placing a ceiling on offshore RMB borrowing costs and truncating the right tail of the borrowing cost distribution.

Trade finance currency complementarity: The paper’s central mechanism — the alignment incentive between the currency of a firm’s liabilities (working capital / trade finance for imported inputs) and the currency of its export invoicing. Sticky prices create this complementarity because misaligned currency choices expose firms to uninsurable profit volatility.

Borrowing cost distribution truncation: The mechanism by which a swap line affects firm behavior — not by lowering average costs but by capping the right tail of the distribution of possible RMB borrowing rates. The model requires first-order stochastic dominance of the post-swap-line distribution over the pre-swap-line distribution.

Threshold condition for currency adoption: Derived from the model’s Proposition 2, the condition on the expected concave function of borrowing costs relative to an adjusted interest rate differential that must be satisfied for a firm to choose r-currency credit over d-currency credit. The complementarity factor Psi, which increases with the size of the rising-currency market, enters this threshold.

Extensive vs. intensive margin of currency use: The extensive margin refers to whether a country uses the RMB at all in a given month (1(Rpayment > 0)); the intensive margin refers to the share of payments denominated in RMB or the log value of RMB payments. The paper finds the swap lines affect both margins, with the extensive margin effect appearing immediately and stabilizing after 12 months.

Vehicle currency displacement: The paper’s empirical finding that RMB adoption displaces existing international vehicle currencies (USD, EUR) rather than local currencies. This is a prediction of the model: firms adopting RMB for trade finance were previously using an existing international currency, not their domestic currency, for that purpose.

Latent Heterogeneity in the Marginal Propensity to Consume

Mon, 01 Jan 0001 00:00:00 +0000

Lewis, Melcangi, and Pilossoph estimate the unconditional distribution of the marginal propensity to consume (MPC) using the 2008 Economic Stimulus Act (ESA) rebate payments, deploying Gaussian mixture linear regression (GMLR) — a clustering regression approach — rather than the standard practice of interacting the rebate with observable household characteristics. The key methodological departure is that households are assigned to groups not by any presupposed observable, but by how well estimated group-specific MPCs describe each household’s actual consumption response; this allows recovery of the full unconditional MPC distribution, including heterogeneity driven by latent (unobservable) factors.

Data come from the 2008 Consumer Expenditure Survey (CEX), which contains household-level expenditure data and supplemental questions on ESA payments. Identification exploits the quasi-random timing of rebate receipt, determined by the last two digits of recipients’ Social Security Numbers, following the design of Parker, Souleles, Johnson, and McClelland (2013). The specification is updated following Borusyak et al. (2024) to avoid “forbidden comparisons” in staggered treatment settings. The number of groups G is selected by BIC, which selects G = 3 for total expenditures, confirmed by K-fold cross-validation.

The main finding is substantial MPC heterogeneity. For total expenditures, the three estimated group-level MPCs are 0.04, 0.23, and 1.33, with population shares of 30%, 48%, and 23% respectively. The implied aggregate (share-weighted average) MPC is 0.42, compared to 0.24 in the homogeneous Parker et al. (2013) specification estimated on the same data. Splitting by consumption category: for nondurables, two groups have MPCs of 0.09 and 0.18, with roughly equal population shares, and the lower bound of 0.09 is statistically distinguishable from zero — evidence against strict adherence to the Permanent Income Hypothesis even among the lowest-MPC group. For durables, the MPC distribution is dichotomous: about 29% of households have a durable MPC statistically indistinguishable from zero, while 21% have an MPC of 0.67. The cross-good correlation between household-level nondurable and durable predicted MPCs is only 0.13, ruling out strong substitution but indicating weak complementarity.

Turning to observable determinants, the paper finds that many household characteristics are individually correlated with estimated MPCs — including homeownership, mortgage status, income, and the average propensity to consume (APC) — despite the fact that the same dataset and similar identification strategies previously yielded insignificant relationships. Homeowners have significantly higher MPCs than renters; households with a mortgage have even higher MPCs than outright homeowners. In salary income, households in the top tercile spend 0.17 more per rebate dollar than the baseline group; households in the top tercile of non-salary income spend 0.19 more. However, in joint regressions, only two characteristics remain robustly and positively correlated with MPCs: total income (both salary and non-salary components) and the APC. The APC relationship is particularly notable: a one-percentage-point higher prior spending rate is associated with 0.19 additional cents spent per rebate dollar in the full multivariate specification.

The paper identifies three groups in the joint income-APC space: “poor savers” (low income, low APC, lowest MPCs), an intermediate group (high income or high APC but not both), and “rich spenders” (high income and high APC, highest MPCs). The “rich spender” group has received little prior attention in consumption-savings models.

Critically, observable characteristics jointly explain at most 8% of MPC variation (adjusted R-squared from a measurement-error correction). With 92% of MPC heterogeneity unexplained by standard observables, the authors conclude that a substantial share of variation reflects latent household traits — plausibly heterogeneity in discount rates or intertemporal elasticities of substitution. This finding also limits the practical scope for government targeting of fiscal transfers: because observable characteristics predict little MPC variation, any targeting strategy can exploit only a small fraction of the overall distribution.

Scope conditions: results apply to household expenditure responses (marginal propensities to spend, not to consume in the strict sense) within one quarter of rebate receipt. The income-MPC positive correlation is confined to households within the income range eligible for the 2008 ESA (phased out above $150,000 for joint filers). The sample excludes the top and bottom 1.5% of consumption changes as outliers.

Q: What is the core methodological innovation of this paper? A: The paper applies Gaussian mixture linear regression (GMLR) to the 2008 tax rebate setting, jointly estimating group-level MPCs and household group membership probabilities without imposing any prior restriction on which observable characteristics drive heterogeneity. Because groups are determined by how well group-specific MPCs explain consumption patterns rather than by presupposed observables, the method recovers the full unconditional distribution of MPCs, including latent heterogeneity. This contrasts with sample-splitting approaches that can only recover co-variation with chosen characteristics.

Q: What are the three group-level MPCs for total expenditures, and what shares of the population do they represent? A: The three estimated MPCs are 0.04 (30% of households), 0.23 (48%), and 1.33 (23%), all with precisely estimated group shares (standard errors of 0.01). The largest MPC of 1.33 is statistically significant at the 1% level. The lowest MPC of 0.04 is not statistically different from zero even under the more favorable conditional standard errors that treat group assignment as known.

Q: How does the average MPC implied by the GMLR distribution compare to the homogeneous specification? A: The share-weighted average MPC from the three-group GMLR is 0.42, compared to 0.24 from the homogeneous (G=1) specification on the same data and identification strategy. This gap arises partly because the homogeneous estimate averages across households with very heterogeneous responses, and partly because the distribution has a right-skewed tail with a meaningful mass at MPC above 1.

Q: What are the MPC distributions for nondurable and durable goods separately? A: For nondurables, BIC selects two groups with MPCs of 0.09 and 0.18 and roughly equal population shares (48% and 52%); crucially, the lower bound of 0.09 is statistically distinguishable from zero at the 5% level, providing evidence that no household strictly follows the Permanent Income Hypothesis for nondurables. For durables, BIC selects three groups: MPCs of 0.03 (not distinguishable from zero, 29% of households), 0.15 (50%), and 0.67 (21%), reflecting the discrete, lumpy nature of durable goods purchases.

Q: How correlated are nondurable and durable MPCs at the household level? A: The correlation between household-level posterior predicted MPCs for nondurables and durables is 0.13, statistically significant at the 1% level. This rules out substitution between goods categories, but the positive complementarity is quantitatively small. The authors interpret this as possibly reflecting a small share of “spender” types who adjust multiple consumption categories in response to transitory income shocks.

Q: Which observable characteristics are individually correlated with MPCs? A: Homeowners have significantly higher MPCs than renters; households with a mortgage display even greater MPCs than outright homeowners. Both salary and non-salary income are positively correlated: households in the top tercile of salary income have MPCs about 0.13 higher than the omitted group, and top-tercile non-salary income households have MPCs about 0.015 higher (though the latter is individually less precisely estimated). The average propensity to consume (APC) is significantly positively correlated with the MPC, with a coefficient of 0.075 in univariate regression and 0.166 in the full joint specification.

Q: Which observable characteristics remain significant in the joint (multivariate) regression? A: When all household characteristics are included jointly, only income (both salary and non-salary components) and the APC remain robustly and positively correlated with MPCs. Top-tercile salary income is associated with 0.112 higher MPCs and top-tercile non-salary income with 0.049 higher MPCs, while the APC coefficient rises to 0.166 (from 0.075 univariate). Homeownership, age, education, and most demographic controls become statistically insignificant in the joint specification.

Q: What fraction of MPC variation is explained by observable characteristics? A: The adjusted R-squared from the full multivariate regression of predicted MPCs on all observable characteristics is approximately 6%. After a measurement-error correction proposed in Supplement A.6 to account for noise in estimated posterior MPCs, the corrected R-squared rises to 8%. Either way, the vast majority — over 90% — of MPC heterogeneity is unexplained by standard observables, implicating latent household traits such as heterogeneous discount rates or intertemporal elasticities of substitution.

Q: How does the extent of MPC heterogeneity recovered by GMLR compare to sample-splitting on observables? A: Table 4 shows that splitting by age terciles yields MPC estimates ranging from 0.13 to 0.34; splitting by total income yields a range of 0.18 to 0.45; splitting by the APC yields 0.06 to 0.21. All of these ranges are far narrower than the GMLR-recovered range of 0.04 to 1.33. The authors argue that sample-splitting on individual observables, which are noisy and correlated with only a portion of MPC heterogeneity, systematically understates the true extent of heterogeneity.

Q: What is the “rich spender” finding and why is it theoretically notable? A: Households with both high total income and a high prior average propensity to consume have the largest MPCs. This “rich spender” group is poorly accommodated by standard consumption-savings models: the canonical one-asset incomplete markets model typically predicts a negative MPC-APC correlation conditional on income, and the two-asset Kaplan-Violante (2014) model can generate wealthy hand-to-mouth households with high income and high MPCs, but not necessarily high APCs. Preference heterogeneity — e.g., heterogeneous intertemporal elasticities of substitution as in Aguiar, Boar, and Bils (2019) — can rationalize the positive income-APC-MPC nexus.

Q: What explains the positive income-MPC correlation, and how does the paper relate it to the prior literature? A: The paper notes that this positive correlation is consistent with Kueng (2018), who finds higher spending propensities among high-income recipients of Alaska Permanent Fund payments, and rationalizes it via near-rationality or mental accounting: when a rebate is small relative to income, the perceived cost of deviating from consumption smoothing is low. The authors also note that low-income households still exhibit large absolute MPCs, suggesting sizable deviations from consumption smoothing at the bottom of the income distribution, even if relatively lower than for high-income households.

Q: What are the policy implications for targeting fiscal transfers? A: The paper finds that the 2008 ESA increased spending for all households in partial equilibrium (minimum group MPC of 0.04, nondurable lower bound 0.09, all statistically positive or near-positive). Among observable characteristics, targeting relatively higher-income households (including retirees and entrepreneurs via non-salary income) would maximize aggregate consumption effects. However, since observables explain only 8% of MPC variation, any targeting strategy can exploit only a small fraction of the overall heterogeneity; the government faces fundamental limits on feasible targeting. This also implies a tension between stimulus and distributional/insurance motives for transfer programs.

Q: How does the paper confirm that recovered heterogeneity is not spurious? A: The authors generate 250 Monte Carlo samples from the estimated homogeneous model, impose G=3, and re-run the GMLR and observable regressions; they find significant relationships with observable characteristics in virtually none of these samples. Additionally, applying the BIC to homogeneous Monte Carlo samples, the BIC selects G=1 in all 250 samples, confirming that the selected G=3 in actual data reflects genuine heterogeneity rather than overfitting.

Q: How does GMLR compare to quantile regression for recovering the MPC distribution? A: Quantile regression (as used by Misra and Surico (2014) on the same data) recovers relationships at percentiles of the overall conditional distribution of consumption changes, so the ranking of households is driven by all sources of variation in consumption, not just the rebate response. If factors unrelated to the rebate dominate the conditional distribution, MPC heterogeneity will be underestimated in the presence of noise. The authors illustrate this formally in Supplement B and note that Misra and Surico (2014) find a substantial share of MPCs at or below zero for nondurables, in contrast to the GMLR lower bound of 0.09 that is statistically positive.

Q: What do the longer-run (lagged) MPC estimates show? A: The specification includes up to two lags of rebate indicators, allowing measurement of spending responses in subsequent quarters after rebate receipt. The paper reports these results (Section 4.4) but the text provided does not fully detail them; the heterogeneous structure is maintained across horizons.

Gaussian Mixture Linear Regression (GMLR): A probabilistic clustering regression approach that jointly estimates group-specific regression coefficients (here, MPCs) and population group shares by maximizing an expected log-likelihood via the EM algorithm. Households receive continuous posterior weights (gamma_{jg}) reflecting uncertainty about their group membership rather than binary hard assignment, with identification from a Gaussianity assumption on within-group errors.

Unconditional MPC Distribution: The full marginal distribution of MPCs across all households in the population, capturing heterogeneity from both observable and latent (unobservable) sources. Contrasted in the paper with the conditional distributions recovered by sample-splitting on observables, which by construction can only reflect co-variation with the chosen splitting variable.

Posterior Predicted MPC: For each household, the expectation of the group-specific MPC weighted by the household’s posterior group membership probabilities (lambda-tilde_{0,j} = sum_g gamma_{jg} lambda_{0g}). This object is the optimal (MSE-minimizing) individual-level MPC prediction and is the relevant input for targeted fiscal policy design.

Latent Heterogeneity: MPC variation that cannot be attributed to any observable household characteristic and is instead driven by unobserved traits — plausibly heterogeneous discount rates, intertemporal elasticities of substitution, or other preference parameters. Operationalized as the share of MPC variance unexplained by observable regressors (approximately 92% in this paper).

Rich Spenders: A group identified jointly in the APC-income space: households with both high total income and a high average propensity to consume, displaying the largest marginal propensities to consume out of the rebate. This group is not well-accommodated by standard one-asset or two-asset incomplete markets models under homogeneous preferences.

Average Propensity to Consume (APC): Defined empirically as average lagged consumption expenditures divided by total income, intended to capture persistent preference heterogeneity — a “spender type” — by measuring how much of income a household habitually spends before receiving the rebate. A one-percentage-point higher APC is associated with 0.19 additional cents spent per rebate dollar in the full multivariate specification.

Forbidden Comparisons: A bias identified by Borusyak et al. (2024) in event-study designs with staggered treatment, arising when newly treated units are compared to previously treated units rather than true controls. The paper addresses this by regressing consumption changes on rebate receipt indicators (iota_{jl}) directly rather than on rebate amounts, and including lagged rebate indicators to account for persistent effects.

Life-Cycle Wages and Human Capital Investments: Selection and Missing Data

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 – Overview

Research Question

This paper asks how wage inequalities build up over the life cycle when individual wage trajectories are plagued by interruptions in private-sector participation, and when the standard Missing At Random (MAR) assumption used to handle those gaps may be violated. Specifically, it asks: what is the causal effect of career interruptions on both the level and the dispersion of wages after twenty years of potential experience, and does endogeneity of those interruptions matter for the dispersion result?

Data and Sample

The empirical analysis uses the 2011 DADS Grand Format-EDP panel, a French administrative dataset merging social security records (DADS) and census extracts (EDP). The working sample covers males who entered the private sector between 1985 and 1992, aged 16-30 at entry, and observed through 2011. The authors require at least 15 years of observed private-sector wages, yielding a working sample of 7,004 males and 137,315 person-year observations. Education is grouped into four levels (high-school dropouts, high-school graduates, some college, college graduates). Participation outside the private sector – including public-sector employment, self-employment, unemployment, and non-employment – constitutes the “alternative sector” and generates missing wage observations. On average, cumulative duration outside the private sector is 3.7 years, and the average number of interruptions is 1.44.

Model and Methodology

The paper builds on a structural Ben Porath (1967) human capital model extended to two sectors (private sector and an alternative sector), yielding a reduced-form log-wage equation with five individual-specific coefficients: an intercept (initial human capital), a linear trend in potential experience (growth rate), a curvature term in potential experience (Mincer concavity), the cumulative years of interruptions, and a curvature term in interruptions. Because parameters are individual-specific, the wage equation is a random-coefficient model estimated with a fixed-effects approach.

Selection into the private sector is addressed not by a standard MAR assumption but by a weaker “Missing At Random Conditionally On Factors” (MARCOF) assumption. Sector-preference shocks, human capital prices, and depreciation rates are each decomposed into a common factor (time-varying) and an individual factor loading, plus a residual that is mean-independent of factors and loadings. Conditional on factors and factor loadings, wage residuals and sector choices are independent, making covariates – including the interruption variables – exogenous. The preferred specification includes two unobserved factors, selected by four of six Bai-Ng (2002) information criteria.

Estimation proceeds via an Expectation-Maximization (EM) algorithm adapted from Bai (2009) and Song (2013), with initial values from Moon and Weidner (2018)’s nuclear-norm convex estimator. Because individual parameters converge at rate sqrt(T) and summary statistics of their distributions suffer from incidental-parameter bias, the authors use bias-correction methods from Jochmans and Weidner (2019) for quantiles and inter-decile ranges, and from Arellano and Bonhomme (2012) for variances. Monte Carlo experiments confirm that variances remain poorly corrected even when T > 20, so the paper focuses on inter-decile ranges as the dispersion measure.

Counterfactual “average structural functions” (Blundell and Powell, 2003) are constructed by holding individual parameters fixed and manipulating the history of interruptions. These compare four scenarios: the observed benchmark, the counterfactual with no interruptions (potential wage), the counterfactual with no current-period selection, and both combined.

Main Findings

Downward bias from omitting interruptions and factors. Omitting interruption variables and unobserved factors strongly downward biases estimated returns to experience after 20 years. Most of this bias is attributable to interruptions rather than to the interactive factor effects: selectivity is mainly captured through the interruption channel, not through residual factor structure.
Effect on mean wages. Potential experience increases log wages by approximately 65% over 20 years, consistent with cross-country evidence from homogeneous Mincer equations. The average cost of interruptions after 20 years is approximately 10% of log wages. Reassigning interruptions to the beginning of the working life has a persistent negative effect on mean log wages that never fully recovers over 20 years, while reassigning them to the end increases mean wages above the no-interruption benchmark at every experience level.
Effect on wage dispersion – a new stylized fact. Interruptions decrease, not increase, the inter-decile range of log wages after 20 years. After 20 years, with an average interruption duration of 2.47 years, interruptions decrease the inter-decile range by 0.52 log points (approximately 38%). This compression operates differentially: the 90th percentile falls by 0.34 and the 10th percentile rises by 0.18.
Endogeneity explains the dispersion compression. When years of interruption are randomly reassigned across time (holding total interruption years fixed), the inter-decile range diverges upward from the observed benchmark after about 5 years. This shows that the dispersion-reducing effect of actual interruptions is due to the endogenous timing of those interruptions – specifically to the negative correlation between the timing of interruptions and potential log wages – rather than to the correlation between the structural coefficients on interruptions and potential wages (which is also negative, with a Spearman rank correlation of -0.32 between eta_i1 and eta_i3). Endogenously chosen interruptions smooth inequality over time.
Current-period selection is negligible. Current-period selection into private-sector employment has no statistically significant effect on median, mean, variance, or inter-decile range of wages at any experience level, as confirmed by the small inter-decile range of the interactive factor component.

Scope Conditions

Results pertain to cohorts of French males entering the private sector between 1985 and 1992, restricted to those with at least 15 observed private-sector years. The French context is distinctive: wage inequality in the working population was stable over 1985-2011, driven in part by minimum wage policy and payroll tax exemptions for lower-skilled workers, in contrast to rising inequality in the United States and Germany. Results on timing of interruptions (eta_i3 and eta_i4) are identified only for individuals with at least two interruptions followed by re-entry (roughly those with K_T >= 2). The paper does not analyze female wages.

In depth

Q1. What is the structural model and how does it generate a reduced-form wage equation?

The model is a Ben Porath (1967) two-sector human capital model in which individuals divide time between investing in human capital and earning wages in either the private sector (e) or an alternative sector (n). Human capital accumulation in each sector has a sector-specific return rate (rho^s) and depreciation (lambda^s_t). Period utility is log income minus a quadratic investment cost, plus a sector preference shock. Solving the dynamic program backwards (because of log-linearity) yields closed-form optimal investments that are linear in the individual-specific terminal value of human capital (kappa). The resulting log-wage equation (Proposition 5) is a function of five terms: an intercept (eta_i0), a linear trend in potential experience t (eta_i1), a geometric curvature term beta^{-t} (eta_i2), cumulative years of interruptions x^(3)_it (eta_i3), and a curvature in interruptions x^(4)_it (eta_i4), all with individual-specific coefficients. This provides a tractable random-coefficient structure.

Q2. What is the MARCOF assumption and why is it weaker than MAR?

MARCOF – Missing At Random Conditionally On Factors – posits that sector-preference shocks, human capital prices, and depreciation rates each follow factor structures: a common time-varying factor (phi_t) multiplied by an individual loading (theta_i) plus an i.i.d. residual. The residuals are assumed mean-independent of factors and loadings, and independent over time. Under standard MAR, missingness is assumed independent of outcomes conditional on observables alone. Under MARCOF, residuals in the wage equation and the sector choice equation are independent conditional on (unobserved) factors and factor loadings. This is weaker than MAR because it allows the unobservable determinants of wages and participation to share common factors, accommodating the high persistence observed in human capital stocks (20-year lag correlation of 0.28, far above the geometric decay benchmark of 0.024).

Q3. How are the individual-specific parameters identified?

Under exogenous selection (or, under MARCOF, conditional on factors), identification of eta_i0, eta_i1, and eta_i2 requires variation in potential experience within the individual’s time series. Identification of eta_i3 and eta_i4 separately requires individuals to experience at least two spells out of the private sector each followed by re-entry (at least four transitions, so K_T >= 2). An individual with only one interruption spell generates proportional variation in x^(3) and x^(4), so only a linear combination of eta_i3 and eta_i4 is identified. The “flat spot” approach – using the observed fact that individuals aged 50-55 have stopped investing in human capital – separately identifies time, cohort, and age effects and provides the restriction that factors are orthogonal to the level, trend, and curvature in potential experience.

Q4. What do the distributions of estimated individual-specific coefficients look like?

Focusing on the main (two-factor) specification with bias correction: the median of the growth parameter eta_i1 is positive (consistent with rising wages with experience) and the median of the curvature parameter eta_i2 is negative (consistent with concavity). However, heterogeneity is substantial: the 90th percentile of eta_i1 is 6.2 times the median, and the first quartile of eta_i1 is negative (implying declining potential wages for a non-negligible share). For the interruption coefficients eta_i3 (year of interruptions) and eta_i4 (curvature), bias-corrected medians are close to zero in the sub-sample with >=2 interruptions, but dispersion is large and symmetric around zero. Bias correction reduces the 90th percentile of eta_i1 by approximately 20% and reduces the absolute 10th percentile of eta_i3 by approximately 27%.

Q5. How important are interruptions relative to potential experience and factors in explaining wage variation?

A wage decomposition using inter-decile ranges (preferred over variance due to bias) shows that the potential experience component is the largest contributor to wage dispersion, followed by the interruption component (described as “sizable”), while factors play a minor role. Crucially, the potential experience and interruption components are highly negatively rank-correlated: the Spearman rank correlation between the growth coefficient eta_i1 and the interruption coefficient eta_i3 is -0.32. This negative correlation is central to understanding why interruptions compress dispersion rather than expanding it.

Q6. What is the finding on the effect of interruptions on mean wages, and what does the timing experiment show?

After 20 years, the average cost of interruptions (relative to a counterfactual of no interruptions) is approximately 10% of log wages. The timing of interruptions matters: reassigning interruptions to the beginning of the working life causes a persistent loss in mean log wages that does not fully recover over the 20-year horizon, while reassigning them to the end raises mean log wages above the no-interruption level at every experience level. For median wages, the early-interruption loss is eventually recovered (median log wages do catch up), but the mean does not catch up. These asymmetries are consistent with early interruptions having a larger negative effect on human capital accumulation due to the geometric structure of investment returns.

Q7. What is the key finding on wage dispersion and what explains it?

Interruptions compress the inter-decile range of log wages by 0.52 log points (approximately 38%) after 20 years, with average interruption duration of 2.47 years. This compression is asymmetric: the 90th percentile of wages falls by 0.34 and the 10th percentile rises by 0.18. The dispersion-reducing effect is established by comparing the benchmark (observed interruptions) to the counterfactual of no interruptions. When interruptions are instead randomly reassigned across time (holding total interruption duration fixed), the inter-decile range diverges upward from the benchmark starting around 5 years of experience. This demonstrates that the compression is due to the endogenous timing of interruptions – individuals who have high potential wages tend to time their interruptions in ways that reduce the measured spread of actual wages – rather than to the negative structural coefficient (eta_i3 < 0 for high-wage workers on average).

Q8. How does the paper handle the incidental parameter problem for distributional statistics?

Because individual parameters are estimated at rate sqrt(T) and the panel is unbalanced (some individuals observed for as few as 15 years while the model has up to 7 individual parameters), standard distributional statistics like the variance suffer from substantial incidental parameter bias. Monte Carlo experiments show that bias-corrected variance estimates remain strongly biased even at T > 20. Inter-decile ranges are better behaved and the Jochmans and Weidner (2019) bias-correction procedure reduces their bias satisfactorily. This is why the paper reports inter-decile ranges as its primary dispersion measure rather than variances. The bias in corrected inter-decile ranges is at most approximately 10% of the uncorrected estimate.

Q9. What does the paper show about the MAR assumption in the context of this data?

The results directly challenge the MAR assumption that is standard in the life-cycle earnings literature. Under MAR, interruptions would be treated as random conditional on observables, and their endogeneity would be ignored. The paper shows that treating interruptions as endogenous (through the MARCOF + structural model approach) substantially changes estimated returns to experience (there is a strong downward bias when interruptions and factors are omitted) and reverses the sign of the effect of interruptions on dispersion (under exogenous interruptions, randomly reassigned, dispersion would be higher than observed; the actual compression is an artifact of endogenous timing). The conclusion is that MAR assumptions produce systematically misleading pictures of life-cycle wage inequality dynamics.

Q10. What are the robustness and external validity considerations?

The working sample excludes individuals observed fewer than 15 years. A robustness exercise compares the subsample observed 10-14 years to a censored version of the 20+ subsample with matched marginal distributions of observation counts. Median profiles for the uncensored and censored 20+ samples are similar, and inter-decile ranges are slightly more dispersed in the censored sample only for potential experience greater than 7. However, the 10-14 year sample shows substantially different patterns – larger median gaps between benchmark and no-interruption cases, and a larger inter-decile range – consistent with lower private-sector returns to human capital for that group. The authors conclude that selection into the 15+ working sample matters, and results are explicitly restricted to that working sample. The French context (stable aggregate wage inequality, minimum wage policy) limits direct comparability to countries with rising inequality.

Key Concepts

MARCOF (Missing At Random Conditionally On Factors): The paper’s central identifying assumption, weaker than standard MAR. It posits that sector-preference shocks, human capital prices, and depreciation rates follow factor structures (common time-varying factor x individual loading + i.i.d. residual), and that residuals are mean-independent of factors, loadings, and their own histories. Conditional on factors and loadings, wage residuals and sector-choice residuals are independent, making selection exogenous.

Interactive effects / factor structure for selection: An approach in which unobserved confounders are modeled as a bilinear product of time-varying common factors (phi_t) and individual factor loadings (theta_i). This allows flexible correlation between wage processes and participation choices without requiring exclusion restrictions or instrumental variables. The paper’s preferred specification uses two unobserved factors identified by Bai-Ng information criteria.

Average structural functions: Objects defined by Blundell and Powell (2003) that integrate counterfactual outcomes (wages evaluated at a manipulated interruption history) over the distribution of individual-specific parameters. They allow estimation of the causal impact of a change in interruption timing or presence while holding individual structural parameters fixed, under identification conditions analogous to those of Chernozhukov et al. (2013).

Individual-specific coefficients (random coefficients): The five parameters (eta_i0, eta_i1, eta_i2, eta_i3, eta_i4) governing each individual’s wage equation, with structural interpretations: initial log human capital, return to potential experience, curvature (Mincer concavity), effect of cumulative interruption years, and curvature in interruptions. Their individual-specificity is the source of the incidental parameter problem for distributional statistics.

Flat spot approach: An identification device (from Heckman, Lochner, and Taber, 1998; Bowlus and Robinson, 2012) that uses median wages of workers aged 50-55 – who are assumed to have stopped investing in human capital – as consistent estimates of human capital prices by education group and year. This separates the volume of human capital from its price, and provides the restriction identifying the level, trend, and curvature factors from the time-varying unobserved factors phi_t.

Interruption variables x^(3) and x^(4): Reduced-form variables derived from the structural model summarizing the history of private-sector participation gaps. x^(3)_it is the cumulative number of periods spent in the alternative sector prior to date t; x^(4)_it is a geometric-weighted version of those interruptions that reflects the timing (early vs. late) through the discount factor beta. They enter the wage equation with individual-specific coefficients that are identified only for workers with at least two complete interruption spells.

Mincer dip: A U-shaped profile in wage variance (or inter-decile range) over potential experience, predicted by the Ben Porath model because high-return workers invest more at the start of their careers (reducing current wages), causing their wage profile to cross below then above low-return workers. Estimated in this paper at approximately 5 years of potential experience under the main specification.

Incidental parameter bias in distributional statistics: The bias that arises when estimating moments or quantiles of the distribution of individual-specific parameters that converge at rate sqrt(T) rather than sqrt(N). The paper shows through Monte Carlo experiments that variance estimates remain substantially biased even after Arellano-Bonhomme (2012) correction when T >= 20, while inter-decile ranges corrected by Jochmans-Weidner (2019) are more reliable.

Liquidity Traps, Prudential Policies, and International Spillovers

Mon, 01 Jan 0001 00:00:00 +0000

The paper develops a tractable open-economy New Keynesian model with nominal rigidities and an occasionally binding zero lower bound (ZLB) to study how monetary policy and macroprudential policy (modeled as a tax on capital flows) jointly transmit to output, capital flows, and the exchange rate, and what this implies for international spillovers and global welfare. An analytical decomposition identifies three transmission channels — intertemporal substitution, expenditure switching, and aggregate income — and the calibration finds that capital controls operate almost entirely through intertemporal substitution (about 95%), whereas expenditure switching accounts for roughly a quarter to a third of the effect of monetary policy. On the normative side, the authors show that, absent capital controls, monetary policy faces a tradeoff between stabilizing output today and curbing capital flows to lower the likelihood of a future liquidity trap, but that ’leaning against the wind’ (pre-emptively raising rates) is not necessarily optimal and can be counterproductive when tradables and non-tradables are highly substitutable. Quantitatively, adding capital controls lowers the average unemployment rate conditional on a liquidity trap from about 6% to about 1.5% and cuts the unconditional welfare cost of liquidity traps from about 0.4% to about 0.1% of permanent consumption, with an average ex-ante tax on inflows of about 0.2% and an average ex-post tax on outflows of about -0.05%. Finally, contrary to ‘currency war’ concerns, the authors argue that capital controls are not beggar-thy-neighbor: a country can use them to insulate itself from adverse foreign-policy spillovers (which operate through the world real interest rate), and coordination is beneficial only during a liquidity trap and works by stimulating rather than restricting flows. All results hold within their small-open-economy model under its calibration.

In depth

Q1. What is the model, and which policies does it study?

The paper studies an infinite-horizon small open economy with nominal rigidities and an occasionally binding zero lower bound on the nominal interest rate, in which the government has two instruments — the nominal interest rate (monetary policy) and a tax on capital flows (macroprudential policy). The economy has a tradable final good and a non-tradable good with sticky prices, and features aggregate demand externalities. The authors use this setting to ask three questions: how interrelated are the transmission channels of the two policies; how should monetary policy be used jointly with macroprudential policy; and what happens to global welfare when many countries adopt prudential policies simultaneously.

Q2. What are the three transmission channels, and how much does each matter?

An analytical decomposition (extending Kaplan, Moll and Violante 2018 and Auclert 2019 to an open economy) identifies three channels — intertemporal substitution, expenditure switching, and aggregate income — and the calibration shows monetary policy and capital controls operate through very different channels. The intertemporal substitution channel accounts for about 95% of the effect of capital controls, while expenditure switching (operating through exchange-rate depreciation that shifts demand toward non-tradables) accounts for a substantial share of the effect of monetary policy — the paper states ‘about one-third’ in its introduction and ‘about one-quarter’ in its conclusion. The expenditure-switching channel and the role of the exchange rate are what distinguish the open-economy decomposition from its closed-economy antecedents.

Q3. Do open capital markets amplify or dampen monetary policy?

Capital flows may either amplify or attenuate the output effects of monetary policy, depending on the relative sizes of the elasticity of substitution over time and the elasticity across sectors. If the intertemporal elasticity exceeds the intratemporal one, an open capital account amplifies monetary policy (a monetary expansion raises total consumption more than output, so households borrow from abroad); the result reverses when the intratemporal elasticity is larger, in which case a closed capital account produces the larger output expansion.

Q4. Is ’leaning against the wind’ the optimal prudential use of monetary policy?

Contrary to a widespread policy view, leaning against the wind is not necessarily optimal: when the elasticity of substitution across sectors is higher than across time, raising the interest rate ahead of a liquidity trap can be counterproductive. In that case a rate hike generates a large negative expenditure-switching effect and a sharp income drop while only modestly reducing consumption, so in general equilibrium it leads to capital inflows and more external debt — exacerbating the aggregate demand externality and making a future contraction more likely. The implication is that a prudential monetary policy may require lowering, not raising, the interest rate ahead of a liquidity trap.

Q5. How should monetary and macroprudential policy be combined, and how pre-emptively?

When capital controls are available, the central bank uses monetary policy to stabilize output and uses the capital-flow tax to manage flows, with the macroprudential tax on debt positive only if the ZLB is likely to bind next period; monetary policy, by contrast, must be used prudentially even when the ZLB binds only in some distant future. Because monetary policy is a blunter instrument, it has to be used more pre-emptively than capital controls. The authors also show the central bank may restrict outflows during a liquidity trap when that trap is either temporary or very severe.

Q6. What are the quantitative welfare and unemployment gains from capital controls?

Adding capital controls substantially improves macroeconomic stabilization: average unemployment conditional on a liquidity trap falls from about 6% to about 1.5%, and the unconditional welfare cost of liquidity traps falls from about 0.4% to about 0.1% of permanent consumption — more than a fourfold reduction. The average ex-ante prudential tax on inflows is about 0.2% and the average ex-post tax on outflows is about -0.05%. The authors also note that, with capital controls, liquidity traps are less frequent and less severe but — perhaps surprisingly — tend to last longer.

Q7. Are capital controls beggar-thy-neighbor, and how do international spillovers work?

The authors argue that, contrary to emerging policy concerns, capital controls are not beggar-thy-neighbor and can enhance global macroeconomic stability; international spillovers operate through the world real interest rate, and a country can use capital controls to insulate itself from adverse foreign policies. In their multi-country extension, a country can remain insulated from negative spillovers of a change in the foreign monetary stance through capital controls, which can help prevent the outbreak of a currency war.

Q8. When is international policy coordination desirable?

The authors provide conditions under which a regime of uncoordinated capital controls can dominate laissez-faire, and they find that coordination is desirable only during a liquidity trap — where, notably, it calls for stimulating capital flows rather than preventing them. This stands against the view that uncoordinated capital-control policies necessarily produce a global paradox of thrift.

Q9. How do these results differ from prior open-economy liquidity-trap models?

The paper’s more benign view of spillovers contrasts with contributions such as Caballero, Farhi and Gourinchas (2021), Eggertsson et al. (2016), and Fornaro and Romei (2019), and the authors trace the difference to two features of their model: positive liquidity and the presence of ex-post capital controls. Because goods subject to nominal rigidities are consumed only domestically, foreign policies that favor savings (lowering the world interest rate) raise demand for domestic goods through asset markets and can be stabilizing at the ZLB; and ex-post controls let the central bank actively manage flows during a trap to offset adverse spillovers.

Key concepts

aggregate demand externality : the externality (as in Schmitt-Grohe and Uribe 2016 and Farhi and Werning 2016) by which an individual agent’s borrowing raises external debt and, given nominal rigidities and the ZLB, makes the economy more vulnerable to a future demand-driven contraction; it is the market failure that prudential policy targets in this model.

expenditure switching channel : the open-economy transmission channel through which an exchange-rate depreciation makes non-tradables relatively cheaper, shifting demand toward domestically produced goods; the paper finds it accounts for a substantial share (roughly a quarter to a third) of monetary policy’s effect.

intertemporal substitution channel : the channel through which a change in the intertemporal price shifts consumption between present and future; it accounts for about 95% of the effect of capital controls in the calibration.

liquidity trap / occasionally binding ZLB : a state in which the zero lower bound on the nominal interest rate binds, so conventional monetary policy cannot stabilize output; the risk of entering such a state in the future is what makes pre-emptive prudential policy valuable here.

capital controls (prudential tax on flows) : the macroprudential instrument in the model — a tax on capital inflows (ex ante) or outflows (ex post) — used to manage the level and timing of capital flows and to insulate the economy from foreign spillovers.

beggar-thy-neighbor : a policy that improves one country’s outcomes at others’ expense; the paper argues capital controls are, contrary to common concern, not beggar-thy-neighbor in its setting and can raise global stability.

Local Projection-Based Inference under General Conditions

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a uniform asymptotic theory for local projection (LP) regression under general conditions, addressing a gap in the literature where existing results required restrictive assumptions about lag order, data persistence, and shock processes. The research question is: how can one conduct valid statistical inference on impulse responses from LP regressions when the true lag order is unknown (possibly infinite), data exhibit arbitrary persistence including unit roots and near-unit roots, horizons are allowed to grow with sample size, and shocks follow general conditionally heteroskedastic martingale difference sequences (MDS)?

The paper works within a VAR(infinity) data-generating process framework, where the vector autoregression may have an unknown and potentially infinite number of lags. The LP regression truncates this at a chosen model order p, with the truncation bias controlled by tail decay conditions on the VAR coefficients. The theoretical framework accommodates a class of VARMA models as a specific illustration, showing that Assumptions 1 and 2 hold for VARMA(q+1, r) processes when the model lag order p diverges at least as fast as log n.

The main theoretical result (Theorem 1) establishes uniform asymptotic normality of the LP estimator, simultaneously over: the coefficient parameter space A, model lag orders p in [p_low, p_high], horizons h in [1, h_bar], and configurations of the linear combination vector gamma (covering both individual and cumulated impulse responses). The convergence rate is pi_1(h; gamma)^{-1/2} n^{1/2}, which depends on persistence level and horizon. For an AR(1) process, the individual response rate is (sum_{i=0}^{h-1} a_1^{2i})^{-1/2} n^{1/2} and the cumulative response rate is h^{-3/2} n^{1/2}, which is slower.

The paper makes two principal contributions. First, LP is shown to be semiparametrically efficient when the controlled lag order diverges. Under classical assumptions (homoskedastic MDS shocks, stationarity, fixed horizon), the LP estimator achieves the same asymptotic distribution as the VAR-implied iterative estimator, and reaches the semiparametric efficiency bound of Chamberlain (1987) under the conditional moment restriction model. Under Gaussianity, LP is asymptotically Cramer-Rao efficient. This extends Plagborg-Moller and Wolf (2021) from distributional equivalence of estimands to equivalence of asymptotic distributions. The commonly held view that LP is inefficient relative to VAR-implied methods holds only under finite small-order VAR models; with a diverging lag order, the efficiency gain from the parsimonious VAR structure vanishes. The alternative LP estimator of Lusompa (2022), shown to be more efficient than standard LP under a known AR(1) model, is likewise shown (Proposition 2) to be asymptotically equivalent to standard LP when a sufficiently large lag order is used (p_u/sqrt(n) -> 0 and sqrt(n)(1-|rho|)^{p_u} -> 0).

Second, two new standard errors are proposed, neither involving HAR-type correction or bandwidth selection. SE_1 is a White-style heteroskedasticity-robust standard error applied after partialling out controls; it is uniformly consistent under a zero fourth cumulant condition on shocks (e.g., zero excess kurtosis with conditional homoskedasticity), but not for general MDS shocks. SE_2, the paper’s main methodological contribution, constructs the variance estimator using martingale-transformed scores: the LP residual Delta_t is projected onto forward residuals (Delta_{t+1}, …, Delta_{t+h-1}) to partial out serial dependence, recovering the true MDS error xi_{1t}(h; gamma) asymptotically. SE_2 is uniformly consistent for general MDS shocks (Proposition 4) and, under a finite-order VAR DGP, requires only p = p_true lags (rather than p >= p_true + 1 required by SE_1 and HAR-type methods).

Simulations using univariate ARMA(1,1) models with rho in {0, 0.5, 0.95, 1} and theta in {-0.5, 0, 0.5}, and bivariate VAR(1) models, confirm that SE_2-based 95% confidence intervals maintain coverage close to the nominal level across all cases including unit roots, while SE_1 shows degraded coverage under conditional heteroskedasticity (GARCH). Both outperform MOPM for cumulated responses at longer horizons.

Scope conditions: the framework accommodates data with unit roots and near-unit roots but not explosive roots or integration of order greater than one (for which differencing is prescribed before applying the LP). The growing-horizon rate condition p^2 h^2 / n -> 0 becomes binding as h grows, requiring h and p to grow at comparable rates or p more slowly. The results are for the VAR framework and do not directly apply to structural (SVAR) identification without additional assumptions.

Q: What is the central inferential problem that motivates this paper?

A: Applied macroeconomists estimating impulse responses via LP regressions face a trilemma: the true lag order is unknown and may be infinite, data may be highly persistent or integrated, and shocks may be conditionally heteroskedastic. Existing uniform validity results (chiefly Montiel Olea and Plagborg-Møller 2021) assume a finite and known model order and require mean-independent shocks, leaving inference potentially invalid when these conditions fail. The paper constructs a theory and inference procedures that remain valid simultaneously over all these dimensions.

Q: What is the VAR(infinity) data-generating process assumed, and what are the key restrictions on it?

A: The DGP is yt = sum_{j=1}^{infinity} a_j y_{t-j} + u_t, where u_t is serially uncorrelated. Assumption 1 bounds the impulse responses uniformly over the parameter space (ruling out explosive roots and integration of order greater than one). Assumption 2 imposes that the tail coefficients a_j decay fast enough that the truncation bias is asymptotically negligible: the rate condition requires sqrt(n) * p * sum_{j=1}^{infinity} j |a_{p+j}| -> 0, implying p must diverge for infinite-order processes. For VARMA models, p need only diverge as slowly as log n.

Q: What does Theorem 1 establish, and what is the convergence rate?

A: Theorem 1 establishes uniform asymptotic normality of the LP estimator, with the supremum taken jointly over the coefficient space A, lag orders p in [p_low, p_high], horizons h in [1, h_bar], and the linear combination vector gamma. The convergence rate is pi_1(h; gamma)^{-1/2} n^{1/2}, where pi_1(h; gamma) = sum_{i=1}^{h} |phi_{1i}|^2 captures persistence and horizon effects. For an AR(1) process, the individual response rate is (sum_{i=0}^{h-1} a_1^{2i})^{-1/2} n^{1/2} and the cumulative response rate is the slower h^{-3/2} n^{1/2}.

Q: In what sense is LP semiparametrically efficient, and under what assumptions?

A: Under classical assumptions — homoskedastic MDS shocks, stationarity, and fixed horizon — when the controlled lag order p diverges at the appropriate rate, the LP estimator reaches the semiparametric efficiency bound of Chamberlain (1987) under the conditional moment restriction model E(yt - sum a_j y_{t-j} | ys, s <= t-1) = 0. It achieves the same asymptotic distribution as the VAR-implied estimator, which itself has the same distribution as the LP estimator under these conditions (established by extending Lutkepohl 1990). Under Gaussianity, LP is asymptotically Cramer-Rao efficient.

Q: Why does the efficiency advantage of VAR-implied methods over LP vanish with a large lag order?

A: Under a finite, small-order VAR model, imposing the functional relationship between all impulse responses and a small set of VAR slope parameters — analogous to dimension reduction in a factor model — yields an efficiency gain for the iterative VAR-implied estimator. However, as the model lag order grows, the number of parameters to estimate grows correspondingly, eroding the dimension-reduction benefit. With a diverging lag order, the extraction of common parameters through a parsimonious model no longer tightens the asymptotic variance of the VAR-implied estimator relative to the direct LP estimator.

Q: How does SE_2 avoid the need for HAR (heteroskedasticity and autocorrelation robust) bandwidth selection?

A: The LP regression error Delta_t(h; gamma) is serially correlated for h >= 2 (it contains MA terms of order h-1), which would normally require HAR correction. SE_2 avoids this by constructing the variance estimator from the martingale-transformed score: the LP residual Delta_t is regressed on the forward residuals (Delta_{t+1}, …, Delta_{t+h-1}) and the fitted residual hat{xi}{1t} is used in place of Delta_t. Asymptotically, hat{xi}{1t} recovers the true LP(infinity) error xi_{1t}(h; gamma) = sum_{i=1}^{h} phi’{1i} u{t+i}, which is a MDS with respect to {u_t, u_{t-1}, …}. Since MDS sums have a martingale structure, their variance can be estimated as a simple sum of squares without bandwidth selection.

Q: Under what condition is SE_1 uniformly consistent, and when does it fail?

A: SE_1 is the standard White heteroskedasticity-robust variance estimator applied to the partialled-out score. It is uniformly consistent under the zero fourth cumulant condition on shocks — that is, when u_t has zero excess kurtosis and is conditionally homoskedastic. This condition fails for general MDS shocks (e.g., GARCH-type shocks), because the cross-moment Cov((tau’w_0)^2, (tau’w_k)^2) does not vanish in general. Simulation results confirm that SE_1-based confidence intervals show degraded coverage under GARCH shocks, while SE_2 maintains coverage.

Q: What is the relationship between this paper and Montiel Olea and Plagborg-Møller (2021)?

A: Montiel Olea and Plagborg-Møller (2021) (MOPM) established uniform validity of LP inference under a finite-order, known VAR model and required mean-independent (not merely MDS) shocks. The current paper extends MOPM in five dimensions: it allows an unknown and potentially infinite true lag order; allows the controlled lag order to diverge; develops new asymptotic theory for general MDS shocks; proposes SE_2 whose consistency does not require mean-independent shocks; and unifies inference for both individual and cumulated impulse responses. The lag-augmented LP regression of MOPM (setting p = p_true + 1) is a special case of the framework here.

Q: What does the paper show about the alternative LP estimator of Lusompa (2022)?

A: Lusompa (2022) showed that, under a known AR(1) model with the true lag order, an alternative LP estimator that exploits the serial dependence structure of the LP error is asymptotically more efficient than standard LP across horizons. Proposition 2 of the current paper shows this efficiency gain does not survive when a sufficiently large lag order is used for the preliminary VAR used to compute the transformation. Specifically, when p_u/sqrt(n) -> 0 and sqrt(n)(1-|rho|)^{p_u} -> 0, the alternative and standard LP estimators are asymptotically equivalent: sqrt(n)[tilde{beta}_1(h) - beta_1(h)] - sqrt(n)[hat{beta}_1(h) - beta_1(h)] = o_p(1). The discrepancy arises from estimation errors in the preliminary residuals entering the asymptotic distribution.

Q: What are the rate conditions on the lag order p and horizon h, and how do they compare to VAR-implied methods?

A: Under a fixed horizon, the condition p^2/n -> 0 suffices for LP, which is weaker than the p^3/n -> 0 typically required for VAR-implied methods (the stricter condition arises because VAR-implied methods must estimate all p slope matrices jointly, while LP treats all but the first as nuisance). Under growing horizons (h -> infinity), the rate condition is p^2 h^2/n -> 0, and the analysis shows p = O(h) is sometimes optimal — p and h should grow at the same rate or p more slowly. By contrast, VAR-implied methods require p = o(n^{1/3}/h^{2/3}) under growing horizons.

Q: What is the lag order flexibility advantage of SE_2 under a finite-order VAR DGP?

A: When the true DGP is a finite-order VAR(p_true), SE_2 achieves consistent inference using exactly p = p_true lags — the exact order. In contrast, SE_1 and HAR-type standard errors require p >= p_true + 1 (at least one extra lag) because at p = p_true the LP residuals Delta_t(h; gamma) contain MA terms of order h-1 that create serial dependence. SE_2’s martingale transformation handles this serial dependence directly, without requiring the extra lag to purge it.

Q: What scope conditions limit the paper’s framework?

A: The framework rules out explosive roots (violating the uniform impulse response bound in Assumption 1) and integration of order two or higher (violating Assumption 1(iii)). For I(2) variables, the prescribed solution is to take differences before applying the LP, and then use the cumulated response (gamma = gamma_CIR) to recover original level responses. The growing-horizon results require the tension condition h_bar * p^2 / n -> 0 (for gamma with ||gamma||_1 = O(1)), implying a binding tradeoff between the range of allowed horizons and the range of allowed lag orders. Results do not directly extend to structural identification without additional assumptions.

Local Projection (LP) regression: A direct regression of the outcome h periods ahead on current and lagged endogenous variables, as in Jorda (2005). The LP estimator of the horizon-h impulse response is the OLS coefficient on the current endogenous variable in this regression, with p-1 lags included as controls. It estimates impulse responses directly for each horizon without imposing the recursive structure of a VAR model.

Uniform asymptotic validity: A distributional approximation (here, standard normal) that holds simultaneously over a parameter space A, a range of model lag orders [p_low, p_high], a range of horizons [1, h_bar], and specifications of the linear combination vector gamma — not merely pointwise for fixed parameter values. Uniformity is the operative concept ensuring finite-sample reliability across empirically relevant configurations.

Semiparametric efficiency: In the paper’s usage, the LP estimator achieves the efficiency bound of Chamberlain (1987) for the semiparametric conditional moment restriction model E(yt - sum a_j y_{t-j} | ys, s <= t-1) = 0 when the controlled lag order diverges. Under Gaussianity, this coincides with Cramer-Rao efficiency. The key result is that the efficiency loss of LP relative to VAR-implied methods — well-documented under finite small-order VAR — is asymptotically negligible once the lag order diverges.

Martingale difference sequence (MDS) shocks: The shock process u_t satisfying E(u_t | u_s, s <= t-1) = 0 almost surely — a condition weaker than mean independence (E(u_t | u_s, s <= t-1) = 0 for all functions of past shocks). MDS shocks include GARCH and stochastic volatility processes. The paper’s SE_2 is designed to be consistent for general MDS shocks, while SE_1 and MOPM require the stronger mean-independence condition.

SE_2 (martingale-transformed standard error): The paper’s proposed standard error, constructed by first regressing LP residuals Delta_t on their forward values (Delta_{t+1}, …, Delta_{t+h-1}) to partial out serial dependence, then using the residual hat{xi}{1t} in the variance estimator as a simple sum of squares. SE_2 is uniformly consistent for general MDS shocks and requires no bandwidth selection, because the residual hat{xi}{1t} asymptotically recovers the MDS LP(infinity) error xi_{1t}(h; gamma).

VAR(infinity) model: A vector autoregression yt = sum_{j=1}^{infinity} a_j y_{t-j} + u_t with potentially infinitely many lags. The paper’s framework treats the true lag order as unknown and possibly infinite, requiring the controlled lag order p in the LP regression to diverge (at a rate constrained by Assumption 2) so that truncation bias becomes asymptotically negligible. VARMA processes are a special case shown to satisfy the paper’s assumptions.

Cumulated impulse response: The linear combination beta_1(h; gamma_CIR) = sum_{j=1}^{h} beta_1(j), corresponding to gamma = (1, …, 1)’. Cumulated responses exhibit slower convergence rates than individual responses — h^{-3/2} n^{1/2} versus (sum_{i=0}^{h-1} a_1^{2i})^{-1/2} n^{1/2} for an AR(1) — and are especially relevant when the response variable is in differences and the researcher seeks level responses of the original variable.

Loose Monetary Policy and Financial Instability

Mon, 01 Jan 0001 00:00:00 +0000

This paper provides the first long-run causal evidence that a persistently loose stance of monetary policy — defined as extended periods of low interest rates relative to the neutral rate — significantly raises the probability of a financial crisis several years later. Using a long historical panel of 18 advanced economies (approximately 1870–2020, excluding world wars), the paper estimates local projection (LP) regressions in which the stance is measured as the 5-year backward moving average of (r – r*), with r* from the Del Negro–Giannoni–Gaballo–Tambalotti (DGGT) factor model. The OLS baseline finds that a 1 percentage-point (pp) looser average stance over a 5-year window raises the 3-year financial crisis probability by 2.2pp at a 5–7 year horizon and 3.3pp at a 7–9 year horizon, against an unconditional base of 10.5%. To address the endogeneity of monetary policy to pre-existing economic conditions, the authors construct an instrumental variable based on the international trilemma of open-economy finance: for countries pegging their exchange rate, changes in the base-country interest rate orthogonal to domestic economic conditions provide exogenous variation in domestic rates, weighted by a capital mobility index. IV estimates are substantially larger: 1pp looser average stance raises crisis probability by 5.5pp at 5–7 years and 15.5pp at 7–9 years, indicating that OLS understates the causal effect because accommodative policy is endogenously adopted during recessions when crisis risk is already low. The same loose-policy stance significantly raises the probability of entering R-zones — periods of credit market overheating identified by Greenwood, Hanson, Shleifer, and Sørensen (2022) as harbingers of financial crisis — and, with a lag of 6–9 years, raises the probability of historically low GDP growth (below the 20th percentile of the cross-country distribution). The evidence supports a growth-risk tradeoff: loose policy may deliver short-term stimulus, but at a meaningful cost in medium-term financial fragility and real tail risk.

Data and sample (Section 2): 18 advanced economies, long historical panel from the 1870s to 2020, excluding the world war episodes (pre-1914, interwar, and 1939–1945 conflicts), yielding an unbalanced panel of roughly 1,500 country-year observations. Financial crisis dates from the Jordà–Schularick–Taylor (2017) Macrofinancial History Database. The stance measure is r_{i,t} − r*{i,t}, where r*{i,t} is country-specific and time-varying, estimated from a factor model (DGGT); the 5-year backward moving average smooths over cyclical fluctuations and captures the sustained character of monetary accommodation that theory associates with financial fragility buildup. The unconditional 3-year financial crisis probability in the post-WWII sample is 10.5%.

Empirical methodology (Section 3): Local projections (Jordà 2005) with financial crisis indicator B_{i,t} as the outcome and 5-year backward MA of stance as the key regressor, estimated at horizons h = 0 to 12 years:

B_{i,t+h} = α_{i} + β_{h} · stance_{i,t} + γ_{h} · X_{i,t} + ε_{i,t+h}

Controls X_{i,t} include: lagged B (crisis history), lagged stance, lagged log GDP growth, lagged credit-to-GDP growth, lagged inflation, and lagged short-term rate — plus global controls (cross-country averages) to absorb common factors. Country fixed effects α_{i} and Driscoll–Kraay (1998) standard errors with h lags account for serial correlation and cross-sectional dependence. The coefficient −100β_{h} converts to the change in 3-year crisis probability (in percentage points) per 1pp tighter stance, so a positive −100β_{h} means a looser stance raises crisis probability.

OLS baseline results (Section 4.1): The baseline LP-OLS model (Figure 3, panel (a)) finds no significant association between stance and crisis probability in the first 4 years after the policy window — loose monetary policy does not immediately raise crisis risk. Crisis probability rises meaningfully from horizons 5 onward:

5–7 year horizon: +2.2pp crisis probability per 1pp lower average stance
7–9 year horizon: +3.3pp crisis probability per 1pp lower average stance
Very loose indicator (stance at the 20th percentile, approximately −2.5%): +13pp at the peak horizon; when stance = −1%, crisis probability is approximately 16% (vs unconditional 10.5%)
Alternative chronology (Baron–Verner–Xiong 2021, bank equity crash events): +5.3pp at the 8-year horizon per 1pp lower stance — broadly consistent with the baseline

R-zone analysis (Section 4.2): Greenwood, Hanson, Shleifer, and Sørensen (2022) define R-zones as periods when household or business credit grows anomalously fast — a pre-crisis credit overheating indicator. LP-OLS estimates show:

1pp lower average stance → +3.2pp household R-zone probability within 5 years; +1.8pp business R-zone probability
Very-loose binary indicator (bottom quintile of stance) → +9.6 to 10.8pp R-zone probability These magnitudes confirm that the financial instability buildup operates through the canonical credit channel: loose monetary policy inflates credit volumes first, with financial crises following several years later.

Eurozone periphery illustration (Section 4.2): The pre-2008 divergence between the ECB’s common stance and country-specific neutral rates is shown in Figure 10. Core eurozone countries (Belgium, Denmark, France, Germany, Netherlands) experienced tight-to-neutral effective stances during 2003–2008, while periphery countries (Ireland, Italy, Portugal, Spain) faced loose stances of up to approximately −10pp. The periphery’s credit boom — in total credit, household credit, mortgage credit, and house prices — far exceeded the core’s over 2002–2008, consistent with the LP-OLS estimates. This pattern motivates the IV strategy.

IV construction (Section 4.3): The instrument follows Jordà, Schularick, and Taylor (2020) and uses the international monetary trilemma. For countries pegging their exchange rate (identified by exchange rate stability), the domestic interest rate is mechanically tied to the base country’s rate; the instrument is:

z_{i,t} = k_{i,t} × (ΔR_{b(i,t),t} − ΔR̂_{b(i,t),t})

where k_{i,t} is a Chinn–Ito capital mobility index, b(i,t) is the base country for country i in year t, ΔR_{b,t} is the actual change in the base country’s interest rate, and ΔR̂_{b,t} is the predicted change obtained from a first-stage regression of base-country rates on base-country economic conditions. The residual captures shifts in the base country’s rate that are orthogonal to economic fundamentals and are transmitted to pegged countries via the exchange rate commitment — exogenous from the perspective of the pegged country. Ten lags of z are used as instruments for the 5-year moving average of stance. The Kleibergen–Paap (2006) test for weak instruments exceeds 10 across all first-stage regressions.

IV second-stage results (Figure 11): The IV estimates are substantially larger than OLS throughout the horizon:

5–7 year horizon: +5.5pp crisis probability per 1pp lower average stance (vs +2.2pp OLS)
7–9 year horizon: +15.5pp per 1pp lower average stance (vs +3.3pp OLS)
With stance = −1%, the IV-implied crisis probability is 16% at 5–7 years; at 7–9 years, medium-term crisis risk more than doubles from the unconditional 10.5% to over 20%
These IV estimates are 2.5× to 5× the OLS, implying substantial attenuation bias in OLS: monetary policy is endogenously loosened during downturns when crisis risk is already low, so reverse causality compresses the OLS coefficient toward zero

IV R-zones (Figure 13): LP-IV estimates for household and business R-zones confirm the LP-OLS direction — loose monetary policy raises the likelihood of entering credit market overheating as defined by Greenwood et al. (2022), at economically relevant magnitudes in the post-WWII period.

Growth-risk tradeoff (Section 5): To close the circle between monetary policy, financial fragility, and real activity, the paper estimates LP models with tail real growth indicators as outcomes. Define Low-Output-Growth_{i,t} = 1{Δ₃(log Y_{i,t}) < 20th percentile} — an indicator for historically low 3-year real GDP per capita growth. The 20th percentile in the sample corresponds to positive growth of 1.32%. Results (Figure 14a):

No significant relationship between stance and Low-Output-Growth probability in the first 4–5 years — consistent with the idea that short-term stimulus benefits materialize before financial fragility builds
At horizons 6–9 years: when stance is 1pp looser, the probability that Low-Output-Growth turns on rises by 2pp (at 8 years) and 3pp (at 9 years), significant at the 32% (5%) level at h=8 (h=9)
For Barro–Ursua (2008) disaster events (peak-to-trough falls in real GDP per capita of ≥10%, 3.2% of sample observations): the disaster probability follows a similar hump — slightly lower disaster risk in the short term under loose policy (the stimulus dividend), followed by materially higher disaster risk at 7–9 years (Figure 14b)
Conclusion: loose monetary policy produces a growth-risk tradeoff, where short-run stimulus gains are offset by elevated medium-term tail risk in financial and real activity

Scope conditions: The paper documents empirical regularities from long historical data; it does not build or estimate a structural model, so it cannot formally decompose the mechanisms driving the reduced-form effects (risk-taking channel, credit-boom channel, or asset-price inflation). The stance measure (r − r*) depends on estimates of the time-varying neutral rate, which carries its own uncertainty; robustness using alternative r* measures is presented. The IV relies on countries pegging their exchange rate, which varies across time and countries; results may not generalize to monetary unions or fully flexible exchange rate regimes where the trilemma applies differently. The sample of 18 advanced economies may not be representative of emerging market contexts. The analysis is positive, not normative: it does not compute welfare-optimal monetary policy rules that account for the intertemporal tradeoff.

In depth

Q1. Why does the paper measure stance as a 5-year backward moving average rather than the contemporaneous rate gap?

The 5-year moving average captures the sustained character of loose monetary policy that theory associates with financial fragility accumulation; a single quarter of low rates does not meaningfully alter bank balance sheets or credit market dynamics, but several years of below-neutral rates allow risk appetite to build up gradually through reach-for-yield behavior, leveraging, and lending standard erosion. The backward average also corresponds more naturally to the length of a typical financial cycle (Borio 2014), over which excessive credit and asset price growth gradually accumulates before a crisis materializes. Using the contemporaneous rate gap would miss the cumulative nature of the stance and would likely attenuate the estimated effect toward zero because any individual year’s rate is highly endogenous to the current cyclical position.

Q2. Why are the IV estimates so much larger than the OLS estimates, and what does this imply about the direction of endogeneity bias?

The IV estimates (5.5pp at 5–7 years, 15.5pp at 7–9 years) are roughly 2.5× to 5× the OLS estimates (2.2pp and 3.3pp), implying that OLS is severely attenuated by reverse causality: central banks endogenously loosen policy during recessions and financial downturns — precisely the states in which crisis risk is temporarily depressed — so the OLS coefficient conflates the true causal effect (loose policy raises crisis risk) with an offsetting correlation (loose policy coincides with post-crisis low-risk states). The trilemma IV isolates the exogenous component of the stance — changes transmitted to pegged countries by the base-country’s monetary decisions that are orthogonal to the pegged country’s own economic conditions — and strips away this endogeneity, revealing that the true causal effect on crisis risk is substantially larger than OLS suggests. This finding matters for policy: it implies that the textbook concerns about risk-taking and financial cycle effects of low rates are not only statistically detectable but quantitatively much more important than naive correlations suggest.

Q3. How does the trilemma instrument achieve exogenous variation in domestic monetary conditions?

For countries pegging their exchange rate, the trilemma forces domestic interest rates to shadow the base country’s rate (usually the US, Germany, or the UK); when the base country cuts rates for reasons driven by its own domestic conditions — unrelated to the pegged country’s economic state — the pegged country inherits looser monetary conditions through the exchange rate commitment. The instrument refines this logic by: (i) using the residual of the base-country rate change after partialling out the base country’s own macro fundamentals, eliminating the component of the base-country cut that might be correlated globally with crisis risk; and (ii) weighting by the capital mobility index k_{i,t}, so that the instrument is strongest when capital flows freely and the trilemma constraint is tightest. The exclusion restriction requires that these exogenous shifts in the base-country rate affect the pegged country’s financial crisis probability only through the channel of domestic monetary conditions, not through other international spillovers (e.g., trade or capital flow channels).

Q4. What is the timing pattern of crisis risk accumulation and what explains the absence of an effect in the first four years?

Crisis risk does not rise in the first 4 years after a period of loose monetary policy, rises sharply at 5–7 years (5.5pp IV), and peaks at 7–9 years (15.5pp IV) — the “slow burn” pattern reflects the lag between credit market overheating and realized financial crises. The mechanism links stance to crisis through the intermediary of credit booms: the paper shows (Figure 13) that R-zones (credit overheating) build within 5 years of loose policy, and the literature (Schularick–Taylor 2012; Jordà–Schularick–Taylor 2015) has established that credit booms predict financial crises with similar multi-year lags. The short-term absence of elevated crisis risk is consistent with — and not in tension with — the Barro–Ursua disaster results, which show lower disaster probability in the short term under loose policy, capturing the genuine stimulus dividend before the financial fragility materializes.

Q5. What are R-zones and what role do they play in the paper’s chain of evidence?

R-zones (Greenwood, Hanson, Shleifer, and Sørensen 2022) are periods when household or business credit grows anomalously fast relative to historical norms, identified as leading indicators of subsequent financial distress; the paper uses them to establish a link in the causal chain: loose monetary policy → credit overheating → financial crisis, providing a mechanism-level bridge between the reduced-form IV results. The R-zone regressions show that loose policy raises the household R-zone probability by 3.2pp and business R-zone by 1.8pp within 5 years (OLS; LP-IV confirms the direction), implying that the credit channel is active within the financial cycle window before the eventual crisis materializes. This is important because it distinguishes the paper’s finding from a pure statistical correlation between stance and crisis: the financial system’s credit overheating is a detectable intermediate state that connects loose policy to the eventual fragility outcome.

Q6. What does the growth-risk tradeoff finding imply for the welfare calculus of monetary accommodation?

The short-term benefits of loose policy (higher output, lower unemployment in the first 4–5 years) are offset in expectation by a materially elevated probability of historically severe output collapses at 6–9 year horizons; the Barro–Ursua disaster evidence further suggests a slight reduction in disaster risk in the short term followed by a large increase at medium horizons, which is exactly the intertemporal tradeoff that makes evaluating accommodative policy difficult in real time. The growth-risk tradeoff does not by itself deliver an optimal policy prescription — the tradeoff between near-term stimulus and medium-term tail risk depends on the discount rate, the size of the respective effects, and the welfare cost of financial crises — but it establishes that any evaluation of prolonged accommodative policy that considers only its near-term benefits is incomplete. The finding is consistent with the Growth-at-Risk literature (Adrian et al. 2019, 2022) and with the BIS’s documented concerns about financial cycle risks during the 2010s low-rate environment.

Q7. Why is the endogeneity of monetary policy to financial conditions particularly important for this paper’s identification?

A central objection to any empirical relationship between low rates and subsequent financial crises is that central banks loosen policy in response to financial stress and economic weakness — states in which crisis risk is already elevated or depressed by pre-existing vulnerabilities; the OLS coefficient would then reflect the reverse-causal channel (crisis risk → loose policy) as much as the forward-causal channel (loose policy → crisis risk), making it impossible to infer causation. The trilemma IV directly addresses this by exploiting variation in monetary conditions that is literally determined by a different country’s central bank for that country’s domestic reasons — making it extremely implausible that the pegged country’s crisis risk influenced the base country’s rate decision in ways that satisfy the exclusion restriction. The result that IV exceeds OLS by 2.5–5× implies the endogeneity was strongly attenuating (loose policy coincides with low-risk states, biasing OLS downward), and the true causal effect of sustained accommodation on crisis risk is considerably larger than the raw correlations would suggest.

Q8. How does the paper relate to and distinguish itself from the theoretical risk-taking channel literature?

The paper is entirely empirical and does not propose a structural model; it complements the theoretical risk-taking channel literature (Borio–Zhu 2012; Dell’Ariccia–Laeven–Marquez 2014; Bekaert–Hoerova–Lo Duca 2013) by providing the first long-run causal evidence that the reduced-form prediction of that literature — loose policy raises systemic financial fragility — holds in the historical data. Existing empirical work had focused on high-frequency or cross-sectional responses of individual bank risk metrics to monetary policy surprises; the paper’s long-run LP approach is better suited to capturing the slow financial cycle dynamics that theory predicts and cannot be identified in event-study windows. The IV strategy resolves the identification problem that had stymied prior cross-country empirical work, where reverse causality confounded the relationship.

Key concepts

monetary policy stance : in this paper, the 5-year backward moving average of the policy rate gap (ri,t − r*i,t), where r* is the time-varying natural rate from the DGGT factor model; the sustained character of the measure captures the cumulative accommodation relevant for financial cycle dynamics, as opposed to short-lived rate cuts that do not materially affect bank portfolio decisions or credit standards.

trilemma IV : the paper’s instrumental variable for monetary stance, constructed for exchange-rate pegging countries as the capital-mobility-weighted residual of base-country interest rate changes (orthogonal to the base country’s own macro conditions); exploits the international monetary trilemma — a country pegging its exchange rate surrenders monetary autonomy and must match the base country’s rate regardless of its own economic conditions — to generate exogenous variation in the domestic stance.

local projections (LP) : the empirical methodology (Jordà 2005) estimating a separate OLS regression for each horizon h = 0,…,12, with the future crisis indicator (or R-zone, or low growth indicator) at horizon h as the outcome and the current stance measure as the key regressor; provides flexible impulse response functions without imposing the dynamic restrictions of a VAR, and allows the timing of crisis risk buildup to emerge directly from the data.

R-zones : periods of credit market overheating as defined by Greenwood, Hanson, Shleifer, and Sørensen (2022) in which household or business credit grows anomalously fast; used in this paper as an intermediate-state indicator that links loose monetary policy (identified 1–4 years earlier) to subsequent financial crisis (materializing 5–9 years later), supporting the credit-channel interpretation of the reduced-form IV results.

growth-risk tradeoff : the paper’s characterization of the intertemporal welfare consequences of sustained monetary accommodation; loose policy delivers short-term output gains (visible as slightly lower disaster probability at short horizons) but raises the probability of historically low real GDP growth at 8–9 year horizons by 2–3pp and elevates medium-term financial crisis risk by up to 15.5pp per 1pp looser average stance, implying that assessments of accommodative policy based only on near-term stimulus benefits substantially understate the medium-term costs.

Manager Pay Inequality and Market Power

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether managers are paid for market power. Bao, De Loecker, and Eeckhout build a general equilibrium model in which firms compete oligopolistically in goods markets (following Atkeson and Burstein 2008) while managers are allocated to firms through a competitive matching market (following Gabaix and Landier 2008 and Tervio 2008). The model identifies two distinct channels through which market power and firm size jointly determine executive compensation: a market power channel, whereby a more productive firm charges a higher markup given its output level, and a firm size channel, whereby higher total factor productivity expands output given markups. Because manager ability and firm type are complementary inputs into TFP, assortative matching arises: high-ability managers sort into high-type firms, amplifying both productivity dispersion and markup dispersion across firms.

The authors estimate the model year-by-year using Simulated Method of Moments on Compustat data covering 1994 to 2019, targeting ten moments including the average salary share, markup distribution, employment, and manager compensation levels. Firm-level markups are estimated using the production approach of De Loecker, Eeckhout, and Unger (2020). The ExecuComp variable TDC1 — encompassing salary, bonus, restricted stock grants, and option grant values — measures manager pay. Finance, insurance, and real estate sectors (SIC 6000–6799) are excluded.

Main findings: market power accounts for on average 45.8% of total manager pay over the sample period, rising from 38.0% in 1994 to 48.8% in 2019. Over the full period, average CEO compensation (net of reservation utility) roughly doubled, from approximately $2.94 million to $6.43 million. Of the $3.49 million cumulative increase, $2.02 million (57.8%) is attributed to rising market power, with the remainder ($1.47 million) due to the firm size channel. The market power channel’s dominance is concentrated among top managers: for the highest-ranked managers in 2019, 80.3% of pay is attributable to market power, and nearly all of their pay growth since 1994 stems from the market power channel. For lower-ranked managers, pay is determined primarily by the firm size channel and has been roughly flat over the period.

Within the market power channel, changes in technology — specifically increasing dispersion in firm-level TFP — are the dominant factor, contributing $1.33 million (65.9% of total market power channel growth). The increasing importance of manager ability (rising parameter alpha) contributes an additional $1.14 million through the market power channel. Within the firm size channel, TFP change accounts for 70.1% ($1.03 million) of growth, but the large effects from rising alpha and rising complementarity (gamma) are substantially offset by increasing dispersion in firm type. Structural estimates confirm that the average number of firms per market declines from 4.40 to 3.15, and firm-type dispersion (sigma_z) rises from 0.51 to 0.77, both consistent with rising market power over the period.

A counterfactual economy with no market power — firms priced at marginal cost — would yield a social welfare gain of 58.4% on average. The welfare cost of market power in 1994 could be offset by a 33.8% TFP increase; by 2019 the required TFP offset had risen to 51.7%. Without any market power, even the most talented managers would earn only their reservation utility, because firms earn zero profits regardless of productivity, eliminating the complementarity-driven matching surplus that makes top managers valuable. This confirms that superstar manager pay is intrinsically tied to the existence of market power in goods markets, not solely to firm size.

Scope conditions: the model applies to publicly listed US firms covered by Compustat and ExecuComp. The mechanism relies on Cournot competition within oligopolistic markets, assortative matching between managers and firms, and complementarity between manager ability and firm type (elasticity of substitution gamma estimated to be negative throughout the sample). The findings on market power share apply to CEOs specifically; the authors argue the same logic extends to all managerial positions with span-of-control over other workers, which encompasses roughly one-fifth of the workforce.

Q: What are the two channels through which manager pay is determined in the model, and how do they differ mechanically? A: The market power channel captures how a given level of TFP translates into higher markups — more productive firms charge more above marginal cost — thereby increasing profits per unit of output. The firm size channel captures how higher TFP expands the quantity of output a firm produces, increasing total profits through scale rather than through price-cost margin. Both channels raise profits and thus the marginal product of managers, but they operate through distinct economic mechanisms: one through pricing power and the other through productive scale.

Q: What is the empirical magnitude of the market power channel’s contribution to manager pay levels and growth? A: Market power accounts for an average of 45.8% of total manager pay over 1994–2019, rising monotonically from 38.0% in 1994 to 48.8% in 2019. For the total pay increase of $3.49 million over the period, $2.02 million (57.8%) is due to the increase in market power, with the remaining $1.47 million attributable to the firm size channel.

Q: How does the market power channel’s importance vary across the manager ability distribution? A: For the highest-ranked managers, 80.3% of total pay in 2019 is attributable to market power, and nearly all of their pay growth since 1994 runs through the market power channel. For the lowest-ranked managers, pay is almost entirely explained by the firm size channel and has been approximately flat over the period. This heterogeneity arises because top managers sort into high-markup firms through assortative matching, making their compensation disproportionately dependent on those firms’ market power.

Q: How does the model generate assortative matching between manager ability and firm type? A: Manager ability and firm type are complementary inputs into TFP (the CES aggregator with elasticity of substitution gamma less than one), which makes the matching output supermodular. In a frictionless matching market with transferable utility, supermodularity guarantees that high-ability managers match with high-type firms in equilibrium (Proposition 1). This positive assortative matching then amplifies productivity and markup dispersion, since the most productive firms become even more productive and gain larger market shares.

Q: What structural changes drive the rising importance of market power in manager pay over time? A: The dominant factor within the market power channel is changes in technology, specifically increasing firm-type dispersion (sigma_z rising from 0.51 to 0.77), which contributes $1.33 million or 65.9% of market power channel growth. The rising importance of manager ability (alpha, the weight on manager ability relative to firm type in the TFP aggregator) contributes another $1.14 million. The number of firms per market declines from an average of 4.40 to 3.15, further reducing competitive pressure and amplifying the markup premium for high-productivity firms.

Q: What does the counterfactual with no market power (first-best pricing) imply for manager pay and social welfare? A: Without market power, firms price at marginal cost and earn zero profits regardless of productivity, which eliminates the surplus from manager-firm matching. All managers would earn only their reservation utility, which is negligible relative to actual compensation. Social welfare would increase by 58.4% on average. The efficiency cost of market power — measured as the TFP increase needed to offset welfare losses — rose from 33.8% in 1994 to 51.7% in 2019, indicating a worsening welfare distortion over the period.

Q: How are markups measured, and what is their trend in the data? A: Markups are not directly observable and are estimated using the production approach of De Loecker, Eeckhout, and Unger (2020), which recovers firm-level price-cost margins from production data without requiring price data. Average markups in the Compustat sample rose from 1.53 in 1994 to 1.78 in 2019. The reduced-form elasticity of manager pay with respect to markups (controlling for firm characteristics, year, and firm fixed effects) increased substantially: in 2019 a one-percent increase in firm-level markup raises manager pay by 0.41 percent, which is 70.1% larger than the effect estimated in 1994.

Q: How does the paper handle the identification challenges inherent in regressing manager pay on markups? A: The reduced-form regression (with firm fixed effects, year effects, and interactions of year dummies with markups) documents a robust positive correlation but cannot establish causality due to reverse causality and omitted-variable bias. The paper addresses this by embedding the markup-manager pay relationship in a structural model where both are jointly determined by primitives — technology, market structure, and manager ability — and estimating those primitives via Simulated Method of Moments. The quantitative decomposition into market power and firm size channels derives from the model structure rather than from identifying variation in an instrumental variables sense.

Q: What do the matching model estimates reveal about manager-firm complementarity over time? A: The estimated elasticity of substitution between manager ability and firm type (gamma) is negative throughout the sample, confirming complementarity. Gamma was relatively stable before declining sharply from -2.22 in 2014 to -3.55 in 2019, indicating that manager ability and firm type became substantially more complementary in the latter part of the sample. The importance-of-manager parameter alpha is small (consistent with Gabaix and Landier 2008) but generally increasing, suggesting managers play an expanding role in determining firm-level TFP over time.

Q: What are the broader macroeconomic and distributional implications of the findings? A: Because approximately one-fifth of workers supervise other workers, the market-power-driven premium in managerial pay has implications beyond CEO compensation for the shape of the earnings distribution. The rise in top-1-percent income is identified as an efficiency concern, not just an equity concern: the best managers are hired by high-markup firms where they generate profits for shareholders but disproportionately little additional social value. Assortative matching between top managers and top firms widens the productivity gap between competitors, increasing market power and deadweight loss — the social return to managerial talent is therefore below the private return in equilibrium.

Market Power Channel: The component of manager pay attributable to how a firm’s TFP raises its markup — the ratio of output price to marginal cost — given the level of output. Distinct from the firm size channel; operates through pricing power rather than scale.

Firm Size Channel: The component of manager pay attributable to how a firm’s TFP expands output quantity given markups. Increasing output scale raises total profits and thus the marginal product of the manager even absent any change in price-cost margins.

Assortative Matching: The equilibrium allocation of high-ability managers to high-type firms, arising because manager ability and firm type are complementary inputs into TFP (supermodular matching output). Matching is determined in a frictionless market with transferable utility.

Markup: The ratio of output price to marginal cost, equal to the inverse of the price elasticity of demand under the nested CES preference structure. Endogenously determined by the firm’s sales share within its oligopolistic market and the elasticities of substitution within markets (eta) and across markets (theta).

Manager-Firm Complementarity: The property that manager ability and firm type are imperfect substitutes with elasticity of substitution gamma less than one in the TFP aggregator. Complementarity is the necessary condition for positive assortative matching and for the supermodularity of matching surplus.

Span of Control (Lucas 1978): The mechanism by which a manager raises the productivity of all workers under supervision, so that a more able manager generates a proportionally larger productivity gain the larger the firm. Provides the microfoundation for why firm size amplifies the value of manager ability.

Market Structure: The number of firms in each oligopolistic sub-market (Ij), which varies across markets and over time. Together with the distribution of firm-level TFP within a market, market structure determines how much competitive pressure limits markup extraction. Average firms per market declines from 4.40 to 3.15 over 1994–2019.

Market Segmentation through Information

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks what market outcomes an information designer — modeled as an internet platform that knows consumers’ preferences — can achieve by choosing what information to disclose to competing oligopolistic firms who then make personalized price offers. The model features n firms each producing a single differentiated product at zero cost, a continuum of consumers with unit demand and multidimensional valuations (one per product), and a designer who commits to a mapping from consumer types to joint distributions over messages sent to firms before they play a simultaneous pricing game. The designer’s objective spans the full range from maximizing producer surplus to maximizing consumer surplus.

The paper establishes two main results. First, under a necessary and sufficient condition called Aggregate Incentive Compatibility (AIC), the designer can implement full surplus extraction by firms — the producer-optimal outcome — in which every consumer buys her most preferred product at a price exactly equal to her valuation for it, capturing 100% of available surplus for producers. The AIC condition requires, for each firm i and each candidate deviation price p_hat_i, that the infra-marginal losses firm i would bear on its natural customers (those in Ei who value i most) from lowering price to p_hat_i must be weakly greater than the maximum business-stealing profit available from consumers who prefer other products but have valuation for i above p_hat_i. The condition is easier to satisfy when consumer preferences are more polarized, i.e., when consumers have stronger relative preferences for their most-preferred product. When firms offer homogeneous products the condition fails everywhere and no information structure can generate any producer surplus — Bertrand competition drives all profits to zero under any signal structure.

Second, the paper characterizes the consumer-optimal information structure, which achieves the maximum possible consumer surplus across all equilibria induced by any information structure. The upper bound on consumer surplus is CS* = (total surplus) minus sum_i Pi*_i, where Pi*_i is the profit firm i can guarantee itself by ignoring the designer’s signal and setting the best uniform price assuming all rivals price at zero. This bound is tight: the designer can implement it by publicly partitioning consumers into groups by most-preferred product, inducing rival firms to price at marginal cost (zero) for consumers who prefer another firm’s product, and then applying the Bergemann-Brooks-Morris (2015) extremal segmentation within each firm’s natural customer set to preserve each firm’s guarantee profit while achieving efficiency.

The illustrative two-firm example shows the quantitative stakes concretely. With no information disclosure, firms charge 4/5 and total producer surplus is about 76% of total surplus S*, consumer surplus is just under 10% of S*, and some consumers are excluded. With full disclosure, producer surplus rises to about 81% of S* and consumer surplus to 19%. The producer-optimal information structure (Case 3) achieves 100% of S* as producer surplus by pooling consumers who prefer different products into the same message submarket, giving each firm an incentive to price for its highest-valuing customers and ignore the others. The consumer-optimal information structure (Case 4) brings producer surplus down to about 57% of S* — its guaranteed lower bound — and delivers roughly 43% of S* to consumers, an outcome unattainable by full disclosure alone.

Both producer-optimal and consumer-optimal outcomes are efficient: all consumers buy their most-preferred product in both cases. The paper further characterizes the full efficient frontier between consumer- and producer-optimal outcomes, showing that mixing the consumer-optimal and full-information structures (or consumer-optimal, full-information, and producer-optimal structures when the latter is implementable) spans every point on the frontier.

The model assumes firms will price-discriminate if they can, that the designer has full knowledge of consumer types, and that the game is played once. The core results extend to continuous type distributions as shown in Online Appendix B.2. The analysis is restricted to a monopoly platform; competition among platforms is left for future work.

Q: What is the central research question and why does the two-benchmark comparison used by antitrust authorities miss important possibilities?

A: The paper asks what market outcomes — combinations of consumer and producer surplus — an information designer (a platform) can achieve by choosing among all possible information structures, not just the two benchmarks of no-information and full-information. Antitrust analysis that compares only those two cases misses a vast middle ground: an intermediary can package information in ways that, for instance, implement perfect collusion (extracting all surplus as producer surplus) while appearing to use privacy-protective technologies, or can intensify competition well beyond the full-information benchmark to benefit consumers.

Q: What is the producer-optimal information structure and when does it exist?

A: A producer-optimal information structure is one that induces an equilibrium in which every consumer buys her most-preferred product at a price exactly equal to her valuation — full surplus extraction. It exists if and only if, for every firm i and every candidate deviation price p_hat_i, the Aggregate Incentive Compatibility (AIC) condition holds: the aggregate infra-marginal losses firm i would suffer on its natural customers Ei from lowering price to p_hat_i must be at least as large as the maximum business-stealing profit from consumers outside Ei who have valuation for i weakly above p_hat_i. This is a condition on the distribution of consumer valuations, not on the information structure per se.

Q: What is the economic mechanism behind the producer-optimal structure — how does pooling consumers implement full surplus extraction?

A: The designer assigns consumers who prefer product A to the same message submarket as consumers who prefer another product but have a lower valuation for A. Firm A is then price-recommended its highest-valuing customers’ willingness to pay. The presence of the “outside” consumers in the same message makes it unprofitable for firm A to deviate downward to capture them, because the infra-marginal loss on the natural customers exceeds the additional revenue. Simultaneously, the rival firm cannot identify and undercut for A’s natural customers because the messages do not allow it to distinguish them. The result is that each firm plays a niche strategy, setting price equal to the valuation of its highest-type natural customers and excluding the others from its offer.

Q: When does polarization of consumer preferences help achieve the producer-optimal outcome?

A: Proposition 1 states that if a producer-optimal information structure exists under distribution f, it also exists under any distribution f_tilde that is more polarized than f — where more polarized means the mass of consumers who prefer i and have valuation above any threshold for i increases, and the mass of consumers who prefer j but have valuation above that threshold for i decreases. Intuitively, polarization slackens the Firm IC constraints because it reduces the business-stealing temptation: fewer consumers with high cross-product valuations are available for firm i to capture by undercutting. Concrete continuous-distribution examples include: uniform over the unit square (producer-optimal always exists), Hotelling anti-correlated values (exists everywhere), and truncated normal with mean 1/2 — producer-optimal is feasible for all standard deviations sigma > 0.15.

Q: Why does the producer-optimal outcome fail entirely when products are homogeneous?

A: Proposition 2 states that when all consumer types have equal valuations across products (the support of f lies on the diagonal of V^n), then for any information structure and any induced equilibrium, every consumer buys at price zero and all firms earn zero profit. The logic extends the standard Bertrand undercutting argument: with homogeneous products, any positive price a firm charges is undercut by a rival who can always profitably steal demand, and this applies to any posterior distribution induced by any signal realization. Even private signals cannot prevent this outcome because no signal realization can give a firm a non-contestable position.

Q: How is the consumer-optimal information structure constructed, and what is its key economic logic?

A: Theorem 2 shows the consumer-optimal structure has three layers. First, consumers are partitioned into n groups by most-preferred product (Ei). Second, firms j not equal to i are induced — by publicly revealing which group a consumer belongs to — to set price zero for consumers outside their group, because competing for those consumers is hopeless when their preferred firm is identified. Third, within each Ei, consumers are further partitioned into submarkets using the Bergemann-Brooks-Morris (2015) extremal segmentation applied to residual valuations (theta_i minus the maximum of competing valuations), ensuring firm i earns exactly its guarantee profit Pi*_i. By holding each firm down to its guarantee profit, the residual goes to consumers, maximizing CS.

Q: What is the guarantee profit Pi*_i and how does it bound consumer surplus?

A: Pi*i is the maximum profit firm i can achieve by ignoring all designer signals and setting a single uniform price to all consumers, against the worst-case scenario in which all other firms price at zero. Formally, Pi*i = max{pi} sum{theta in Ei: theta_i - pi >= max_{j not equal i} theta_j} pi * f(theta). Since firm i can always achieve Pi*_i regardless of the information structure (by simply ignoring signals), no information structure can push firm i’s profit below Pi*_i. The sum of these guarantee profits across all firms provides a lower bound on total producer surplus — and therefore an upper bound on consumer surplus — achievable by any information structure.

Q: In the two-firm numerical example, what is the quantitative comparison across the four cases?

A: Total available surplus S* = 0.84. Under no information (Case 1): producer surplus approximately 76% of S*, consumer surplus just under 10% of S*, and consumers of types (3/5, 2/5) and (2/5, 3/5) do not trade. Under full disclosure (Case 2): producer surplus approximately 81% of S*, consumer surplus 19% of S*, efficient. Under the producer-optimal structure (Case 3): producer surplus = 100% of S* (all surplus extracted), consumer surplus = 0%, efficient. Under the consumer-optimal structure (Case 4): producer surplus approximately 57% of S*, consumer surplus approximately 43% of S*, efficient. All cases except Case 1 are efficient; the no-information case excludes some consumers from trading.

Q: Is the full-information disclosure structure consumer-optimal?

A: Not in general. Proposition 3 states that full information is consumer-optimal if and only if all consumers in Ei have identical residual valuations (theta_i minus their second-best alternative) — a condition that generically fails. When residual valuations within Ei are heterogeneous, the designer can do strictly better for consumers by applying the extremal segmentation within each Ei rather than revealing full information, which would allow firms to price-discriminate on individual residual valuations and extract more surplus.

Q: Can the designer trace out the entire efficient frontier between consumer- and producer-optimal outcomes?

A: Yes, under two conditions. First, by mixing the consumer-optimal structure (point A) with the full-information structure (point B) using fractions lambda and 1-lambda respectively, the designer can implement any point on the efficient frontier between A and B. Second, when the producer-optimal outcome (point C) is also implementable, mixing the full-information structure with the producer-optimal structure by applying them to fractions lambda and 1-lambda of the consumer population respectively spans every point between B and C. The key insight is that the AIC condition, if it holds for f, also holds for any rescaled sub-distribution of f (it is scale-invariant), so the producer-optimal sub-problem remains feasible.

Q: What are the regulatory implications of the analysis?

A: The paper identifies a fundamental tension: banning information use sacrifices efficiency (some consumers excluded, wrong products purchased), but unrestricted use permits platforms to implement perfect collusion through information design. Critically, the paper shows that privacy-enhancing technologies that pool consumers into cohorts — like Google’s Privacy Sandbox — are equally consistent with the producer-optimal (collusive) and consumer-optimal (competitive) structures; the two differ only in the principle by which consumers are grouped. The paper suggests regulators could mandate that consumers in the same cohort share the same most-preferred product and that information be disclosed symmetrically across firms — the defining features of the consumer-optimal structure. This would block the producer-optimal grouping (which mixes consumers with different most-preferred products) while preserving efficiency.

Q: How does this paper relate to and extend Bergemann, Brooks, and Morris (2015)?

A: Bergemann, Brooks, and Morris (2015) characterize achievable consumer and producer surplus outcomes when a designer discloses information to a single monopolist who can price-discriminate. The present paper extends this to oligopoly, where competition between firms creates both additional constraints (firms may undercut each other) and additional instruments (the designer can play firms against each other). The consumer-optimal construction directly applies the BBM (2015) extremal segmentation within each firm’s natural customer set Ei, but the outer layer — using public revelation of group membership to induce rival firms to price at zero — is new and arises specifically from the oligopoly setting.

Information designer: An entity (modeled as a platform) that observes the full joint distribution of consumer valuations over all products and commits, before firms price, to a mapping from consumer types to joint distributions over messages sent to competing firms; the designer can be interpreted as an internet intermediary choosing how to package and share consumer data.

Aggregate Incentive Compatibility (AIC): The necessary and sufficient condition on the distribution of consumer valuations for the existence of a producer-optimal information structure; for each firm i and each candidate deviation price p_hat_i, the aggregate infra-marginal losses firm i would incur on its natural customers by lowering price to p_hat_i must weakly exceed the maximum revenue firm i could gain by attracting consumers who prefer rival products but have valuation for i above p_hat_i.

Producer-optimal information structure: An information structure that induces an equilibrium in which every consumer buys her most-preferred product at a price exactly equal to her full valuation for it, extracting 100% of available surplus as producer surplus — the outcome equivalent to the firms’ fully collusive joint surplus maximum.

Consumer-optimal information structure: An information structure that achieves the maximum consumer surplus attainable across all equilibria induced by any information structure, holding each firm to its guarantee profit Pi*_i (the best uniform-price profit the firm can secure by ignoring all signals) and allocating all residual surplus to consumers while maintaining allocative efficiency.

Guarantee profit (Pi*i): The maximum profit firm i can secure unilaterally by ignoring the designer’s signal and setting an optimal uniform price, computed against the worst case in which all rival firms price at zero; it equals max{pi} times the sum of f(theta) over all types in Ei for which theta_i minus pi exceeds all rival valuations.

Polarization of preferences: A stochastic dominance condition under which, relative to a baseline distribution, the mass of consumers who prefer product i and have high valuations for it increases while the mass of consumers who prefer rival products but have high valuations for i decreases; higher polarization weakens the Firm IC constraints and makes the producer-optimal outcome easier to implement (Proposition 1).

Separation and Consistency: Two structural properties any producer-optimal information structure must satisfy: Separation requires that the messages firm i sends to different consumers in Ei who have distinct valuations for i are disjoint in support; Consistency requires that every message firm i can send to any consumer type is contained in the union of messages firm i sends to consumers in Ei, preventing firm i from ever inferring that a consumer prefers a rival’s product.

Markov-Perfect Equilibria in Differential Games—With an Application to Climate Policy

Mon, 01 Jan 0001 00:00:00 +0000

This paper by Jaakkola and Wagener addresses a long-standing open problem in the theory of differential games: how to make Markov-perfect equilibria (MPE) well-defined when best-response policy functions are generically discontinuous in the state variable. The paper’s primary contribution is methodological — it introduces discontinuous Markovian strategies into differential games and proves that, under this extension, (i) payoffs can always be computed and (ii) unique best responses exist for almost all strategy profiles of opponents. The authors then apply this framework to derive the entire set of symmetric MPE in a canonical non-cooperative climate mitigation model (van der Ploeg and de Zeeuw, 1992), finding welfare results that are quantitatively large and policy-relevant.

The technical difficulty the paper resolves is that discontinuous policy functions can cause the ordinary differential equation governing state dynamics to lack classical solutions, making payoffs undefined. Prior literature responded either by restricting strategies to continuous functions — which rules out many natural best responses and imposes an unjustified constraint on the strategy space — or by allowing discontinuities only in “admissible” profiles, which makes each player’s strategy set depend on opponents’ choices and thus violates the basic structure of non-cooperative game theory. The authors’ solution is to adopt Filippov solutions (differential inclusions that convexify dynamics at discontinuities), so that a well-defined state trajectory and payoff exist for every strategy profile, not just admissible ones.

The paper’s three main theorems cover existence (Theorem 1), characterization (Theorem 2), and symmetric equilibrium conditions (Theorem 3). Theorem 1 establishes that, given any fixed set of potential jump points, the best-response correspondence maps almost all opponent strategy profiles to a unique Markovian best response — “almost all” in the sense of prevalence on infinite-dimensional function spaces. Theorem 2 provides necessary and sufficient conditions for a strategy to be a best response: it must satisfy the maximum principle where the value function is differentiable, value discontinuities may only occur at jump points of opponents’ strategies where the player cannot unilaterally push the state back to the low-stock side, and the value at any such interface must exceed the static optimum. Theorem 3 translates these into conditions for symmetric Nash equilibrium.

Applied to the van der Ploeg–de Zeeuw climate model — N symmetric countries choosing emissions a_i, with carbon stock x evolving as x-dot = sum(a_i) - deltax, and flow utility u(x, a_i) = a_i - (1/2)a_i^2 - dx — the paper characterizes the complete set of symmetric MPE. The unique continuous globally defined equilibrium (the linear MPE, previously established by Rowat 2007) is shown to be weakly Pareto-dominated by every other MPE with a continuous value function. The best equilibria feature discontinuous strategies that act like stock-conditioned trigger strategies: when the carbon stock falls below a target steady state x, players respond with a discrete upward jump in emissions to rapidly return the economy to x*; when carbon rises above x*, players increase emissions only gradually, creating a threat of drifting to a higher-pollution steady state that disciplines deviations. In a calibrated example with N=10, delta=0.02, rho=0.02, and damage parameter d=0.5, the linear equilibrium steady state is approximately 2.5 times the first-best level, while the best continuous-value MPE steady state is approximately 1.2 times the first-best level. Choosing the best equilibrium rather than the linear equilibrium closes between 50 and 100 percent of the welfare gap to the first-best outcome, depending on initial conditions. The paper also identifies particularly bad equilibria involving value-function discontinuities — coordination failures in which no single country can unilaterally stop the carbon stock from rising past a threshold — that can yield welfare outcomes worse than the linear equilibrium at high carbon levels.

The scope of the methodological results covers differential games with a single state variable and strategies that are real-analytic except at finitely many points. Extension to multiple state variables is left for future work. The climate application is restricted to the symmetric linear-quadratic van der Ploeg–de Zeeuw framework, chosen to facilitate comparison with prior literature.

Q: What is the fundamental technical problem with MPE in differential games that this paper resolves?

A: In differential games with Markovian strategies, best-response policy functions are generically discontinuous in the state variable. Discontinuous right-hand sides in the state dynamics ODE can prevent existence or uniqueness of classical solutions, making payoffs undefined for some strategy profiles. Prior literature either restricted attention to continuous strategies (causing non-existence of best responses to many profiles) or defined “admissible” strategy sets that depend on opponents’ choices (violating non-cooperative game theory structure). This paper resolves both problems for the single-state-variable case.

Q: How does the paper make payoffs well-defined under discontinuous strategies?

A: The paper adopts Filippov solutions — differential inclusions that replace the dynamics at a discontinuity point with a convex hull of the left and right limits. At a “push-push” discontinuity (where dynamics push the state toward the jump point from both sides), the Filippov solution remains at the jump point and flow payoffs are a weighted average of left and right actions. This ensures a well-defined trajectory and payoff for every strategy profile, not just “admissible” ones, restoring the standard non-cooperative game-theoretic structure.

Q: What does Theorem 1 establish, and what does “almost all” mean in this context?

A: Theorem 1 establishes that, for any fixed collection of jump points, each player has a unique Markovian best response to almost every profile of opponents’ strategies. “Almost all” is in the sense of prevalence on infinite-dimensional function spaces (following Hunt, Sauer, and Yorke 1992): the set of profiles for which a unique best response fails to exist is shy (measure-zero analog in infinite dimensions) and nowhere dense. This resolves the long-standing open problem of making MPE well-founded in differential games.

Q: What are the necessary and sufficient conditions for a best response given by Theorem 2?

A: A strategy phi_i is the best response to opponents’ profile if and only if: (i) at all points where the value function is differentiable, the strategy satisfies the maximum principle; (ii) the value function is decreasing in the state (monotonicity); (iii) value discontinuities may occur only at opponents’ jump points where player i cannot unilaterally move the state back to the low-stock region; (iv) at any such interface, the value must be at least as large as the static optimum u(x, a_i)/rho; and (v) the value is differentiable at push-push steady states. These conditions extend the standard maximum principle with local requirements that restrict which discontinuities are possible.

Q: What is the van der Ploeg–de Zeeuw model and why is it used here?

A: The van der Ploeg–de Zeeuw (1992) model has N symmetric countries choosing emissions a_i, with carbon stock evolving as x-dot = sum(a_i) - delta*x, and flow utility u(x, a_i) = a_i - (1/2)a_i^2 - dx. It is linear-quadratic, so a linear MPE exists and is analytically tractable, and prior literature (Dockner and Long 1993; Rowat 2007; Dockner and Wagener 2014) has studied it extensively. The paper uses it as a benchmark to demonstrate that the new methods yield novel and economically important results for even well-understood models.

Q: What is the linear equilibrium and why does it produce poor welfare outcomes?

A: The linear equilibrium phi_L(x) = alpha + beta*x, with beta negative, is the unique continuous globally defined MPE (Rowat 2007). In it, emissions decrease with the carbon stock because each player anticipates that opponents will also reduce emissions when carbon is high. This strategic substitutability creates adverse dynamic free-riding: players try to exploit the fact that high carbon stock will cause opponents to cut back, so each has an incentive to emit more when carbon is low. In the calibrated example, the linear equilibrium steady state is approximately 2.5 times the first-best level.

Q: What do the best equilibria look like, and why do they achieve high welfare?

A: The best equilibria feature a target steady state x* near the first-best level and a discontinuous upward jump in emissions when carbon falls slightly below x*. This threat rapidly returns any carbon reduction back to x*, eliminating the strategic incentive to free-ride on others’ reductions. When carbon rises above x*, emissions increase only slightly, causing the economy to drift slowly toward a higher-pollution steady state — the threat of this bad outcome disciplines overshooting. This mechanism is analogous to a trigger strategy but is conditioned on the stock level rather than on past actions, making it compatible with Markovian strategies.

Q: How large are the welfare gains from the best equilibrium relative to the linear equilibrium?

A: In the calibrated example with N=10, delta=0.02, rho=0.02, and d=0.5, the best continuous-value MPE steady state is approximately 1.2 times the first-best level, compared to 2.5 times for the linear equilibrium. Choosing the best equilibrium closes between 50 and 100 percent of the welfare gap between the linear equilibrium and the first-best outcome, depending on initial conditions. The paper characterizes this as a quantitatively large, first-order welfare improvement.

Q: What are “coordination failure” equilibria and when do they arise?

A: Coordination failure equilibria feature discontinuities not only in the strategy (emission rate) but also in the value function itself. They arise when no single country can unilaterally prevent the carbon stock from rising past a threshold — formally, when N * a_max < delta * x at the discontinuity point. In such cases, if opponents are emitting heavily, no individual country can stop atmospheric carbon from rising even if it emits nothing, making heavy emission a best response. All players following this logic simultaneously produce a self-fulfilling collapse to high emissions. At high carbon levels these equilibria can yield welfare outcomes worse than the linear equilibrium.

Q: What is the paper’s main policy implication for climate negotiations?

A: The paper argues that international climate negotiations should be understood as a coordination problem over which of many MPE is played, rather than as bargaining over a limited cooperative surplus in a dynamic prisoners’ dilemma. Since the best equilibria are self-enforcing (they are Nash equilibria, not cooperative solutions), they do not require external enforcement. The paper suggests effective agreements may involve threshold-based commitments — sharp decarbonisation if a carbon target is met, but acceptance of a substantially higher stabilisation target (e.g., 2.5 degrees C rather than 2 degrees C) if the first target is missed — to create the discontinuous strategic incentives that support good equilibria.

Q: How does the paper handle the previously identified “local MPE” that could not be extended to the entire state space?

A: Prior work (Dockner and Long 1993; Rubio and Casino 2002; Dockner and Wagener 2014) constructed nonlinear equilibria that were only locally defined, and the validity of such equilibria was questioned (Rowat 2007; Bernhard 2024) because they were undefined on the full state space. The present paper’s framework allows discontinuous strategies, so these locally defined equilibria can be extended into globally defined, discontinuous MPE. Most previously discovered equilibria are shown to be nested within the larger set of all symmetric MPE identified here.

Q: What mathematical tools are used to prove the main results?

A: The proofs rely on the theory of viscosity solutions to Hamilton-Jacobi-Bellman equations (Bardi and Capuzzo-Dolcetta 2008), building on and extending results of Barles, Briani, and Chasseigne (2013, 2014) on optimal control with discontinuous dynamics. A key departure from Barles et al. is that the paper cannot assume controllability of the dynamics near discontinuities without imposing undue restrictions on opponents’ strategies. The application of these results to a fixed-point condition of the best-response correspondence to construct MPE conditions is described as entirely novel.

Q: What are the scope conditions and limitations of the methodological results?

A: The main results (Theorems 1–3) apply to differential games with a single state variable and strategies that are real-analytic except at finitely many points with one-sided derivatives everywhere. The climate application is further restricted to the symmetric linear-quadratic van der Ploeg–de Zeeuw framework. Extension to multiple state variables is acknowledged as future work. The welfare calibration results are specific to the parameter values N=10, delta=0.02, rho=0.02, d=0.5.

Markov-perfect equilibrium (MPE): A Nash equilibrium in Markovian strategies, where each player’s strategy conditions only on the current state variable and not on the history of play. The paper makes this concept well-founded in differential games by allowing discontinuous strategies, ensuring payoffs can be computed for all strategy profiles and unique best responses exist almost everywhere.

Filippov solution: A solution concept for ordinary differential equations with discontinuous right-hand sides, which replaces the dynamics at a discontinuity point with a convex hull of the left and right limits. Used in this paper to define well-specified state trajectories and payoffs even when players’ strategies have jumps, eliminating the need to restrict strategy sets to “admissible” profiles.

Discontinuous Markovian strategy: A policy function phi: X -> A that maps the state to an action and is real-analytic except at finitely many points, with well-defined one-sided derivatives everywhere. The key innovation of the paper — allowing such strategies makes differential games well-behaved as standard non-cooperative games while capturing the generically discontinuous nature of optimal policy functions.

Push-push steady state: A steady state at a discontinuity point of a strategy where the dynamics push the state toward that point from both sides. Under Filippov solutions the state remains at such a point, with flow payoffs being a weighted average of left and right actions. Theorem 2 requires the value function to be differentiable at these points in equilibrium.

Coordination failure equilibrium: An MPE featuring discontinuities in both the strategy and the value function, arising when no single player can unilaterally move the state across a threshold. At high carbon levels, if opponents emit heavily, individual emission cuts are ineffective; heavy emission becomes a best response for all, sustaining a self-fulfilling high-emission outcome. These equilibria can yield welfare outcomes worse than the linear equilibrium.

Linear equilibrium: The unique continuous globally defined symmetric MPE in the van der Ploeg–de Zeeuw model, characterized by emissions decreasing linearly in the carbon stock. It involves adverse strategic substitutability — each player reduces emissions in response to high carbon because opponents do likewise — and is weakly Pareto-dominated by every MPE with a continuous value function.

Skiba point: A state at which the optimal policy is discontinuous because the value function has distinct left and right derivatives, corresponding to the boundary between two basins of attraction with different long-run outcomes. In this paper, the steady state of a best equilibrium is a Skiba-type point: below it, emissions jump up to return rapidly to the target; above it, emissions increase only gradually.

Markups Across Space and Time

Mon, 01 Jan 0001 00:00:00 +0000

Anderson, Rebelo, and Wong study the behavior of markups in the retail sector across regions and over time, using a combination of firm-level Compustat data and product-level scanner data from two large retailers — one operating over 100 stores across U.S. states (quarterly data from 2006 Q1 to 2009 Q3, covering roughly 3.6 million SKU-store pairs across 79 product categories) and one operating hundreds of stores across Canadian provinces (quarterly data from 2016 Q1 to 2018 Q4, covering 15.6 million item-store pairs across 41 product groups). Markups are measured using gross margins — sales minus cost of goods sold as a fraction of sales — computed at the product level using the replacement cost for every item. This measurement approach is appropriate for retail because cost of goods sold accounts for over 80 percent of total retail firm costs, making it a reliable proxy for marginal cost. The replacement cost data, available at the store level, is the cost used by managers in actual pricing decisions, distinguishing these datasets from typical scanner data that contain only average costs.

The paper documents five main facts. First, markups are remarkably stable over time and display a mild procyclical pattern. At the aggregate level, gross margins are roughly acyclical or mildly procyclical while sales and cost of goods sold are highly procyclical. The elasticity of gross margins with respect to real GDP is statistically insignificant at both the aggregate and firm level. The conditional response of gross margins to high-frequency monetary policy shocks and oil price shocks is also statistically insignificant, while net operating profit margins fall significantly in response to both shocks. Operating profit margins are 3.4 times more volatile than gross margins at a quarterly frequency, and sales and costs are roughly 2.6 times more volatile.

Second, there is large regional dispersion in gross margins. A variance decomposition shows that the regional variance of gross margins (0.103) is substantially larger than the time-series variance (0.013), with a near-zero covariance between the two components. Third, regions with higher incomes and more expensive houses have higher markups — gross margins are positively correlated with log household income and log median house value in both the U.S. and Canadian data.

Fourth, these higher regional markups do not result from less intense competition or regional differences in marginal costs. Gross margins are uncorrelated with the Herfindahl index (a measure of competition) and with a rural dummy (a proxy for higher transportation costs). The cyclicality of markups is acyclical or mildly procyclical regardless of whether the underlying product costs are themselves acyclical, procyclical, or countercyclical.

Fifth, and most distinctively, regional variation in markups arises from differences in assortment composition across regions rather than from deviations from uniform pricing. A decomposition of regional gross margin variance confirms that the dominant component is the term capturing differences in product assortment across markets; the term capturing differences in gross margins for the same item — which would be nonzero under geographic price discrimination — accounts for very little of the regional variation. When the same item is available in different regions, the retailer charges a uniform price, consistent with Della Vigna and Gentzkow (2019).

To rationalize these five facts, the authors propose a model with non-homothetic, quadratic preferences (following Melitz and Ottaviano 2008). In the model, higher-productivity regions choose higher-quality goods, which have less elastic demand and therefore higher markups. The markup is procyclical with respect to productivity shocks (A) but acyclical with respect to labor supply shocks (N), so a mixture of both types of shocks produces mildly procyclical markups. The model generates uniform pricing across regions for the homogeneous good, with regional markup differences arising through quality and assortment selection rather than price discrimination.

Q: How do the authors measure markups, and why is this approach appropriate for retail? A: Markups are measured as gross margins — (sales minus cost of goods sold) divided by sales — computed at the product level using the replacement cost for every item. This is appropriate for retail because cost of goods sold is the predominant variable cost, accounting for over 80 percent of total retail firm costs. The replacement cost is the marginal cost concept used by managers in pricing decisions and is available at the store level rather than as a national average.

Q: What is the cyclical behavior of gross margins at the aggregate retail level? A: Gross margins are roughly acyclical or mildly procyclical. Sales and cost of goods sold are highly procyclical, suggesting that the business cycle primarily affects quantities sold rather than markups. Operating profit margins are 3.4 times more volatile than gross margins at a quarterly frequency, while sales and costs are roughly 2.6 times more volatile.

Q: What is the conditional response of gross margins to monetary policy and oil price shocks? A: The response of gross margins to both high-frequency monetary policy shocks (identified from Federal Funds futures data) and oil price shocks (identified via the Ramey-Vine 2010 VAR approach) is statistically insignificant. In contrast, net operating profit margins fall in a statistically significant manner in response to both types of shocks, indicating that fixed cost absorption rather than markup adjustment drives profit volatility.

Q: How large is the regional dispersion in gross margins relative to their time-series variation? A: The variance decomposition shows that the regional variance of gross margins is 0.103, compared to a time-series variance of only 0.013, with a covariance term close to zero. The vast majority of gross margin variation is therefore cross-sectional rather than time-series.

Q: What variables explain the regional variation in gross margins? A: In the U.S. data, gross margins are positively correlated with log household income and log median house value. Gross margins are uncorrelated with the Herfindahl index (a competition measure) and with the rural county dummy (a transportation cost proxy). Canadian data confirms the positive correlation between gross margins and both log household income and log median house value.

Q: What is the mechanism through which higher-income regions have higher markups? A: Regional markup differences are driven by assortment composition differences, not price discrimination. When the same item is sold in multiple regions, it sells at a uniform price. Higher-income regions carry different (higher-quality, higher-margin) products. The correlation between unique items sold and regional household income is 0.42 for the Canadian retailer and 0.17 for the U.S. retailer.

Q: How is the variance of regional gross margins decomposed into assortment versus pricing components? A: The variance decomposition separates total regional gross margin variance into: (1) a term for differences in gross margins for the same item across regions (would be nonzero with geographic price discrimination), (2) a term for differences in assortment composition holding gross margins fixed, and (3) an interaction term plus covariance terms. The dominant term is the assortment composition component; the same-item price difference term accounts for very little of the regional variation.

Q: Does the acyclicality of gross margins hold for products with procyclical costs? A: Yes. The authors divide products into those with acyclical, procyclical, and countercyclical costs and show (Table 7) that gross margins are acyclical or mildly procyclical for all three groups in both the U.S. and Canadian data. This implies that retailer pricing behavior contributes to price inertia even for products whose wholesale costs move with the cycle.

Q: What fraction of gross margin changes are active versus passive? A: In the U.S. data, 91 percent of margin changes are active (resulting from price changes, regardless of whether replacement cost has changed); 9 percent are passive (replacement cost changes with no price change). In the Canadian data, 93 percent of changes are active. Both the probability of active margin changes and the size of margin changes are acyclical with respect to unemployment and local house prices.

Q: How does the Hall approach compare to gross-margin-based markup estimates? A: When the Hall approach is implemented using output elasticities (deflating sales by a product-level price deflator to obtain quantity), the resulting markup estimates are very close to those from gross margins — the ratio is 1.014 for the U.S. firm and 0.991 for the Canadian firm. However, when revenue elasticities are used instead of output elasticities (the common practice in the literature due to data limitations), the implied markup is 14 percent lower for the U.S. firm and 13 percent lower for the Canadian firm, confirming the bias documented by Bond et al. (2020).

Q: What are the key features of the theoretical model and what facts does it explain? A: The model uses non-homothetic quadratic preferences (Melitz-Ottaviano form) in which demand elasticity falls as consumption quality rises. Higher-productivity regions optimally consume higher-quality varieties, which face less elastic demand and hence carry higher markups. The markup is procyclical in productivity (A) with an elasticity less than one (incomplete cost passthrough) and acyclical in labor supply (N), so a mixture of shocks generates mild procyclicality. Uniform pricing across regions for the homogeneous good holds by construction, and regional markup differences arise through quality-assortment selection.

Q: Which existing macroeconomic models are consistent with the time-series evidence, and which are not? A: The evidence is inconsistent with models featuring countercyclical markups (Rotemberg-Woodford 1992 imperfect competition, Ravn-Schmitt-Grohe-Uribe deep habits, Jaimovich-Floetotto entry-exit, and standard New Keynesian models with sticky prices and procyclical marginal costs). The time-series evidence is consistent with models featuring sticky retail prices and acyclical marginal costs (Nakamura-Steinsson 2010, Coibion-Gorodnichenko-Hong 2015) and models with price and wage rigidities at the manufacturing level (Erceg-Henderson-Levin 2000, Christiano-Eichenbaum-Evans 2005). Mildly procyclical search models (Alessandria 2009) are also consistent when procyclicality is mild.

Q: Which existing trade and regional models are consistent or inconsistent with the regional evidence? A: The spatial price discrimination models of Greenhut-Greenhut (1975) and Thisse-Vives (1988), which predict higher markups in less competitive regions, are inconsistent with the data. The Bertoletti-Etro (2017) non-homothetic model predicts that regional markup variation is driven by deviations from uniform pricing, which is also inconsistent. The Fajgelbaum-Grossman-Helpman (2011) model predicts countercyclical markups when costs are procyclical, contradicting the time-series results. Most existing macroeconomic models rely on homothetic preferences, predicting markups independent of regional income, inconsistent with the regional facts.

Q: What are the scope conditions on the measurement approach? A: Gross margins are valid proxies for markups only in the retail sector, where cost of goods sold is the dominant variable cost (over 80 percent of total costs). In manufacturing, where labor and other costs represent a larger fraction of total variable costs, gross margins would not be a reliable markup measure. The product-level scanner data cover the 2006-2009 period for the U.S. and 2016-2018 for Canada; the U.S. sample includes a recession while the Canadian sample covers a moderate expansion.

Gross margin as markup proxy: The ratio of (sales minus cost of goods sold) to sales, computed at the product level using the replacement cost for each item at each store and time period. Used as a proxy for the price-cost markup because cost of goods sold is the dominant variable cost in retail (over 80 percent of total costs), and the replacement cost is the marginal cost concept managers use in pricing decisions.

Replacement cost: The cost at which the retailer would replenish a unit of inventory at current prices, available at the store level in the scanner datasets. Distinct from average historical cost and used here as a direct proxy for marginal cost, eliminating one of the main sources of markup mismeasurement in prior empirical work.

Assortment composition: The set of products stocked and the expenditure weights of those products within a region. The paper’s central mechanism for regional markup variation — higher-income regions carry different (higher-quality, higher-margin) goods rather than charging different prices for the same goods.

Uniform pricing: The practice of charging identical prices for the same item across different geographic regions. Confirmed empirically in both the U.S. and Canadian scanner datasets, and embedded structurally in the theoretical model for the homogeneous good.

Active versus passive margin changes: A decomposition of gross margin changes into active changes (arising from retailer price decisions, irrespective of cost changes) and passive changes (arising when replacement cost changes but the retailer holds price fixed). Ninety-one percent of U.S. margin changes and 93 percent of Canadian changes are active.

Non-homothetic quadratic preferences: The utility specification (following Melitz and Ottaviano 2008) in which the absolute value of the own-price demand elasticity falls as quality consumption rises. This property implies that higher-quality goods carry higher markups and that richer regions, which demand higher quality, have higher average markups — the key mechanism linking income to markups in the model.

Hall approach to markup estimation: A production-function-based method in which the markup equals the output elasticity with respect to a variable input divided by that input’s cost share in revenue. The paper shows this yields estimates close to gross-margin estimates when implemented with true output quantities, but produces markups roughly 13-14 percent lower when revenue is substituted for output (a common approximation), confirming the Bond et al. 2020 bias.

Monetary Policy and Endogenous Financial Crises

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether a central bank should deviate from strict inflation targeting (SIT) to promote financial stability, studying the question in a textbook New Keynesian model augmented with capital accumulation and microfounded endogenous credit-market crises. The model embeds two financial frictions — limited contract enforcement and asymmetric information about firm productivity — that together generate fragile credit markets in which, when productive firms’ marginal return on capital falls below a threshold, the credit market collapses (a “financial crisis”). The calibrated model matches the empirical regularity that economies spend roughly 8% of time in financial crises. The central finding is threefold: (1) monetary policy affects crisis probability both in the short run (via output and markups) and in the medium run (via capital accumulation dynamics); (2) a Taylor-type rule that responds to output fluctuations — rather than SIT — reduces crisis incidence and raises welfare, with TR93 (φ_y = 0.125) generating a 0.016% permanent consumption equivalent gain over SIT; (3) prolonged unexpected monetary easing followed by abrupt tightening is itself a mechanism that can trigger financial crises. These findings imply a genuine price-versus-financial-stability tradeoff and challenge the “divine coincidence” view that SIT is sufficient in the presence of financial frictions.

Layer 1: Overview

Boissay, Collard, Galí, and Manea build a New Keynesian model with capital accumulation and endogenous credit-market crises to study whether central banks should deviate from inflation targeting to promote financial stability. The model departs from the textbook three-equation NK framework in four ways: capital accumulation that allows persistent booms, firm heterogeneity in productivity that generates a credit market, financial frictions (limited enforcement and asymmetric information) that make the credit market fragile, and global (nonlinear) solution methods that can capture the boom-bust dynamics. A financial crisis — credit-market collapse — occurs when productive firms’ marginal return on capital falls below the minimum loan rate that unproductive firms require to willingly lend. The model is calibrated so that the economy spends 8% of time in crisis (consistent with cross-country evidence from Reinhart and Rogoff, Laeven and Valencia, and Baron et al.) and the additional parameter governing financial frictions (the proportion μ = 2.42% of unproductive firms) is chosen to match this target. Three main findings emerge: monetary policy operates through short-run aggregate demand channels and a medium-run capital accumulation channel; a Taylor-type rule that responds to output improves welfare over SIT, with TR93 raising permanent consumption by 0.016% relative to SIT; and discretionary loosening followed by abrupt tightening can itself generate crises.

In depth

Q1. How do financial crises arise in the model, and what is the triggering condition?

A financial crisis in the model is a credit-market breakdown in which the credit market collapses to autarky: unproductive firms stop lending because the loan rate they can credibly demand falls below the return on holding idle capital. The friction generating this fragility is a combination of limited contract enforcement (firms that borrow to purchase capital can abscond with sale proceeds) and asymmetric information about idiosyncratic productivity. Together, these frictions imply that productive firms cannot borrow beyond an incentive-compatible leverage cap, and that the minimum loan rate required to induce unproductive firms to lend is a positive threshold $\bar{r}^k = \mu/(1-\mu) - \delta$. A crisis occurs if and only if productive firms’ marginal return on capital $r_t^k$ falls below this threshold — which happens at the end of a protracted boom when the economy has accumulated excess capital, driving down marginal productivity. The average simulated crisis is triggered by a roughly three-standard-deviation negative TFP shock (around 1.5% below steady state) hitting an economy where the capital stock has been elevated by a long sequence of positive shocks. The same shock would not trigger a crisis at lower capital stocks — the capital overhang is a necessary precondition.

Q2. Through what channels does monetary policy affect financial stability, and how do short-run and medium-run channels differ?

The paper identifies three channels: a Y-channel (output), an M-channel (markups), and a K-channel (capital accumulation), with the K-channel operating only in the medium run through expectations about the policy rule. In the short run, a rate hike that compresses output and raises markups reduces the marginal return on capital, pushing the economy closer to a crisis — a destabilizing short-run effect. In the medium run, however, a commitment to lean against output booms (high φ_y) slows capital accumulation during expansions through two mechanisms: (i) it reduces investors’ expected returns from expansion, dampening incentives to accumulate capital; and (ii) it provides households with implicit insurance against aggregate shocks, reducing precautionary savings. Because capital accumulation is slow, these medium-run effects only materialize over multiple years and require that the central bank pre-commit to the rule. Expectations of the rule thus shape the boom dynamics before any crisis.

Q3. What does the welfare comparison across Taylor rules reveal about the price-versus-financial-stability tradeoff?

Responding to output raises welfare in the presence of financial frictions, even though it reduces welfare in the frictionless benchmark, generating a genuine price-versus-financial-stability tradeoff. Under strict inflation targeting, the welfare loss relative to the first best is 0.11% in consumption equivalent variation, entirely attributable to financial crises (since SIT eliminates price distortions). Responding more aggressively to output (higher φ_y) reduces crisis incidence from 9.85% of time (under SIT) to as low as 0.45% (under φ_y = 0.75), but raises inflation volatility. The welfare gain is non-monotone in φ_y: under the baseline φ_π = 1.5, welfare is highest around φ_y ≈ 0.5–0.6, and declines for higher φ_y as markup volatility (M-channel) more than offsets the financial stability gain. TR93 (φ_y = 0.125) already delivers 0.016% higher permanent consumption than SIT.

Q4. What is the role of monetary policy discretion in generating financial crises?

The model shows that sustained discretionary loosening followed by abrupt tightening can itself trigger a crisis, formalizing the “rates too low for too long” narrative of the 2007-08 Global Financial Crisis. Using only monetary policy shocks (either AR(1) with ρ = 0.5, σ = 0.25% or i.i.d.) as the source of aggregate uncertainty, the average simulated crisis follows a long period of unexpectedly accommodative policy that feeds an investment boom, with the crisis triggered by three consecutive unexpected rate hikes (persistent shock case) or a single 60-basis-point jolt (i.i.d. case) at the end of the boom. This is consistent with empirical evidence (Schularick, Ter Steege, and Ward 2021) that unanticipated rate hikes at the end of a boom are more likely to trigger crises than prevent them.

Q5. How much additional welfare gain is available from a “backstop” commitment that forestalls crises entirely?

A nonlinear backstop rule — under which the central bank deviates from its normal rule just enough to prevent a crisis whenever one would otherwise occur — nearly eliminates the welfare cost of financial crises, requiring only modest policy deviations. Under SIT, the backstop improves welfare by 0.11% in consumption equivalent variation — the full cost of crises — leaving a residual welfare loss of only 0.0013% relative to the first best. The backstop requires rate cuts of on average 20 basis points below TR93, or tolerance of 0.6 percentage points of extra inflation above the SIT target, in the periods when a crisis would otherwise emerge. The tradeoff is that backstopping increases the frequency with which the central bank must intervene, since knowing that the bank will intervene can increase the financial sector’s risk-taking (fragility).

Q6. How does the paper’s approach to microfounding crises compare to reduced-form alternatives?

Unlike Woodford (2012) and Gourio, Kashyap, and Sim (2018), who use reduced-form functions linking credit or leverage gaps to crisis probability, this paper derives crisis probability and severity endogenously from first principles, with implications for the policy prescriptions. Because crises and their depth are both endogenous to policy, the model can determine not only how policy affects the probability of a crisis but also how it affects the size of the output loss conditional on a crisis. This distinction matters: the model shows that not all credit booms are equally dangerous — a boom accompanied by genuine productivity gains carries lower crisis risk than an equivalent capital accumulation driven by precautionary saving externalities. The endogenous crisis mechanism also implies that some forms of leaning that superficially appear to reduce crisis probability may actually increase it by raising markup volatility, an effect absent from reduced-form models.

Key Concepts

divine coincidence : the standard New Keynesian result that strict inflation targeting (SIT) simultaneously eliminates output gap fluctuations and is welfare-optimal in the absence of financial frictions; the paper shows this coincidence breaks down when the credit market is fragile, because SIT does not internalize the externalities driving capital overhang and crisis risk.

financial crisis (in the model) : the autarkic equilibrium of the credit market, in which productive firms’ marginal return on capital falls below the minimum loan rate required for unproductive firms to willingly lend; characterized by credit-market collapse, capital misallocation (unproductive firms retain idle capital), severe output loss, and inflationary pressure.

K-channel of monetary policy on financial stability : the medium-run mechanism by which a commitment to respond strongly to output fluctuations dampens capital accumulation during booms, reducing the likelihood of the excess capital overhang that triggers crises; operates through expectations and requires multi-year lead times, distinguishing it from the short-run output (Y) and markup (M) channels.

savings glut externality : the tendency of households to over-accumulate capital relative to the socially efficient level in anticipation of a crisis, because individual households do not internalize the aggregate effect of their precautionary saving on the economy’s distance from the credit-market collapse threshold; identified by Boissay, Collard, and Smets (2016) and present in this model as a driver of endogenous boom-bust dynamics.

backstop rule : a nonlinear monetary policy rule in which the central bank follows a standard Taylor or SIT rule in normal times but commits to deviating just enough from that rule to forestall a financial crisis whenever one would otherwise emerge; shown to nearly eliminate the welfare cost of crises at the cost of modest and infrequent policy deviations, with the side effect of increasing the frequency of needed interventions.

Money Markets, Collateral and Monetary Policy

Mon, 01 Jan 0001 00:00:00 +0000

The paper studies the euro area interbank money markets during the global financial crisis (2007–09) and sovereign debt crisis (2010–15), documenting four empirical regularities and building a quantitative general equilibrium model to evaluate their macroeconomic impact and the role of central bank policy. The central finding is that the ECB’s collateral policy — lending to banks at haircuts more favorable than private markets — prevented output and investment from falling roughly twice as much as they would have under a passive constant-balance-sheet policy.

Four empirical observations (Section 2, 2003–2015):

The share of unsecured interbank borrowing declined throughout the euro area; banks substituted toward secured (repo) transactions — the secured share rose from roughly 42% to 90% of turnover
Private market haircuts on Southern sovereign bonds (IT, ES, PT) rose dramatically during the sovereign debt crisis, peaking at 25.16% in 2012–2013 (vs 3% in 2010) — while the ECB kept its haircuts nearly unchanged, creating a “haircut gap”
Bank borrowing from the ECB increased eight-fold in Southern regions as the haircut gap widened
Household deposits at banks remained stable throughout

Model architecture (Section 3): Two regions (North: DE/FR; South: IT/ES/PT) share a common central bank. Each period is divided into a morning and afternoon. In the morning, banks choose portfolios subject to a Gertler-Karadi (2011) leverage constraint (fraction λ of assets can be diverted by the manager) and a central bank collateral constraint (CB loans require bonds pledged at CB haircut η). In the afternoon, banks face idiosyncratic liquidity shocks ω~iid F(ω) on deposits. Connected banks (fraction ξ) can borrow unsecured in the afternoon interbank market. Unconnected banks (fraction 1−ξ) must cover their maximum possible payment outflow ωmaxD by holding reserves or pledging bonds as collateral in the private secured market (at haircut 1−η̃^γ). Five inequality constraints — the morning leverage constraint, a CB collateral constraint, and three short-sale constraints (bonds, deposits, capital) — can each switch between binding and slack; the model requires a non-linear solution (Dynare Levenberg-Marquardt mixed complementarity solver).

Calibration (Table 2, quarterly frequency):

Standard: capital share θ = 0.33, depreciation δ = 0.02, discount factor β = 0.994, Frisch inverse ε = 0.40, government spending g = 0.566
Bond maturity 1/κ = 5.952 years; dividend fraction φ = 0.025; leverage constraint λ = 0.701
Pre-crisis interbank structure: ξ = 0.42 (42% connected), haircuts η̃ = η = 0.97 (3%)
Maximum liquidity shock ωmax = 0.10; foreign sector bond demand elasticity ρ = 1.757
6 targeted moments (Table 3, exact fit): Govt/GDP = 0.20; bank leverage = 6; annual bond spread = 0.2%; bank share of bond holdings = 23%; foreign sector share = 64%; annual inflation = 2%
Non-targeted moments broadly matched: central bank bond holdings/GDP, government debt/GDP

Two shock processes (Section 5.2):

ξ shock (permanent, onset t=1 corresponding to 2009 Q1): connected share log(ξt) transitions from ξ−1 = 0.42 to ξ∞ = 0.10 with AR(1) persistence ρξ = 0.95
η̃S shock (temporary-persistent, onset t=13 corresponding to 2012 Q1): Southern private haircut recovery factor follows AR(2) with ρη1 = 1.65, ρη2 = −0.70 and an initial impulse ε13 = −0.11; model haircuts peak at 25%, matching the data peak of 25.16%

Comparative statics (Section 6.1):

ξ shock alone: As the share of unconnected banks rises from 0.58 to 0.89 (pre- to post-2008 average), the capital stock falls 10% on aggregate and output declines 1.8% in the new steady state; no CB intervention occurs because CB and private haircuts are equal — banks have no incentive to use CB funding
η̃S shock alone (without prior ξ shift): Output falls only 0.15% even as private haircuts reach 40% in comparative statics; the muted effect arises because collateral markets are segmented in the baseline — Northern banks hold only Northern bonds (unaffected haircuts), fully counteracting Southern banks’ investment decline

Dynamic analysis (Section 6.2): In the full simulation combining both shocks:

The ξ shock causes an immediate output and investment overshoot below the new steady-state: anticipating future crowding-out of capital (unconnected banks hold bonds/reserves rather than investing), bank net worth falls immediately and leverage declines, pushing output below the eventual new steady state before gradual recovery
The η̃S shock (at t=13) additionally tightens collateral constraints for unconnected banks in the South; they endogenously switch to holding money as collateral, which integrates money markets across regions and creates a pecuniary externality on Northern banks (all banks now face the same higher collateral price for money) — a sharp contrast to the segmented-market comparative statics where Northern banks were unaffected
CB take-up peaks at 2.5% of total bank assets under CO policy, closely matching the data

CO policy vs CB policy counterfactual (Section 6.2.3, Figure 10):

Under the CO policy (benchmark: ECB keeps CB haircut at 3% while private market haircuts rise to 25%), unconnected banks in the South substitute expensive deposit funding for cheaper CB funding, reducing the collateral premium for money and directly benefiting Northern unconnected banks (pecuniary externality channel)
Under the CB policy (counterfactual: constant balance sheet, CB haircut = 100%), this substitution is impossible; collateral scarcity is unmitigated; the Northern banks’ spillover is larger
Main result: output and investment fall around twice as much on impact under the CB policy; the CB policy also produces a stronger post-crisis rebound as higher initial capital returns raise bank leverage
Conclusion: the ECB’s collateralized lending operations were crucial in containing the crisis, working through a haircut-gap channel that reduced the premium on collateral and attenuated the pecuniary externality between North and South

Scope conditions: Sovereign default risk on government bonds is treated as exogenous (the model does not endogenize default); the paper notes this would require a separate analysis linking haircuts to default probabilities. Prices are set one period in advance (not a full NK model), which disciplines inflation dynamics but is not a full monetary policy analysis. The model abstracts from the ECB’s Securities Markets Programme (sterilized asset purchases, not in scope). The two-region framework aggregates heterogeneous countries into North and South. Results depend on the perfect-foresight assumption; uncertainty about the path of shocks would introduce additional precautionary effects.

In depth

Q1. Why did the decline in unsecured interbank lending harm the real economy?

Unsecured interbank borrowing allows banks to pool idiosyncratic liquidity shocks without holding any liquid buffer; when unconnected banks (unable to borrow unsecured) must instead cover their maximum possible afternoon deposit outflow ωmaxD by holding bonds or reserves, they divert balance sheet capacity away from capital investment, crowding it out. As the share of unconnected banks rises from 42% to 90%, this crowding-out effect operates through two channels: (i) direct diversion of assets from productive capital to unproductive liquidity buffers; (ii) higher demand for collateral raises the collateral premium on bonds, increasing the effective cost of deposit funding and inducing all banks — even connected ones — to downsize their balance sheets through the leverage constraint.

Q2. Why was the steady-state impact of Southern haircuts muted while the dynamic impact was large?

In the baseline steady-state, collateral markets are segmented: Northern unconnected banks hold only Northern bonds (unaffected by Southern haircuts) and Southern unconnected banks hold only Southern bonds; in comparative statics, Northern banks absorb the capital freed by Southern banks’ disinvestment and the aggregate effect is small (−0.15% output for haircuts rising to 40%). In the dynamic model, however, the prior ξ shock has already pushed Northern unconnected banks to hold money as collateral (since high bond demand from all unconnected banks raises bond prices until money becomes the cheaper alternative); when Southern haircuts then spike, Southern banks also switch to money as collateral — and since money is a non-regional collateral, its price spike affects all unconnected banks simultaneously, integrating the previously segmented collateral markets and transmitting the Southern shock to the North.

Q3. How does the CO policy’s “haircut gap” channel work?

Under CO policy, the ECB maintains its haircut at 3% while private markets charge 25%; for each unit of collateral, a bank can access (1−0.03)=0.97 units from the ECB but only (1−0.25)=0.75 units from the private repo market — a 22-percentage-point haircut gap that makes ECB funding more efficient per unit of collateral pledged. When private haircuts rise, unconnected Southern banks face a collateral scarcity that makes deposit funding more expensive (higher afternoon constraint tightening); under CO policy, they optimally substitute toward CB funding, reducing their dependence on expensive deposits and mitigating the collateral premium spike. This directly benefits Northern unconnected banks because the reduced collateral premium for money (driven by Southern banks switching out of money as collateral) relaxes their own afternoon constraints without any direct exposure to Southern bonds.

Q4. Why does the CB policy produce a stronger post-crisis rebound?

The CB policy’s larger initial output and investment decline implies a larger undershoot below the new (post-ξ) steady state; during the recovery phase, banks face elevated returns on capital investment because capital is below its steady-state level; these higher returns raise bank net worth and allow more aggressive leverage, producing a steeper rebound than under the CO policy where the downturn was mitigated. This “larger crisis, faster recovery” tradeoff means the CB policy does not necessarily produce lower total welfare than the CO policy over the full cycle — the welfare comparison requires integrating the entire path, not just comparing the initial impact.

Q5. What makes the model require a non-linear solution?

The model features five inequality constraints that each can switch between binding and slack as parameters change: the morning leverage constraint, a collateral constraint on CB loans, and three short-sale constraints (kt,i ≥ 0, Bt,i ≥ 0, Dt,i ≥ 0). Standard linearized DSGE methods assume constraints are either always binding or always slack; here, for instance, connected banks begin holding positive money balances only when the share of unconnected banks rises past a threshold (0.61 in comparative statics), at which point the collateral premium rises enough to equalize returns on bonds and money — a kink that requires tracking which constraints are active. The Dynare Levenberg-Marquardt mixed complementarity solver handles these transitions, with T=400 periods imposed to ensure convergence to steady state.

Q6. What is the role of the leverage constraint in transmitting interbank frictions to the real economy?

The leverage constraint (Gertler-Karadi 2011) limits each bank’s total assets to Vt,i/λ; when money market frictions reduce the bank’s value Vt,i — either directly (collateral premia reduce bond prices and thus net worth) or through lower expected future net worth — the binding leverage constraint forces a proportional reduction in all assets including capital. This is the channel through which a purely financial friction in interbank markets (collateral scarcity) translates into a real investment decline: the leverage constraint links bank net worth to lending capacity, and interbank frictions that depress net worth also shrink investment. The result that “output and investment fall around twice as much” under CB policy is quantitatively driven by this chain: CB policy mitigates the collateral premium, preserving net worth and thus the lending capacity of banks.

Q7. Why do household deposits remain stable even as interbank markets are disrupted?

The model’s equilibrium has banks absorbing shocks through their balance sheet structure (switching between deposit funding, CB funding, bonds, and money) rather than through deposit supply; household deposits Dt,i are determined by households’ intertemporal optimization and the deposit rate, both of which are relatively insulated from the interbank friction. The friction operates within the banking system (between banks, or between banks and the CB), not in the retail deposit market; the afternoon liquidity shocks are interbank in nature (payment flows between banks) and are settled without household involvement. This matches Observation 4 from the data (stable household deposits) and is consistent with the mechanism: banks’ portfolio recomposition toward CB funding or bonds is a liability-side substitution that leaves retail deposits intact.

Key concepts

haircut gap channel : the mechanism through which the ECB’s policy of maintaining favorable haircuts (3%) on collateral while private market haircuts spike (to 25%) provides effective relief from collateral scarcity; banks can access more liquidity per unit of pledged collateral from the ECB than from the private repo market, inducing substitution from deposit funding to CB funding when the private haircut gap widens.

connected vs. unconnected banks : the model’s key bank heterogeneity; connected banks (fraction ξ) can borrow unsecured in the afternoon interbank market and therefore need no liquidity buffer; unconnected banks must cover their maximum afternoon payment outflow ωmaxD with reserves or pledged bond collateral, crowding out capital investment — the shift from ξ = 0.42 to ξ = 0.10 is the model’s representation of the euro area secured-market shift.

pecuniary externality (North-South spillover) : the channel through which a rise in Southern bond haircuts affects Northern banks even though Northern bonds are not repriced; when Southern banks switch to holding money as collateral, the demand for money rises, pushing up its collateral price; Northern unconnected banks (already holding money after the ξ shock) pay the higher price, tightening their afternoon constraint and reducing their capital investment indirectly.

collateral premium : the shadow price on bonds arising from their dual role as investment assets (in the morning) and collateral for afternoon liquidity (in the private repo or CB markets); when the afternoon constraint is binding, the collateral premium is positive — bonds are valued above their pure investment return — and determines how much of a bank’s balance sheet is diverted from capital to liquidity buffers.

CO policy vs CB policy : the paper’s two scenarios for the ECB’s response; CO policy (benchmark) maintains collateralized lending at a fixed (favorable) CB haircut, allowing CB balance sheet expansion as private haircuts rise; CB policy (counterfactual) keeps the balance sheet constant (CB haircut = 100%, no CB lending), forcing all liquidity needs to be met through private markets — the comparison isolates the macroeconomic value of the ECB’s lender-of-last-resort function.

Monopsony Makes Firms Not Only Small but Also Unproductive: Why East Germany Has Not Converged

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Summary

When employers face a trade-off between growing large and paying low wages — that is, when they have monopsony power — some productive employers will decide to acquire fewer customers, forgo sales, and remain small; these decisions have adverse consequences for aggregate labor productivity beyond the standard monopsony result that firms are too small. The paper documents that East German plants (compared to West German ones) face a steeper size-wage curve, invest less into marketing, and remain smaller, with the share of employment at plants with more than 249 employees standing at roughly 25% in East Germany versus 39% in West Germany in 2014 (and 31% versus 55% in manufacturing specifically). The steeper size-wage curve in East Germany is traceable to the historically determined underrepresentation of collective bargaining and union membership in small East German plants — a legacy of communist-era labor organization that caused union membership to collapse after reunification. The authors combine this evidence with a heterogeneous-plant model in which plants have product market power and choose how many customers to acquire subject to an upward-sloping size-wage schedule; two channels reduce aggregate productivity: a love-of-variety loss (fewer active plants means consumers bundle from a smaller variety of suppliers) and a compositional reallocation loss (labor is shifted from more productive to less productive plants, an effect exacerbated by product market power). When the model is calibrated to West Germany and the steeper East German size-wage trade-off is imposed, it predicts 10 percentage points lower aggregate labor productivity in East Germany — and for manufacturing, where East-West differences in plant size and the size-wage trade-off are particularly pronounced, the model predicts 18 percentage points lower productivity; in both cases the compression of the plant size distribution accounts for the largest share of the predicted productivity loss. The paper thus offers an explanation for why, more than thirty years after reunification, labor productivity and wages remain roughly 25% lower in the East German private sector despite uniform legal institutions across the two regions.

In depth

Q1. What is the core mechanism by which monopsony power reduces aggregate productivity, and how does it differ from the standard “firms are too small” result?

In the standard monopsony account, firms face an upward-sloping labor supply curve and choose to employ fewer workers than the competitive optimum, so individual firms are below efficient scale. The paper identifies an additional, investment-distortion channel: plants must also decide how large a customer base to acquire, and doing so requires marketing expenditure as well as the labor to service additional customers — labor whose cost rises with plant size along the size-wage schedule. A steeper size-wage curve therefore makes customer acquisition more expensive at the margin, and some productive plants optimally choose to acquire fewer customers, forgo sales, and remain small. The new aggregate productivity loss stems from this distorted investment margin: plants that could generate high value added at large scale instead operate at sub-optimal customer networks, suppressing aggregate output through both a love-of-variety effect (fewer active large plants means consumers access a smaller product variety) and a misallocation effect (the compressed size distribution shifts employment toward less productive plants).

Q2. What empirical patterns do the authors document to link the East-West productivity gap to missing large plants and steeper size-wage curves?

The authors document three nested empirical facts using the German Structure of Earnings Survey (SES) pooled across 2006, 2010, and 2014, supplemented by administrative wage panel data (AWFP) and national accounts (VGR). First, East German labor productivity in the private non-primary sector is about 25% below West Germany’s and has not converged since roughly 1995. Second, the share of employment at large plants (>249 employees) is substantially smaller in the East, and this gap is present both cross-sectionally across survey years and conditionally: East German plants enter smaller and remain smaller over their life-cycles, so plant age does not explain the difference. Third, industries where missing large plants are most pronounced in East Germany relative to West Germany are also the industries with the largest East-West productivity and wage gaps — the employment-weighted correlation between the large-plant share gap and the productivity gap is 0.53 across industries. The steeper size-wage curve itself is documented using within-industry comparisons: on average the plant size elasticity of wages is one-fifth larger in East Germany, and those industries with a steeper East-West size-wage differential are also the industries with the most missing large plants and the lowest average wages in the East.

Q3. Why is the steeper size-wage curve specific to East Germany, and why does it persist decades after reunification?

In communist East Germany, trade unions did not have the role of representing worker interests; consequently, after reunification, union membership fell dramatically. The key institutional consequence is that collective bargaining coverage in East Germany is underrepresented specifically in small plants. Workers at small plants in East Germany are more likely to have individually rather than collectively bargained wages than their West German counterparts, whereas workers at large plants in both regions are more similarly covered. Because collective bargaining flattens the size-wage curve (larger plants pay a smaller premium over small plants’ wages when both are covered by the same bargaining agreement), its absence in small East German plants produces a steeper gradient of wages with plant size in the East. This is a persistent structural feature rather than a transitional one: government policies and their enforcement are essentially uniform across regions, so the asymmetric bargaining coverage, which originates in communist-era institutional history, has not been erased by market forces or policy since 1990.

Q4. How is the model structured, and what are the three decision stages for plants?

The model is a static, long-run heterogeneous-plant framework that yields closed-form solutions. Within a period, plants face a three-stage decision problem. First, they decide whether to enter the market. Second, after entry, they choose how many customers to acquire, trading off additional sales revenue against marketing costs and the labor cost of servicing a larger customer base — a cost that rises with the number of customers because the upward-sloping size-wage curve means each additional worker hired requires a higher wage for all infra-marginal workers. Third, taking into account their product market power (each plant is a monopolistic competitor with its own customers), plants set prices to each customer and thereby determine how many workers they need. The size-wage schedule enters the second stage directly, so a steeper schedule reduces optimal customer acquisition across all plants, with the distortion being largest for the most productive plants (which would otherwise grow the largest).

Q5. Through what two channels does the steeper size-wage trade-off reduce aggregate labor productivity in the model?

The first channel is a love-of-variety effect in the product market: because more productive plants acquire fewer customers and operate at smaller scale under a steeper size-wage schedule, the average consumer bundles goods from a smaller number of distinct plants, and aggregate efficiency falls through the standard CES love-of-variety mechanism. The second channel is a misallocation effect in the labor market: the steeper size-wage schedule compresses the employment distribution across plants, reallocating labor from more productive to less productive plants relative to the benchmark with a flatter schedule. The paper shows that this second channel is exacerbated by product market power, because plants with stronger pricing power respond more aggressively to the changed labor cost trade-off. In the model’s decomposition, the compression of the plant size distribution (the misallocation channel) accounts for the largest part of the predicted 10 percentage point productivity shortfall.

Q6. What quantitative predictions does the model make, and how does it perform in untargeted moments?

The model is calibrated to two moments for West Germany: average plant size and the share of large plants (>249 employees). When the steeper East German size-wage trade-off is imposed without re-calibrating other parameters, the model predicts 10 percentage points lower aggregate labor productivity in East Germany — accounting for at least 10 of the roughly 25 percentage point observed gap. For the manufacturing sector alone, where East-West differences in plant size, the size-wage trade-off, and aggregate productivity are particularly pronounced, the calibrated model predicts 18 percentage points lower productivity. As an untargeted validation, the model also replicates the plant size distribution in East Germany, matching both the smaller average plant size and the relatively small number of large plants. These untargeted predictions provide additional support for the mechanism.

Q7. What alternative explanations for East Germany’s non-convergence does the paper rule out or place in context?

The paper addresses several confounds. In Appendix A, the authors show that East-West aggregate labor productivity differences are driven by differences in aggregate total factor productivity, not by labor quality differences, capital intensity differences, or capital quality differences — confirming within-country the finding that TFP explains a large fraction of productivity dispersion. The TFP differences are shown to be unlikely the result of greater labor market flexibility in West Germany or differences in industry composition. Appendix B shows that the East-West plant size distribution gap is not driven by differences in urbanization (West Germany has more metropolitan areas). The paper also addresses plant age: East German plants enter smaller and remain smaller at every age and across entry cohorts, ruling out the hypothesis that the size gap is purely a transitional legacy of the restructuring that destroyed many large East German plants at reunification.

Q8. How does this paper relate to the Heise and Porzio (2021) finding that plant productivity differences, not worker quality differences, drive the East-West wage gap?

Heise and Porzio (2021) use matched employer-employee data to document that plant productivity differences (as opposed to worker quality differences) account for most of the East-West wage differential, and they explain why low worker mobility does not remove these differences. The present paper complements this by providing an explanation for why plant productivity is lower in East Germany in the first place and why firm-level convergence does not occur: the steeper size-wage curve induced by the legacy of missing collective bargaining coverage in small East German plants distorts the investment and customer acquisition decisions of productive plants, keeping them small and unproductive. The two papers are thus complementary: Heise and Porzio take the plant productivity gap as given; Bachmann et al. endogenize it through the size-wage mechanism.

Key Concepts

Size-wage curve: The empirical relationship between plant size (measured by employment) and wages paid to workers, conditional on worker characteristics. A steeper size-wage curve means that the wage premium for working at a large plant relative to a small plant is larger. In this paper’s model, plants internalize that expanding their customer base and workforce requires paying higher wages to all workers (not just the marginal hire), making growth more costly when the size-wage curve is steeper.

Monopsony power (monopsonistic competition): The market structure in which an individual employer faces an upward-sloping labor supply curve — i.e., it must raise wages to attract additional workers. The paper uses “monopsonistic competition” to describe a setting with many such employers, each with some wage-setting power, in contrast to oligopsony. The paper focuses on allocative effects of this power, not on normative efficiency questions.

Customer capital / customer acquisition: Plants must incur marketing expenses to build a customer base; each customer relationship generates a stream of sales but requires labor to service. The size of the customer network is a long-run investment decision. Under monopsonistic labor markets, the cost of expanding the customer base includes not only marketing expenses but also the higher wages that a larger workforce requires, making customer acquisition a margin that is distorted by labor market power.

Love-of-variety effect: A welfare loss that arises in models with monopolistic competition and CES preferences when the number of active product varieties declines. In this paper it applies to the product market: when plants remain small and acquire fewer customers, the effective number of distinct varieties consumed falls, reducing aggregate efficiency even holding plant-level productivity fixed.

Misallocation / compressed size distribution: A situation in which factors of production are not allocated to their highest-value uses. Here, the steeper size-wage curve induces productive plants to remain small, so labor that would otherwise be employed at high-productivity large plants is instead employed at lower-productivity small plants. The resulting compression of the plant size distribution — fewer very large plants, more mass in the middle — is both the key empirical fact and the primary quantitative driver of the predicted aggregate productivity shortfall.

Collective bargaining coverage: The fraction of workers whose wages are set by collective agreements between employers (or employer associations) and trade unions, rather than by individual negotiation. The paper establishes that collective bargaining flattens the size-wage curve by compressing wages across plants of different sizes. The historically low collective bargaining coverage among small East German plants — a legacy of communist-era labor relations — is the institutional root cause of the steeper East German size-wage schedule.

Narratives about the Macroeconomy

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

This paper investigates two related empirical questions in the context of the historic surge in US inflation in late 2021 and 2022: (1) What narratives—causal stories—do people invoke to explain why inflation increased? (2) How do those narratives shape economic expectations? A companion theoretical component asks how narrative heterogeneity affects aggregate macroeconomic outcomes.

Data and Methodology

The authors recruit more than 10,000 US households across five descriptive survey waves (November 2021, December 2021, January 2022, March 2022, May 2022) via Lucid, plus a separate expert survey of 111 academic economists with JEL-E publications in top journals, recruited simultaneously with the November 2021 household wave. Household samples are broadly representative of the US population in terms of gender, age, region, and income. The expert sample is highly credentialed: on average 18.6 years post-PhD, 2.7 top-five publications, and 5,534 Google Scholar citations.

Narratives are elicited through open-ended questions asking respondents to explain in their own words why inflation increased. Each text response is coded by two independent, blinded research assistants as a Directed Acyclic Graph (DAG) — a network of causal nodes representing factors (demand-side: government spending, monetary policy, pent-up demand, demand shift; supply-side: supply chain disruptions, labor shortage, energy crisis; miscellaneous: pandemic, government mismanagement, price gouging, Russia-Ukraine war) connected by directed causal edges. Inter-rater reliability is high: if one coder identifies a factor, the other does so 88% of the time; for specific causal connections between factors, agreement is 77%.

Three experiments study the causal effect of narratives on expectations: (1) A pent-up demand vs. energy crisis narrative provision experiment (April 2022, n=2,397 baseline, n=1,329 follow-up); (2) A monetary policy vs. energy crisis narrative provision experiment (June 2022, n=1,069 baseline, n=736 follow-up); (3) A 2×2 belief-updating experiment crossing narrative type (government spending vs. energy crisis) with information type (low vs. high government spending forecast) (April 2022, n=997).

Main Findings with Quantitative Magnitudes

Households’ narratives are substantially coarser than experts’: expert DAGs contain on average 4.3 factors and 3.6 causal links, while household DAGs contain only 3.5 factors and 2.8 links (both differences p < 0.01). Households focus predominantly on supply-side explanations: 57% invoke at least one supply-side factor vs. only 32% invoking any demand-side factor. The most common household narrative factors are supply chain disruptions (30%), labor shortage (27%), and general supply-side factors (22%); the leading demand-side factor is government spending, appearing in only 17% of household narratives, while loose monetary policy appears in just 5%. By contrast, 90% of experts invoke at least one supply-side factor and 84% at least one demand-side factor, with government spending mentioned by 50% of experts and monetary policy by 38%.

Among households who invoke at least one supply or demand narrative, only 34% mention both supply and demand factors; among the corresponding subsample of experts, 77% mention both. Government mismanagement—a politicized judgment of policy failure—appears in 32% of household narratives but only 1% of expert narratives. Price gouging appears in 8% of household narratives and 0% among experts.

Partisan polarization is large: Democrat-leaning respondents are 26 pp more likely to attribute inflation to the pandemic as a root cause (p < 0.01); Republican-leaning respondents are 38 pp more likely to blame government mismanagement (p < 0.01), and 19 pp more likely to mention high government spending (p < 0.01) and 14 pp more likely to mention high energy prices (p < 0.01).

Narratives are correlated with inflation expectations in OLS regressions controlling for demographics and survey wave fixed effects (n=2,951): households invoking government mismanagement predict 1.155 pp higher 1-year-ahead inflation (p < 0.01) and 0.805 pp higher 5-year-ahead inflation (p < 0.01). Energy crisis narratives predict 0.661 pp higher 1-year-ahead inflation (p < 0.01). Pent-up demand narratives predict 0.640 pp lower 5-year-ahead inflation (p < 0.05). Narrative variables explain approximately 10% of the out-of-sample variation in 1-year-ahead inflation expectations via LASSO, comparable to or exceeding the explanatory power of demographics and inflation experiences found in prior work.

In Experiment 1 (pent-up demand vs. energy crisis), providing the pent-up demand narrative reduces 12-month inflation expectations by 0.71 pp relative to the energy crisis treatment (p < 0.01, in the main survey), corresponding to 24% of a standard deviation. This effect persists in the follow-up survey one day later (−0.63 pp, p < 0.01).

In Experiment 2 (monetary policy vs. energy crisis), the monetary policy narrative reduces 12-month inflation expectations by 0.40 pp at the time of the main survey (p < 0.01) and by 0.62 pp in the follow-up (p < 0.01).

In Experiment 3 (information updating), respondents exposed to the government spending narrative increase 12-month inflation expectations by 1.79 pp in response to a high-spending forecast (p < 0.01), while those exposed to the energy crisis narrative show no significant reaction (0.34 pp, p = 0.205). In IV regressions instrumenting government spending expectations with the high/low forecast treatment, a 1 pp increase in perceived government spending growth raises inflation expectations by 0.378 pp among those holding the government spending narrative (p < 0.01) versus only 0.051 pp among those holding the energy narrative (p = 0.184; difference p < 0.01).

The New Keynesian DSGE model shows that a modest shift in perceived importance of monetary policy relative to productivity (raising ω_ν from 0.1 to 0.2, holding ω_g fixed) raises equilibrium consumption by 27 basis points and reduces equilibrium inflation by 27 basis points in the calibrated model with φ = 1.5; with a less reactive central bank (φ = 1.25), the same shift raises consumption by 30 basis points and reduces inflation by 62 basis points.

Scope Conditions

All empirical results are drawn from the US context during the 2021–2022 inflation surge. The authors note that the extent of partisan polarization in US narratives may not generalize to less politically polarized countries. The test-retest correlation of narrative factors across a three-day interval is 0.63 (p < 0.01), indicating significant but not perfect stability. The experiment results may partly reflect that narratives were especially malleable because the inflation surge was a relatively recent and salient phenomenon at the time of data collection.

In depth

Q1. How do the authors define and operationalize “narratives”?

A: The paper defines economic narratives as causal accounts for why an economic event occurred — agents’ assessments of cause-effect relationships across events. Each text response is coded as a Directed Acyclic Graph (DAG) where nodes are economic factors and directed edges represent perceived causal links. DAGs can represent both simple mono-causal accounts and complex multi-factor chains. The authors use a predefined coding scheme of 16+ factor categories spanning demand-side, supply-side, and miscellaneous nodes, with inflation as the terminal node.

Q2. What is the inter-rater reliability of the DAG coding, and what does it imply for the quality of the narrative data?

A: Two independent, blinded coders annotate each response. If one coder assigns a given factor, the other does so 88% of the time; for specific causal connections between factors, agreement is 77%. Approximately 95% of assigned factors and 89% of assigned connections make it to the final coded version. At the coarser level of “any demand-side factor,” agreement rises to 94%; for “any supply-side factor,” to 93%. Test-retest reliability across a three-day interval averages a correlation of 0.63 across all narrative factors (p < 0.01), comparable in magnitude to the measured persistence of economic preferences in prior work.

Q3. How do expert and household narratives differ in their structural complexity?

A: Expert DAGs contain on average 4.3 factors and 3.6 causal links, compared to 3.5 factors and 2.8 links for households (both p < 0.01). These differences persist even after controlling for response time and word count, indicating genuine differences in economic understanding rather than effort. Among agents who invoke at least one supply or demand factor, 77% of experts mention both, compared to only 34% of households.

Q4. What are the most prevalent factors in household narratives versus expert narratives, and why does this matter?

A: Supply chain disruptions (30%), labor shortage (27%), and general supply-side factors (22%) top household narratives, while monetary policy appears in only 5% of household DAGs. Expert narratives are more balanced: 90% cite supply-side factors and 84% cite demand-side factors, with government spending mentioned by 50% and monetary policy by 38%. This matters because factors with different persistence imply different trajectories for future inflation; households’ supply-side emphasis, combined with low awareness of monetary policy, shapes their inflation expectations in systematically different ways than experts.

Q5. What is the structure of household narrative clusters, and how fragmented are they?

A: Agglomerative hierarchical clustering using the Jaccard distance between DAG edge lists reveals 15 optimal clusters (Silhouette criterion), of which eight have at least 30 members. Four supply-side clusters account for 55% of households: pandemic-related supply chain disruptions (20%), general supply-side causes (18%), energy crisis often attributed to government mismanagement (11%), and labor shortages attributed to the pandemic or government spending (7%). The only clear demand-side cluster—combining government spending and loose monetary policy—captures just 8%. Simple mono-causal clusters attributing inflation to the pandemic alone (15%), government mismanagement alone (11%), and price gouging alone (4%) are collectively prominent, underscoring how fragmented and often single-factor household reasoning is.

Q6. How do partisan affiliations correlate with narrative content?

A: Republicans are 38 pp more likely than Democrats to attribute inflation to government mismanagement (p < 0.01), 19 pp more likely to mention high government spending (p < 0.01), and 14 pp more likely to mention high energy prices (p < 0.01). Democrats are 26 pp more likely to cite the pandemic as a root cause of inflation (p < 0.01) and more frequently cite pandemic-related supply chain issues and corporate greed. Government mismanagement appears in 32% of all household narratives (and is often portrayed as a root cause of spending, monetary policy, and energy prices) but in only 1% of expert narratives.

Q7. How did the composition of household narratives shift over time (November 2021 to May 2022)?

A: The energy crisis narrative rose sharply from 12% in January 2022 to 28% in March 2022, coinciding with Russia’s invasion of Ukraine in late February 2022. The Russia-Ukraine war narrative went from virtually zero before February 2022 to 28% in March 2022. By contrast, pandemic references, which climbed from 44% in November 2021 to 55% in January 2022, fell back to 47% in March 2022 and 39% in May 2022. Labor shortage references fell sharply from 32% in January 2022 to 15% in May 2022. These abrupt shifts suggest household narratives respond to major news events and, by extension, could drive rapid revisions in inflation expectations around such events.

Q8. What is the correlational evidence that narratives predict inflation expectations, and how large is the explanatory power?

A: OLS regressions on pooled data from November 2021–January 2022 (n=2,951), controlling for survey wave fixed effects and sociodemographics, show: government mismanagement narratives predict 1.155 pp higher 1-year inflation expectations (p < 0.01) and 0.805 pp higher 5-year expectations (p < 0.01); energy crisis narratives predict 0.661 pp higher 1-year expectations (p < 0.01); monetary policy narratives predict 1.005 pp higher 1-year expectations (p < 0.01); pent-up demand narratives predict 0.640 pp lower 5-year expectations (p < 0.05). LASSO out-of-sample prediction using DAG factor dummies and connection dummies explains approximately 10% of variation in 1-year-ahead inflation expectations — comparable to the 10% within-sample R² found by D’Acunto et al. (2021) for grocery price exposure, and substantially above the 2–7% found by Giglio et al. (2021) for investor characteristics explaining stock return expectations.

Q9. What does Experiment 1 (pent-up demand vs. energy crisis) show about the causal effect of narratives?

A: Providing the pent-up demand narrative (relative to the energy crisis narrative) increases the fraction of respondents invoking pent-up demand by 37.8 pp in the follow-up survey (baseline: 2.8%, p < 0.01) and reduces the fraction invoking the energy crisis by 7.9 pp (p < 0.01), establishing successful first-stage uptake. In the main survey (n=2,397), the pent-up demand treatment reduces 12-month inflation expectations by 0.71 pp relative to the energy treatment (p < 0.01), equivalent to 24% of a standard deviation; the effect persists at −0.63 pp in the follow-up one day later (p < 0.01). The energy crisis treatment has no significant effect on expectations relative to a pure control (−0.02 pp, p = 0.911), suggesting that energy crisis implications were already salient at the time.

Q10. What does Experiment 2 (monetary policy vs. energy crisis) add, given it was conducted after significant Fed tightening?

A: The experiment was run in June 2022, when 61% of respondents were already aware the Fed had raised rates. The monetary policy narrative increases the fraction invoking monetary policy by 39 pp and reduces the energy fraction by 50 pp relative to the energy group (both p < 0.01). The monetary policy narrative reduces 12-month inflation expectations by 0.40 pp in the main survey (p < 0.01) and 0.62 pp in the follow-up (p < 0.01). The mechanism is that attributing past inflation to loose monetary policy — which has since been tightened — leads respondents to infer lower future inflation, consistent with the narrative about persistence of the underlying cause.

Q11. What does Experiment 3 demonstrate about how narratives filter the interpretation of new information?

A: In the 2×2 design, all respondents first receive either a government spending narrative or an energy crisis narrative, then either a low (−4%) or high (+6%) government spending forecast from the Survey of Professional Forecasters. Among those with the government spending narrative, the high-spending forecast raises 12-month inflation expectations by 1.79 pp (p < 0.01); among those with the energy crisis narrative, the high-spending forecast raises inflation expectations by a non-significant 0.34 pp (p = 0.205). The IV estimate shows that a 1 pp increase in expected government spending growth raises inflation expectations by 0.378 pp for those holding the spending narrative (p < 0.01) vs. 0.051 pp for those holding the energy narrative (p = 0.184); this difference is highly significant (p < 0.01). Importantly, the first-stage effect on expected government spending growth is similar across narrative groups (4.7 pp vs. 6.8 pp, difference not significant), ruling out differential interpretation of the forecast itself as the mechanism.

Q12. How do the authors formalize narratives in the DSGE model, and what is the key mapping result?

A: Narratives are formalized as subjective causal models (SCMs): linear mappings from N observable factors to inflation, π_t = ψ_1(i)z_{1,t} + … + ψ_N(i)z_{N,t}, combined with perceived AR(1) processes for each factor. The “subjective inflation narrative” of agent i is summarized by perceived contribution shares ω_z(i). The paper’s Proposition 2 gives closed-form expressions for equilibrium inflation and consumption as functions of these perceived shares, without imposing that they be correct or identical across agents. The key result is that subjective causal models always affect equilibrium outcomes so long as the perceived persistence parameters differ across factors — the mechanism being that different narratives produce different inflation expectations, which feed back into consumption and pricing decisions.

Q13. What are the quantitative implications of narrative shifts in the calibrated DSGE model?

A: The baseline calibration uses standard New Keynesian parameters (β=0.99, γ=1, ς=5, Calvo price duration=4 quarters, φ=1.5, ρ_a=0.9, ρ_g=0.8, ρ_ν=0.5) with a scenario of a 10% productivity decline, 10% government spending increase, and policy rate 2 pp below the Taylor rule. Under rational expectations, π_t=3.68% and c_t=−11.79%. Raising the perceived importance of monetary policy in household and firm inflation narratives from ω_ν=0.1 to ω_ν=0.2 (lowering ω_a by the same amount, holding ω_g fixed) increases equilibrium consumption by 27 basis points and reduces equilibrium inflation by 27 basis points. With a less reactive central bank (φ=1.25), the same narrative shift raises consumption by 30 basis points and reduces inflation by 62 basis points. The paper notes that these effects are approximately linear in the narrative shift, meaning the directional implication holds across a wide range of narrative configurations.

Q14. How does narrative heterogeneity across households affect aggregate outcomes in the model?

A: When households hold heterogeneous narratives, aggregate outcomes depend on the joint distribution of perceived factor importance (ω_z(i)) and perceived factor persistence (ρ_z(i)) across agents, rather than on average values alone. Specifically, the model shows that if households who assign higher importance to a given factor also perceive that factor as more persistent, the aggregate effect on expectations and consumption is amplified beyond what the average narrative predicts. Additionally, narrative heterogeneity generates consumption heterogeneity even when the efficient allocation requires all households to consume the same amount, representing a welfare-relevant distortion absent under rational expectations.

Q15. What is the practical implication for central bank communication?

A: Under full-information rational expectations, central bank narrative communication about the drivers of inflation is irrelevant because agents already hold the correct model. Once subjective causal models can deviate from the truth, central bank narrative provision shifts aggregate equilibrium outcomes (inflation and consumption) in a benchmark New Keynesian model. The paper argues that central banks need to measure the distribution of household narratives to know whether their communication shifts agents toward or away from the rational expectations equilibrium — moving agents in the direction of the correct narrative produces better aggregate outcomes from the central bank’s perspective, conditional on inflation being above target and output below first-best.

Key Concepts

Economic Narrative (as used in this paper): An agent’s causal account for why a given economic event occurred — specifically, an assessment of cause-effect relationships that explains the drivers of an economic outcome. Distinguished from more general notions of “story” in that causality is the core; the paper does not count descriptions of correlation or simple statements of fact as narratives.

Directed Acyclic Graph (DAG) representation of narratives: Each narrative is coded as a network of factor nodes connected by directed edges indicating perceived causation. Acyclicity rules out feedback loops in a respondent’s causal account. Factors with nonzero ψ(i) are included; the direction of edges indicates causal flow. This representation allows quantitative comparison across respondents via adjacency matrices or Jaccard distances between edge lists.

Subjective Causal Model (SCM) of inflation: The paper’s formal theoretical counterpart to a narrative: a linear mapping π_t = Σ_n ψ_n(i) z_{n,t} in which individual i assigns perceived marginal effect ψ_n(i) to each factor z_n, combined with a perceived AR(1) law of motion for each factor. The SCM does not need to be correct or shared across agents. The rational expectations equilibrium is the special case where all agents’ SCMs match the true data-generating process.

Perceived contribution share (ω_z): The ratio ψ_z(i)·z_t / π_t — agent i’s perceived percentage contribution of factor z to current inflation. This is the sufficient statistic for the effect of household narratives on inflation expectations and, through the NK model, on equilibrium aggregate outcomes. The aggregate distribution of ω_z(i) and perceived persistence ρ_z(i) determines the consumption Euler equation at the aggregate level.

Government mismanagement (as a narrative factor): A coding category that captures explicit reference to policy failure or low-quality decision-making by policymakers in a politicized sense — distinct from the economic factors of government spending or monetary policy. It represents households’ attribution of inflation to the incompetence or malfeasance of officials, rather than to any specific economic mechanism. This factor appears in 32% of household narratives but only 1% of expert narratives.

Narrative cluster: A group of respondents whose DAGs are mutually similar (measured by Jaccard distance between edge lists) and whose typical DAG differs from other clusters. Identified via agglomerative hierarchical clustering. The paper identifies eight substantively meaningful clusters, ranging from supply-chain-focused to mono-causal pandemic or mismanagement narratives, with no single cluster capturing more than 20% of households.

Test-retest reliability of narratives: The correlation between the same respondent’s narrative elicited on two occasions three days apart. The paper estimates an average correlation of 0.63 across all narrative factors (p < 0.01), interpreted as indicating significant stability in households’ causal beliefs rather than survey noise. Comparable in magnitude to test-retest correlations of economic preferences in other studies.

Normal Approximation in Large Network Models

Mon, 01 Jan 0001 00:00:00 +0000

This paper proves a central limit theorem (CLT) for network formation models with strategic interactions and homophilous agents, addressing a foundational inferential gap in the econometrics of large networks. The setting is one where the econometrician observes a single large network — the asymptotic framework sends network size n to infinity — which is the empirically relevant case for most network datasets. The network moments of interest are averages of node-level statistics (1/n) Σ ψ_i, where ψ_i can capture degree, clustering coefficients, or subnetwork counts (triangles, k-stars) that have been used for structural inference in network formation games.

The model is a pairwise-stability network formation game augmented onto a latent-space/geometric-graph structure. Each node i has an i.i.d. type (X_i, Z_i), where X_i is a continuously distributed position vector capturing homophilous attributes. Two nodes i and j form a link if a joint-surplus function V(·) exceeds zero, where V depends on the scaled distance r_n^{-1}‖X_i − X_j‖ between positions, a vector of strategic interaction statistics S_{ij} (functions of neighboring links), node attributes Z_i, Z_j, and an i.i.d. utility shock ζ_{ij}. Homophily enters as a monotonicity requirement: V is decreasing in the distance component, so dissimilar nodes are less likely to link. Sparsity is ensured by setting r_n = (κ/n)^{1/d}, which keeps expected degree asymptotically bounded.

Strategic interactions enter through S_{ij}, which depends on links involving neighbors of i or j (local externalities), generating chains of cross-sectional dependence that are the central obstacle to the CLT. The paper identifies two distinct sources of dependence: (1) link interdependencies from best-response chains, where the realization of one link influences neighboring links; and (2) global coordination in equilibrium selection, where agents may condition on a common signal.

The main technical contribution is adapting “stabilization” conditions from the literature on geometric graphs (Penrose and Yukich 2003, 2008) to the strategic setting. Exponential stabilization (Assumption 5) requires that the radius of stabilization R_i — the smallest neighborhood of i such that ψ_i depends only on nodes within that neighborhood — has a distribution with exponential tails. This bounds the effective dependence neighborhood and provides the weak dependence structure needed for the CLT.

To verify stabilization from primitive conditions, the paper employs branching process theory. The key construct is the “strategic neighborhood” C_i^+, the component of i in the network of non-robust links D (pairs where strategic interactions can change the link outcome). The paper bounds |C_i^+| by a subcritical Galton-Watson branching process: if the mean offspring is below 1 (subcriticality, Assumption 7, stated as ‖h*‖_m < 1), the process is non-explosive and its size has exponential tails, yielding the required stabilization. The subcriticality condition directly restricts the strength of strategic interactions and is the network analog of the condition ‖β‖ < 1 in linear autoregressive models. A second condition (Assumption 8, decentralized selection) requires that equilibrium selection operates independently across disjoint strategic neighborhoods, ruling out global coordination; this holds under myopic best-response dynamics.

For inference, the paper proposes a network HAC variance estimator hat_Σ_n = (1/n) Σ_i Σ_j k(d_{ij}/b_n) hat_ψ_i hat_ψ_j^T, where k(·) is a kernel, d_{ij} is the path distance in A, and b_n is a bandwidth, and a network bootstrap that resamples nodes with replacement. Both are shown to be consistent (Theorem 3). Simulation results with n up to 500, varying strategic interaction strength θ_2 from 0 to 0.5, show that the network HAC estimator achieves nominal 5% rejection rates and 95% coverage for n ≥ 500, while the bootstrap slightly over-rejects in small samples and performance degrades as θ_2 increases.

The scope conditions are explicit: the CLT applies to sparse networks (expected degree bounded), undirected networks with local externalities, models admitting a pairwise-stability equilibrium, and equilibrium selection satisfying decentralization. Extensions to directed or denser networks are left for future work.

Q: What is the primary research question and why does it require new theory? A: The paper asks when sample averages of network statistics — degree, clustering, subnetwork counts — satisfy a CLT in strategic network formation models observed as a single large network. Standard CLT proofs require weakly dependent observations, but strategic interactions generate chains of link dependence of a priori unbounded length, and multiple equilibria allow global coordination, both of which can destroy asymptotic normality. Prior work (Leung 2019b; Menzel 2024) established laws of large numbers but not CLTs, which require stronger conditions.

Q: What is the stabilization condition and why is it the right formulation of weak dependence? A: Exponential stabilization (Assumption 5) requires that the radius of stabilization R_i — the smallest K such that ψ_i depends only on the K-neighborhood of i in the network — has a distribution with exponential tails: lim sup_{w→∞} w^{-η} max{log τ_{b,ε}(w), log τ_p(w)} < 0 for some η ∈ (0,1]. This implies that each node’s statistic depends effectively only on a bounded fraction of the network, making {ψ_i} weakly dependent. The condition is a modification of stabilization conditions from the geometric graph literature (Penrose and Yukich 2003, 2008) adapted to allow strategic interactions.

Q: How does the paper connect the abstract stabilization condition to primitive model conditions? A: The paper defines the strategic neighborhood C_i^+ as the union of one-step network neighborhoods of nodes in i’s component in the non-robust link network D (where D_{ij} = 1 iff the link A_{ij} can be switched by strategic interactions). The size |C_i^+| controls the radius of stabilization. By mapping exploration of C_i via breadth-first search onto a Galton-Watson branching process, subcriticality (mean offspring < 1, i.e., ‖h*‖_m < 1) implies that |C_i^+| has exponential tails, which yields exponential stabilization with η = 1 (Theorem 2).

Q: What is the subcriticality condition and what does it restrict? A: Subcriticality (Assumption 7) requires that the mean interaction-strength measure satisfies ‖h*‖_m < 1, where h* bounds the probability that a given link is non-robust as a function of node attributes. This restricts how strongly the existence of one link influences the probability of neighboring links. The authors explicitly analogize this to the condition ‖β‖ < 1 in linear autoregressive models: both bound the magnitude of “autoregressive” dependence below one to prevent explosive propagation of dependence.

Q: What is the decentralized selection condition and what does it rule out? A: Assumption 8 (decentralized selection) requires that the equilibrium selection mechanism operates independently across disjoint strategic neighborhoods: A_{H_l} = λ_{|H_l|}(r^{-1}T_{H_l}, ζ_{H_l}) for each disjoint strategic neighborhood H_l. This rules out global coordination where agents condition on a common signal (such as the type of a particular node) to jointly select an equilibrium. The condition is satisfied by myopic best-response dynamics and is described as the single-network analog of requiring equilibrium selection to be independent across networks under many-network asymptotics.

Q: What is the structure of the CLT proof? A: The proof has two steps. Step 1 proves a CLT for the Poissonized model where the number of nodes N_n ~ Poisson(n), leveraging results from Penrose and Yukich (2008) for geometric graphs extended to the strategic setting. Step 2 is a de-Poissonization argument that transfers the Poissonized CLT back to the fixed-n model. The abstract CLT (Theorem 1) requires Assumptions 5 and 6, and Theorem 2 establishes that Assumptions 1–8 imply Assumption 5 with η = 1.

Q: How does the network HAC estimator work and what are its consistency conditions? A: The estimator is hat_Σ_n = (1/n) Σ_i Σ_j k(d_{ij}/b_n) hat_ψ_i hat_ψ_j^T, where d_{ij} is the path distance between i and j in the observed network A, k(·) is a kernel function, b_n is a bandwidth, and hat_ψ_i = ψ_i(N_n) − (1/n) Σ_j ψ_j(N_n) is the demeaned statistic. Consistency (hat_Σ_n →^p Σ_n) is established under appropriate conditions on the bandwidth b_n (Theorem 3). The bandwidth plays the same role as in time-series HAC estimation, controlling the window over which covariances are summed.

Q: What do the simulations show about finite-sample performance? A: Using a DGP with X_i ~ U([0,1]^2), ζ_{ij} ~ N(0,1), and θ_2 varying from 0 to 0.5 to control strategic interaction strength, the network HAC estimator achieves nominal 5% rejection rates and 95% coverage at n ≥ 500 across all settings. The bootstrap slightly over-rejects in small samples. Performance of all procedures degrades as θ_2 increases (stronger strategic interactions), consistent with the theoretical condition that subcriticality must hold. These results support practical use of the inference procedures based on Theorem 1.

Q: How does this paper relate to prior work on CLTs for network data? A: Kojevnikov et al. (2021) prove a CLT for node-level data conditional on the network, but this does not apply to network formation because the network is the outcome, not a conditioning variable. Leung (2019b) and Menzel (2024) prove laws of large numbers for strategic network formation but not CLTs. Kuersteiner (2019) takes a different approach using a conditional mixingale assumption. The paper’s abstract CLT extends Penrose and Yukich (2008) by modifying the stabilization condition to accommodate strategic interactions; the primitive conditions are new and use branching process tools that build on Leung (2019b).

Q: What network moments can the CLT be applied to? A: The CLT applies to any average of node statistics ψ_i that depends only on the K-neighborhood of i in the network (Assumption 4 with finite K). Explicit examples include average degree (ψ_i = Σ_j A_{ij}), average clustering coefficient, and counts of connected subnetworks such as triangles and k-stars. Subnetwork counts have been used as the basis for structural identification and estimation of network formation games (Sheng 2020), making the CLT directly applicable to inference in those models.

Q: What are the scope limitations and directions for future work? A: The CLT applies to sparse undirected networks with local externalities (Assumption 2), homophily in positions (Assumption 1), and equilibrium selection satisfying decentralization (Assumption 8). It does not cover directed networks, denser networks where expected degree grows with n, or models with global link externalities. The authors identify extending results to directed and denser networks and developing more powerful inference procedures exploiting network structure as priorities for future work.

Stabilization (exponential): The condition that the radius of stabilization R_i — the smallest neighborhood of i beyond which ψ_i does not depend on further nodes — has a distribution with exponential tails (lim sup_{w→∞} w^{-η} log τ(w) < 0 for η ∈ (0,1]). This is the paper’s operative formulation of weak dependence for network statistics and is adapted from geometric graph theory to the strategic setting.

Strategic neighborhood (C_i^+): The union of one-step neighborhoods of nodes in i’s component in the non-robust link network D. A link (i,j) is non-robust (D_{ij} = 1) if strategic interactions can change its realization — i.e., the surplus V can be positive under some interaction configurations and non-positive under others. The size of C_i^+ governs the radius of stabilization and hence the degree of cross-sectional dependence.

Subcriticality (‖h*‖_m < 1): The condition that the mean-field interaction strength measure satisfies ‖h*‖_m < 1, where h* bounds the conditional probability that a link is non-robust. Subcriticality ensures that breadth-first search of the strategic neighborhood is dominated by a subcritical Galton-Watson process (mean offspring < 1), preventing explosive growth of the dependence neighborhood. The paper explicitly frames this as the network analog of ‖β‖ < 1 in autoregressive models.

Decentralized selection (Assumption 8): The requirement that the equilibrium selection mechanism assigns outcomes independently across disjoint strategic neighborhoods: A_{H_l} = λ_{|H_l|}(r^{-1}T_{H_l}, ζ_{H_l}) for each disjoint H_l. This rules out global coordination — agents conditioning on a common signal to select among equilibria — while permitting local coordination within strategic neighborhoods. Satisfied by myopic best-response dynamics.

Pairwise stability: The solution concept underlying the model. A network A satisfies pairwise stability under transferable utility if A_{ij} = 1{V_{ij} > 0}, meaning a link forms exactly when the joint surplus is positive. This is the equilibrium condition from which the strategic interaction statistics S_{ij} and non-robustness indicators D_{ij} are derived.

Network HAC estimator: The variance estimator hat_Σ_n = (1/n) Σ_i Σ_j k(d_{ij}/b_n) hat_ψ_i hat_ψ_j^T, where d_{ij} is the path distance in the observed network, k(·) is a kernel, and b_n is a bandwidth. It is the network analog of heteroskedasticity- and autocorrelation-consistent (HAC) estimators in time series, using path distance in place of temporal lag distance.

Homophily (in this paper’s sense): The property that the joint-surplus function V is decreasing in the first argument r_n^{-1}‖X_i − X_j‖ (scaled positional distance), so nodes that are more dissimilar in position are strictly less likely to form links. Combined with the sparsity scaling r_n = (κ/n)^{1/d}, this ensures that links decay with distance in social space and that the network remains sparse as n grows.

On the Optimal Design of a Financial Stability Fund

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

This paper asks how to optimally design a Financial Stability Fund (Fund) for a union of sovereign countries that must simultaneously (i) prevent sovereign default, (ii) provide risk-sharing and consumption smoothing, (iii) respect countries’ sovereignty (limited enforcement on both sides), (iv) address moral hazard from governments’ non-contractable policy reform effort, and (v) never impose permanent transfers or incur undesired expected losses. The paper develops the formal theory of such a Fund and evaluates it quantitatively against an incomplete-markets economy with sovereign default (IMD), calibrated to euro area “stressed countries” (Greece, Italy, Portugal, Spain — the GIPS).

Model Setup and Methodology

The Fund is modeled as a long-term contract between a risk-neutral lender (the Fund) and a risk-averse, relatively impatient borrower (a small open-economy sovereign). The government maximizes lifetime utility over consumption, leisure, and effort, where effort is private information (non-contractable) and determines the distribution of future endogenous government expenditure shocks. Two-sided limited enforcement (LE) constraints govern the contract: the borrower’s constraint ensures the country never prefers autarky-with-default to staying in the Fund; the lender’s constraint ensures the Fund never prefers investing at the risk-free rate to continuing the contract. The lender’s constraint is set with Z = 0 in the benchmark, meaning the Fund never accepts any expected permanent transfers — no ex-ante or ex-post redistribution.

Because LE and moral hazard (MH) constraints are forward-looking, standard dynamic programming cannot be applied directly. The paper uses recursive contracts (a Saddle-Point Functional Equation, SPFE) with a discounted relative Pareto weight x as the co-state variable. The SPFE characterizes the constrained-efficient allocation. The paper then proves two welfare theorems, providing a novel decentralization of the Fund contract as a recursive competitive equilibrium (RCE) with state-contingent long-term bonds, Pigouvian taxes on Arrow securities (budget-neutral in equilibrium), and endogenous borrowing limits.

The benchmark (IMD) economy features long-term non-contingent defaultable debt modeled following Chatterjee–Eyigungor, with asymmetric default penalties and probabilistic market re-entry after default (λ = 0.264). Both economies are calibrated to GIPS data for 1980–2015 using a panel Markov regime-switching AR(1) productivity process with three regimes (crisis, intermediate, normal). Key parameters: β = 0.929, r = 2.48%, δ = 0.814, κ = 0.083, labor share α = 0.566.

Main Findings with Quantitative Magnitudes

Borrowing capacity: The Fund supports a long-run average debt-to-GDP ratio of 191 percent, compared with 78.6 percent in the IMD economy — more than double — while eliminating default episodes entirely. At the state-level, the maximum debt capacity of the Fund ranges from roughly 99–293 percent of GDP across states, versus 1.6–184 percent in the IMD economy; capacity in bad states (low θ, high g) under the IMD falls to under 2 percent, while the Fund can absorb close to 100 percent even in the worst state.
Consumption volatility: The relative volatility of consumption to output falls from 139 percent in the IMD economy to 36 percent under the Fund, reflecting greatly improved risk sharing through state-contingent payments.
Primary surplus co-movement: The cyclical correlation of the primary surplus with output rises from 0.23 (mildly procyclical — consistent with some consumption smoothing but limited by borrowing constraints and default risk) in the IMD to 0.94 under the Fund, enabling counter-cyclical primary deficits during crises.
Effort: The long-run mean effort is 17 percent higher under the Fund than in the IMD economy in normal times, reflecting the Fund’s long-horizon incentive structure. However, during a crisis, effort is lower under the Fund than under the IMD — the Fund deems high effort in a crisis not part of the efficient allocation, in contrast to the IMD where spreads and borrowing constraints impose austerity-like discipline.
Welfare gains: Starting from zero initial debt, the consumption-equivalent steady-state average welfare gain of the Fund is approximately 8.5 percent (ergodic mean-weighted), ranging from 7.0 percent in the best state (high θ, low g) to 10.3 percent in the worst state (low θ, high g). In a counterfactual crisis simulation initialized at pre-crisis GIPS levels (70 percent debt-to-GDP, 0.8 percent spread), the welfare gain rises to approximately 10.59 percent in consumption-equivalent terms, exceeding the zero-debt benchmark of 8.57 percent for the same shock state.
Welfare decomposition: For the two worst-shock states examined, higher debt capacity (channel iii) and state-contingent insurance (channel iv) together account for more than 90 percent of total welfare gains — specifically, 63.65 percent and 28.10 percent for (θl, gh), and 51.92 percent and 41.39 percent for (θl, gl), respectively. The direct costs of default (output penalty and market exclusion) together contribute less than 10 percent of total gains.
Spreads: The IMD economy generates positive spreads reflecting default risk. The Fund economy generates only non-positive spreads in equilibrium — negative spreads arise when the lender’s limited enforcement constraint is binding (i.e., when continuing to lend risks permanent Fund losses, so the Fund restrains the borrower). This negative spread is interpretable as a Debt Sustainability Analysis signal.

Scope Conditions

Calibration is to GIPS countries over 1980–2015. The Fund assumes full exclusivity (absorbs all sovereign debt). A follow-up paper by other authors shows similar welfare gains hold when only a minimal fraction of debt is absorbed. The benchmark sets Z = 0 (no solidarity transfers); relaxing Z < 0 would allow greater risk sharing. The borrower is strictly more impatient than the lender (η = β(1+r) = 0.9684 < 1).

In depth

Q1. What are the two limited enforcement (LE) constraints in the Fund contract, and what do they individually prevent?

A: The borrower’s LE constraint (constraint 1) ensures the country’s continuation value under the Fund always weakly exceeds its outside option V°(s) — the value of defaulting and entering incomplete markets as a defaulter. This prevents the borrower from reneging on the Fund contract. The lender’s LE constraint (constraint 3) ensures the Fund’s expected net present value of transfers never falls below Z (set to 0 in the benchmark), preventing the Fund from making permanent expected losses. Together, these two constraints define an interval [x(s), x̄(s)] for the relative Pareto weight within which both parties remain voluntarily in the contract.

Q2. How does moral hazard enter the model, and what is the key assumption enabling the first-order-condition (FOC) approach?

A: Government effort e ∈ [0,1] is non-contractable; it shifts the distribution of future government expenditure shocks g in a first-order stochastically dominant direction (higher effort → lower expected g). The incentive compatibility constraint (ICC, constraint 2) imposes that the marginal cost of effort v′(e) equals the marginal benefit in terms of expected future utility changes. The FOC approach is validated by Assumption 1 (monotone likelihood ratio condition on the g-shock transition, and convexity of the CDF with respect to effort), which guarantees the ICC is sufficient as well as necessary. Without this assumption, the full optimization problem would need to replace the ICC, making the recursive formulation substantially more complex.

Q3. How does the paper achieve a recursive formulation despite forward-looking LE and MH constraints?

A: The paper uses the saddle-point Lagrangian approach (following Marcet–Marimon). Rather than tracking the full history of constraints, it introduces a discounted relative Pareto weight x ≡ [β(1+r)]^t · (µ_b,t / µ_l,t) as the sufficient co-state variable. The law of motion for x adjusts at each state realization: the borrower’s LE multiplier ν_b raises x (rewards the borrower), the lender’s LE multiplier ν_l lowers x (restrains the borrower), and the MH multiplier ρ̺ shifts x up or down depending on whether the realized g provides a positive or negative signal about effort (monotone likelihood ratio). This collapses the problem to a stationary Saddle-Point Functional Equation (SPFE) in (x, s).

Q4. What are the key properties of the optimal Fund allocation characterized in the paper?

A: (i) When neither LE constraint binds, consumption increases with x and is constant in s (perfect Pareto weight-determined risk sharing), labor supply is undistorted and increases in θ, and x declines over time due to borrower impatience (η < 1). (ii) When the borrower’s LE binds (x ≤ x̄(s)), consumption, labor, and x are pinned at x̄(s) and the borrower is prevented from receiving less. (iii) When the lender’s LE binds (x ≥ x̄(s)), the same constancy holds and the lender is prevented from being overexposed. Moral hazard introduces state-contingency in the inter-period evolution of x even when neither LE binds, via the likelihood ratio term. The paper shows that immiseration (consumption converging to zero) is prevented by the borrower’s LE constraint, even in the presence of moral hazard.

Q5. What is the modified inverse Euler equation in this model, and how does it differ from standard formulations?

A: In the standard pure moral hazard problem, the inverse of the marginal utility process is a positive supermartingale, leading to immiseration (consumption converging to zero) when the borrower is impatient. In this model with two-sided LE and MH, the inverse Euler equation (Lemma 4, equation 21) has the form: E_s[{1/u′(c(x′,s′))} · {(1+ν_l)/(1+ν_b)}] = η · {1/u′(c(x,s))}. The LE multipliers truncate the supermartingale whenever borrower or lender constraints bind, recurrently preventing both immiseration and permanent lender losses. The MH constraint introduces state-contingent perturbations to the path of consumption (via likelihood ratios) even between binding episodes.

Q6. What is the novel decentralization result, and why is it theoretically significant?

A: The paper provides two welfare theorems (Propositions 1 and 2). The Second Welfare Theorem shows that any constrained-efficient Fund contract can be decentralized as a recursive competitive equilibrium with: (a) long-term state-contingent (Arrow security) assets, (b) Pigouvian state-contingent taxes τ^a(s′) on Arrow securities — which are budget-neutral in equilibrium — where 1/(1+τ^a(s′)) = 1 + χ(x,s)·u′(c(x,s))·[∂_e π(s′|s,e)/π(s′|s,e)], and (c) endogenous borrowing limits “not too tight” relative to outside options. The First Welfare Theorem shows the reverse. This decentralization is novel because it handles both limited commitment and dynamic moral hazard simultaneously — prior work handled each in isolation. The taxes internalize the full social value of effort by creating a wedge between the borrower’s and lender’s intertemporal rates of substitution, removing the need to impose the ICC directly as a constraint in the competitive equilibrium.

Q7. What drives the negative spreads in the Fund economy, and how do they differ from the positive spreads in the IMD economy?

A: In the IMD economy, positive spreads reflect the probability of default: the bond price embeds an expected default discount. In the Fund economy, default is eliminated by construction. Negative spreads arise when the lender’s LE constraint is binding in some future state s′ (i.e., ν_l(x′,s′) > 0): this means the borrower’s Pareto weight is so high that the Fund risks permanent losses by continuing to lend. The asset price equation (45) shows the Arrow security price equals the maximum of the borrower’s discounted marginal utility valuation and the risk-free discounted return — so when the lender’s constraint binds, the price is driven by the risk-free return (q(s′|s) = π(s′|s,e)·A(s′)/(1+r)), which generates a negative implicit spread. The negative spread acts as a DSA-like signal: the Fund is better off restraining lending in those states.

Q8. How does the calibration match the GIPS data, and what is the main misfit?

A: The IMD economy is calibrated to average GIPS moments over 1980–2015 using a panel Markov regime-switching AR(1) for productivity (three regimes: crisis, intermediate, normal) and a three-state government expenditure process. The model matches well: average debt/GDP of 78.57 percent (data: 78.33), average spread of 4.17 percent (data: 4.15), labor moments, relative volatility of spreads (1.74 vs. 1.67 in data), government-output correlation (0.38 matches data), and relative volatility of the primary surplus (0.97 vs. 1.00 in data). The main misfit is the average primary surplus/GDP: the model generates a positive value (consistent with stationarity and debt servicing), while the data shows a slight deficit over the sample, plausibly reflecting growth expectations. The paper notes this level misfit does not compromise its core welfare-comparison results, since what matters is the relative time-series behavior.

Q9. How does the Fund compare to the IMD economy in the crisis simulation initialized at pre-2008 GIPS conditions?

A: The economy is initialized at 70 percent debt-to-GDP and 0.8 percent spread (consistent with 2005–2007 GIPS averages), then hit with a negative productivity and high government expenditure shock. In the IMD economy, this shock generates a wave of defaults (Figure 6), sharp spread increases (spreads spike, consistent with GIPS experience of 2009–2010 where spreads reached 4.04 percent on average), and a required increase in labor supply despite low productivity. Under the Fund, no defaults occur: instead, the country runs a large primary deficit financed by the state-contingent component of the Fund contract (debt actually falls under the Fund while rising in the IMD), consumption is higher than in the IMD for approximately the first 10 periods of the crisis, and labor supply is allowed to fall (consistent with efficiency). The welfare gain in this counterfactual is approximately 10.59 percent in consumption-equivalent terms, exceeding the zero-debt-initial-condition gain of 8.57 percent for the same shock state, demonstrating that welfare gains are amplified when the Fund takes over pre-existing debt.

Q10. How does the Fund affect effort incentives differently in normal times versus crisis times?

A: In normal times, the Fund provides better incentives for effort: long-run average effort is 17 percent higher under the Fund than in the IMD economy. The Fund’s long-term contract links future government expenditure outcomes directly to future lifetime utility via the law of motion for x (equation 5): low g realizations shift x upward (reward the borrower), creating forward-looking incentives. In crisis times, the Fund allows effort to fall relative to the IMD economy; the IMD imposes higher effort in bad states through spread increases and effective borrowing constraints that make budget relief through effort more valuable. The paper interprets this as the efficient outcome: “austerity” (high effort during a crisis) is not part of the constrained-efficient Fund allocation.

Q11. What is the welfare decomposition methodology, and what does it reveal about channels of welfare gain?

A: The authors construct a sequence of counterfactual IMD economies. Channel (i) removes the output penalty upon default, isolating its welfare cost: contributes 6.58 percent (θl, gh) and 5.31 percent (θl, gl) of total gain. Channel (ii) additionally removes market exclusion after default (immediate return): contributes 1.67 percent and 1.38 percent respectively. Channel (iii) solves counterfactual economies with the Fund’s state-specific endogenous borrowing limits but no default allowed, quantifying the value of greater debt capacity: contributes 63.65 percent and 51.92 percent. Channel (iv) is the residual attributable to state-contingent insurance payments: contributes 28.10 percent and 41.39 percent. The decomposition reveals that in the worst state (θl, gh), debt capacity dominates (63.65 percent), while in (θl, gl) — where the low government expenditure partially offsets low productivity — state-contingent insurance is relatively more important (41.39 percent). Together, channels (iii) and (iv) exceed 90 percent of total gains in both cases examined.

Q12. Why is the Fund’s decentralization unlikely to emerge from private international capital markets?

A: Two reasons are given. First, private international lenders typically lack the legal authority to impose state-contingent taxes (τ^a(s′)) on domestic economies; these taxes are a necessary component of the decentralization to internalize the social value of effort. Second, even if such taxes were optimal from the joint perspective of borrower and lender, the borrower has no unilateral incentive to impose them given market conditions — the taxes are only individually rational within the Fund’s constrained-efficient contract. This provides a rationale for an institutional implementation of the Fund rather than reliance on decentralized sovereign debt markets.

Key Concepts

Financial Stability Fund (Fund): A long-term partnership contract between a risk-neutral lender (the Fund) and a risk-averse sovereign borrower, designed to provide risk-sharing and consumption smoothing through state-contingent transfers subject to two-sided limited enforcement and moral hazard constraints, without ever incurring expected permanent losses. Distinguished from standard lending by its long-term contingent structure and dual role as risk-sharing mechanism and crisis-resolution tool.

Two-sided limited enforcement (LE) constraints: Forward-looking constraints in the Fund contract that prevent either party from reneging. The borrower’s LE constraint ensures the contract always delivers at least as much lifetime utility as defaulting and entering incomplete debt markets. The lender’s LE constraint (with Z = 0 in the benchmark) ensures the Fund never accumulates a negative expected net present value from its contractual obligations — i.e., no permanent transfers occur. Both constraints are binding recurrently in the long-run ergodic set.

Moral hazard (MH) / incentive compatibility constraint (ICC): The constraint arising from the fact that government policy reform effort e is non-contractable (sovereign right). The ICC requires that the marginal cost of effort v′(e) equals the marginal lifetime benefit, which depends on the likelihood ratio of future shocks with respect to effort. The Fund contract provides long-horizon performance-based rewards and punishments (via the law of motion of the relative Pareto weight x) to induce efficient effort, without imposing ex-ante austerity conditions.

Discounted relative Pareto weight (x): The key co-state variable in the recursive formulation, defined as x_t = [β(1+r)]^t · (µ_b,t / µ_l,t), where µ_b and µ_l are the time-varying Pareto weights of borrower and lender. It captures the entire history of binding constraints and serves as the state variable summarizing the borrower’s “entitlement” in the contract. Declines over time due to borrower impatience (η = β(1+r) < 1), but is upward-adjusted when the borrower’s LE constraint binds, and shifts state-contingently due to MH likelihood ratios.

Saddle-Point Functional Equation (SPFE): The recursive formulation of the Fund contracting problem (equation 6), analogous to Bellman’s equation but for saddle-point (min-max) problems. Required because standard dynamic programming fails when constraints are forward-looking; solved by the Marcet–Marimon recursive contract approach. The SPFE characterizes the constrained-efficient Fund allocation as a function of the co-state x and exogenous state s.

Incomplete markets with default (IMD) economy: The benchmark comparison economy in which the sovereign borrows via non-contingent long-term defaultable bonds (parameterized by maturity δ and coupon κ), with asymmetric output penalties upon default and probabilistic market re-entry. Calibrated to GIPS countries 1980–2015. Generates positive spreads that reflect default risk; serves as both the status quo and the source of the borrower’s outside option V°(s) in the Fund contract.

Pigouvian Arrow security taxes: State-contingent taxes τ^a(s′) on Arrow security holdings, defined by 1/(1+τ^a(s′)) = 1 + χ(x,s)·u′(c)·[∂_e π/π], introduced in the decentralization of the Fund contract. These taxes create a wedge between the borrower’s and lender’s intertemporal rates of substitution to internalize the full social value of non-contractable effort. Budget-neutral in equilibrium: the government’s lump-sum transfer τ(s) exactly offsets expected tax revenue.

Debt Sustainability Analysis (DSA) interpretation: The paper interprets the lender’s LE constraint (Z = 0) as a Fund-level DSA: it sets the boundary beyond which the contract would embed permanent transfers. A negative spread in the Fund economy signals that the lender’s LE constraint is binding in some future state — a DSA warning that the Fund is better off investing at the risk-free rate rather than extending more credit.

Open Rule Legislative Bargaining

Mon, 01 Jan 0001 00:00:00 +0000

This paper revisits the open rule legislative bargaining model of Baron and Ferejohn (1989) — the dominant workhorse model in political economy for analyzing how legislatures divide a surplus — and provides a more complete characterization of its stationary equilibria. The core research question is whether the equilibrium typically cited in the literature as the “open rule equilibrium” is actually the unique equilibrium, or whether it rests on implicit and unstated assumptions that, once relaxed, reveal a much richer equilibrium set.

The model features n=3 negotiators dividing a surplus normalized to one, operating under simple majority rule (2 of 3 votes required). The common discount factor is Delta in (0,1). In each period, a proposer is selected uniformly at random; under the open rule, an amender is then selected uniformly at random from the two non-proposers and may either accept or counter-propose. Sincere voting determines the outcome. The authors analyze stationary subgame perfect equilibria (SSPE), in which strategies depend only on current role, not history.

The existing literature implicitly adopted what the authors call the “standard assumption”: when given the opportunity to amend, the amender proposes the same allocation she would propose as a proposer in a closed rule game. Under this assumption, the unique SSPE has the proposer receiving share 1-Delta and each of the other two negotiators receiving Delta/2 (in the Pareto-efficient equilibrium). The literature treated this as the definitive open rule solution.

The paper’s first main result is that this standard-assumption equilibrium is indeed a valid SSPE, but it is not the only one. The key mechanism generating multiplicity is the treatment of off-path behavior: what the amender does when the proposer deviates to a non-equilibrium proposal. With n=3, a deviating proposer can exploit the structure so that the amender becomes a “free” coalition member — the proposer does not need to buy the amender’s vote separately, because the amender is already included in the majority once she counter-proposes. This expands the set of credible threats and supports a continuum of additional Pareto-undominated SSPEs.

The paper’s second main result characterizes the broader equilibrium set: all Pareto-undominated SSPEs belong to a class in which the proposer offers (1-Delta) to herself and equal shares to both other negotiators. In the non-standard equilibria, the amender always amends, generating equilibrium delay — agreements are not reached immediately, and payoffs are discounted by Delta^(t-1) for each period of delay.

The third main result is that among all Pareto-undominated SSPEs, the unique Pareto-efficient one is the standard-assumption equilibrium (no delay). All other equilibria involve delay and are therefore Pareto-inferior in expectation.

The institutional design implication reverses a widely held view: the open rule was thought to promote more egalitarian allocations relative to the closed rule. The authors show this is not the case for Pareto-efficient equilibria. The Pareto-efficient open rule equilibrium is actually a special case of the closed rule equilibrium — the proposer captures 1-Delta and offers Delta to the coalition. More broadly, open rule bargaining tends to generate longer equilibrium delays and less egalitarian surplus allocations than previously predicted by Baron and Ferejohn. Scope conditions: the formal analysis is restricted to n=3 negotiators; generalization to larger legislatures is noted as an open direction.

Q: What is the “standard assumption” and why does the existing literature rely on it?

A: The standard assumption holds that when an amender gets the opportunity to counter-propose, she proposes the same allocation she would choose if she were the proposer in a closed rule game. The existing open rule literature — including Baron and Ferejohn (1989), Jackson and Morelli (2004), Baron (2012), van Weelden (2013), and Austen-Smith and Banks (1999) — accepted this assumption implicitly, treating the resulting equilibrium as the unique open rule equilibrium. The assumption sidesteps the question of off-path behavior: what happens when the proposer deviates to a non-equilibrium proposal that the amender would want to amend. Because deviations are resolved within the same bargaining session under the open rule, off-path specifications are consequential.

Q: What is the unique SSPE under the standard assumption, and what are its payoff implications?

A: Under the standard assumption with n=3 and discount factor Delta, the unique SSPE has the proposer receiving a share of 1-Delta of the surplus and each of the other two negotiators receiving Delta/2. There is no delay: the proposal passes immediately in the period it is made. This equilibrium is Pareto-efficient relative to all other stationary equilibria identified in the paper.

Q: What is the mechanism by which the equilibrium set is larger than the standard assumption predicts?

A: With n=3, when a proposer deviates to a non-equilibrium proposal, the amender — who responds by counter-proposing — automatically becomes part of the passing coalition without the proposer needing to separately compensate her. This makes the amender a “free” coalition member in the deviation subgame, which changes the cost structure of deviations and expands the range of proposals the proposer can credibly make. Consequently, a wider set of strategies by the amender can be sustained as equilibrium responses, yielding a continuum of additional Pareto-undominated SSPEs beyond the standard-assumption equilibrium.

Q: What do the non-standard equilibria look like in terms of proposals, delay, and payoffs?

A: In the non-standard Pareto-undominated SSPEs, the proposer offers (1-Delta) to herself and equal shares (Delta/2 each) to the other two negotiators — note the proposer’s own share is the same as in the standard equilibrium, but the off-path behavior differs — and the amender always chooses to amend rather than accept. The amendment triggers a vote in which the amendment fails (or the process repeats), pushing resolution to the next period. This generates equilibrium delay: agreements take multiple periods to reach, and all payoffs are discounted by Delta^(t-1) per period of delay, making these equilibria Pareto-inferior to the no-delay equilibrium.

Q: Which equilibrium is Pareto-efficient among all Pareto-undominated SSPEs, and why?

A: The unique Pareto-efficient SSPE is the standard-assumption equilibrium, because it is the only one that involves no delay. All other Pareto-undominated SSPEs involve at least one period of delay, which destroys surplus through discounting (payoffs shrink by a factor of Delta per period). Since delay is costly for all negotiators and generates no compensating redistribution, any equilibrium with delay is Pareto-dominated by the no-delay equilibrium.

Q: What are the implications for the classic efficiency comparison between open and closed rules?

A: The closed rule always generates an efficient outcome (no delay in SSPE). The open rule can also generate an efficient outcome — under the standard-assumption equilibrium — but uniquely admits a continuum of inefficient equilibria involving delay. Therefore the open rule is weakly dominated by the closed rule from an efficiency standpoint: at best it matches the closed rule (one efficient equilibrium), and at worst it generates costly delay. This reverses the common inference that open rule unambiguously improves outcomes.

Q: What are the implications for the classic fairness comparison between open and closed rules?

A: The open rule was commonly believed to promote more egalitarian surplus divisions relative to the closed rule, which allows the proposer to extract a large share. The paper shows this view is misleading. In the Pareto-efficient open rule equilibrium, the proposer still captures 1-Delta — the same as under the closed rule — and the result is no more egalitarian. In the delay equilibria, the proposer does offer equal shares to both other negotiators, but this comes at the cost of inefficiency (delay). There is no Pareto-undominated open rule equilibrium that is both efficient and more egalitarian than the closed rule.

Q: What is the class of “Pareto-undominated stationary strategies” and why does the paper focus on it?

A: A stationary strategy profile is Pareto-undominated if no other stationary strategy profile gives every negotiator at least as high an expected payoff with at least one strictly better off. The paper focuses on this class to provide a tractable but principled selection criterion within the large set of SSPEs: it eliminates equilibria that are dominated from every player’s perspective, retaining only those that could plausibly arise if players coordinate on mutually beneficial outcomes. The characterization of this class reveals that equilibrium multiplicity is already substantial even after imposing this selection.

Q: What is the scope of the formal results, and what is left open?

A: The formal analysis is restricted to n=3 negotiators with simple majority rule (2 of 3 votes). The authors acknowledge that generalization to larger n is an important open question. The three-legislator case is the simplest non-trivial instance of the majority-rule bargaining problem, and the authors use it to isolate the mechanism cleanly. The model assumes sincere voting, a common discount factor Delta in (0,1), and stationary strategies.

Q: How does this paper relate to Baron and Ferejohn (1989)?

A: Baron and Ferejohn (1989) originated both the closed rule and open rule bargaining frameworks and derived the standard-assumption equilibrium for the open rule. Subsequent literature (Eraslan 2002, Cho and Duggan 2003, 2009, Banks and Duggan 2000) extended various aspects of the B&F framework. The present paper takes the B&F open rule model as given but demonstrates that B&F’s open rule analysis was incomplete: it did not systematically address off-path behavior, and as a result the equilibrium it identified is not unique. The paper’s main contribution is to show that the B&F open rule predictions — more egalitarian allocations and prompt agreement — do not hold generally across the full equilibrium set.

Open Rule: A bargaining protocol in which, after an initial proposal is made, a nominated amender may make a counter-proposal before a vote is taken; contrasted with the closed rule, under which the initial proposal is voted on without amendment.

Closed Rule: A bargaining protocol in which a vote is taken directly on the first proposal, with no opportunity for amendment.

Standard Assumption: The implicit assumption, used by Baron and Ferejohn (1989) and subsequent literature, that when the amender counter-proposes under the open rule, she proposes the same allocation she would choose as a proposer in a closed rule game; the paper shows this assumption is consequential for equilibrium uniqueness.

Stationary Subgame Perfect Equilibrium (SSPE): An equilibrium concept in which each player’s strategy depends only on her current role (proposer, amender, or voter) and not on the history of play; the paper characterizes SSPEs of the open rule model.

Pareto-Undominated Stationary Strategy Profile: A stationary strategy profile for which no other stationary strategy profile gives every negotiator weakly higher expected payoff with at least one strictly higher; used as a selection criterion to prune the large equilibrium set.

Equilibrium Delay: The phenomenon in which agreement is not reached in the current period because the amender always counter-proposes and the counter-proposal also fails, pushing resolution to a future period and discounting payoffs; all non-standard-assumption Pareto-undominated SSPEs involve delay.

Off-Path Behavior: The specification of what strategies players use following a deviation from equilibrium play; the paper shows that different specifications of off-path behavior by the amender support different equilibria, and that the existing literature was not systematic about this.

Optimal Decision Rules When Payoffs are Partially Identified

Mon, 01 Jan 0001 00:00:00 +0000

This paper derives asymptotically optimal statistical decision rules for discrete choice problems when the payoffs associated with some choices are only partially identified. The research question is: how should a decision maker who can bound but not point-identify a payoff-relevant parameter θ use data to make optimal policy choices?

The framework separates two parameter types. The reduced-form parameter µ is point-identified and can be estimated from data. The structural parameter θ — such as the average treatment effect (ATE) in a target population — is set-identified, meaning only that θ ∈ Θ0(µ) can be established, where the identified set is indexed by µ. The decision maker confronts both ambiguity (arising from partial identification of θ given µ) and statistical uncertainty (µ must be estimated).

The authors propose a hybrid optimality criterion that applies minimax reasoning to the partially-identified parameter θ — choosing actions that minimize maximum risk over Θ0(µ) — while applying average (integrated) risk minimization over µ, reflecting the asymmetric nature of the two identification problems. This asymmetric treatment follows the generalized Bayes-minimax principle of Hurwicz (1951).

The optimal decision rule is implemented by computing, for each action, the maximum risk (or regret) over θ ∈ Θ0(µ) conditional on µ, then averaging this maximum risk across either (i) a bootstrap distribution for an efficient estimator µ̂, (ii) a posterior distribution for µ in parametric models, or (iii) a quasi-posterior based on a limited-information criterion in semiparametric models. The optimal action is whichever choice has the smallest average maximum risk.

A central theoretical result (Theorems 1 and 4) establishes formal asymptotic optimality for both parametric and semiparametric settings: Bayes and quasi-Bayes decisions with any prior whose density is positive, bounded, and continuous are asymptotically equivalent and optimal. Critically, the optimality of these rules is asymptotically independent of the choice of prior for µ. The authors also establish a necessity result (Theorems 2 and 5): any decision rule not asymptotically equivalent to the Bayes or bootstrap rule is strictly sub-optimal.

A key finding is that “plug-in” rules — which substitute an efficient point estimate µ̂ directly into the oracle decision rule — can be sub-optimal. This failure occurs generically under partial identification because the maximum risk function R(d,µ) is typically only directionally differentiable (not fully differentiable) in µ, owing to max and min operators in intersection bounds, linear program value functions, or other bound constructions. When full differentiability holds, Corollary 1 confirms plug-in rules are optimal; otherwise they are not. The empirical illustration demonstrates the practical consequence: for German male youths deciding whether to adopt a job-training program based on 14 RCT studies from Card, Kluve, and Weber (2017), the optimal rule recommends treatment (average quasi-posterior robust welfare contrast b̄n > 0) while the plug-in rule recommends against treatment (plug-in value b(µ̂) < 0). The lower bound maximum of µ̂k − C‖x0 − xk‖ is −0.3190 for the leading US study and −0.3298 for the second-best Brazilian study; because these two values are close relative to the average standard error of 0.034 across studies, the lower bound distribution is right-skewed (behaving like the maximum of two Gaussians), pushing b̄n positive even though b(µ̂) is negative.

The paper extends optimality theory to semiparametric models via a least favorable parametric submodel, introduces the concept of σ-optimality for cases where the average maximum risk criterion is infinite (relevant when the dimension K of µ exceeds 1), and provides detailed implementation guides for treatment assignment under intersection bounds, IV-like estimands, and non-separable panel data, as well as for optimal pricing decisions where revealed-preference demand theory bounds counterfactual demand responses via linear programming.

Scope conditions: optimality results apply to discrete action spaces, require efficient estimation of µ, require the identified set Θ0(µ) to be known as a set-valued mapping, and assume no “first-order ties” (the oracle decision is unique at µ0). The asymptotic framework is local, mimicking the finite-sample problem where µ is not known with certainty.

Q: What is the core decision problem this paper addresses?

A: A decision maker must choose from a finite set of actions D = {0, 1, …, D}. Payoffs depend on a structural parameter θ that is only set-identified — the data can establish θ ∈ Θ0(µ) but not pin down θ exactly. The reduced-form parameter µ is point-identified and estimated from data. The decision maker faces both ambiguity (which θ in Θ0(µ) is true?) and sampling uncertainty (what is µ?). The paper asks how to construct decision rules that are optimal in large samples under this dual uncertainty.

Q: What is the proposed optimality criterion, and why is it asymmetric across parameters?

A: The criterion applies minimax reasoning to the partially-identified θ — the maximum risk over Θ0(µ) given µ is the relevant loss — and integrates this maximum risk over µ using Lebesgue measure on local perturbations h = √n(µ − µ0) of a fixed µ0. The asymmetry reflects the fact that θ is not updated by the data (the prior for θ is not identified), while µ can be learned efficiently from the data. Full minimax over both (θ, µ) is rarely tractable even for simple binary treatment problems; the asymmetric approach yields tractable optimal rules for a broad empirically relevant class of settings.

Q: What are the Bayes, bootstrap, and quasi-Bayes implementations of the optimal rule?

A: In all three cases, the decision maker computes R̄n(d) — the average maximum risk for action d — and chooses the action that minimizes it. The Bayes rule averages R(d, µ) over the posterior πn(µ|Xn) for µ using Bayes’ theorem with a prior π on M. The bootstrap rule averages R(d, µ̂*) over bootstrap redraws µ̂* of the efficient estimator µ̂. The quasi-Bayes rule (for semiparametric models) uses a limited-information quasi-posterior N(µ̂, (nÎ)−1) combining a Gaussian quasi-likelihood with a prior for µ. All three implementations are asymptotically equivalent and optimal under the regularity conditions of Theorems 1 and 4.

Q: What do Theorems 1 and 2 (and their semiparametric analogues Theorems 4 and 5) establish?

A: Theorem 1 establishes sufficiency: Bayes decisions with any prior in the class Π are asymptotically equivalent to each other and are optimal; any rule asymptotically equivalent to such a Bayes decision is also optimal. Theorem 2 establishes necessity: any rule in the admissible class D that is not asymptotically equivalent to the Bayes rule has strictly higher average excess risk at any µ0 where asymptotic equivalence fails. Together, these theorems fully characterize the class of asymptotically optimal rules and show that the Bayes/bootstrap class is not merely sufficient but also necessary for optimality.

Q: When are plug-in rules sub-optimal, and when are they optimal?

A: Plug-in rules substitute an efficient point estimate µ̂ directly into the oracle decision δo(µ̂). If R(d, µ) is fully differentiable at µ0 for all oracle-optimal actions d, then the directional derivative is linear and plug-in and Bayes rules are asymptotically equivalent; Corollary 1 confirms plug-in rules are then optimal. However, under partial identification, max and min operators in bound constructions — intersection bounds, linear program value functions, revealed-preference bounds — generically induce only directional (non-linear) differentiability of R(d, µ). In these cases asymptotic equivalence can fail, and Theorem 2 implies plug-in rules are sub-optimal. Manski (2021, 2023) documents poor finite-sample performance of plug-in rules numerically; the authors’ necessity result provides a general theoretical explanation under the asymptotic average risk criterion.

Q: How does the treatment assignment empirical illustration demonstrate the difference between optimal and plug-in rules?

A: Using data from Ishihara and Kitagawa (2021) with K = 14 RCT studies from Card, Kluve, and Weber (2017) and Lipschitz constant C = 0.25, the decision is whether to adopt a job-training program for German male youths or female youths in 2010 (GDP growth 3.48%, unemployment 9.45%). For male youths, the largest lower bound value µ̂k − C‖x0 − xk‖ is −0.3190 (US study) and the second-largest is −0.3298 (Brazilian study), separated by only 0.0108 against an average standard error of 0.034 across studies, so the lower bound distribution is right-skewed (maximum of two near-tied Gaussians). This right-skew pushes the quasi-posterior mean b̄n positive, yielding a treatment recommendation, while the plug-in value b(µ̂) is negative, yielding a non-treatment recommendation — a concrete reversal of the policy decision. For female youths, the minima and maxima are better separated, the distribution is near-Gaussian, and b̄n ≈ b(µ̂), so both rules agree on treatment.

Q: What are intersection bounds and why do they generate directional differentiability?

A: Intersection bounds arise when the ATE is bounded in K separate observational studies by lower bounds bL,k(µk) and upper bounds bU,k(µk). The combined identified set uses bL(µ) = max_{1≤k≤K} bL,k(µk) and bU(µ) = min_{1≤k≤K} bU,k(µk). Even if each component bound is smooth in µk, the max and min operators make bL and bU only directionally differentiable (not fully differentiable) in µ. The directional derivative is positively homogeneous of degree one but non-linear, which is the property that drives the wedge between Bayes and plug-in rules.

Q: How does the paper extend to semiparametric models, and what technical tool does it use?

A: In semiparametric models, the data distribution depends on both µ ∈ R^K and an infinite-dimensional nuisance parameter η. Integrating over local perturbations of η as well as µ raises measure-theoretic problems in infinite-dimensional spaces. The authors instead restrict attention to local perturbations of µ0 within a least favorable parametric submodel, which is the direction that makes the problem hardest. The quasi-posterior N(µ̂, (nÎ)−1) is then used as the averaging distribution, combining a Gaussian quasi-likelihood with a prior for µ. Theorem 4 establishes optimality and Theorem 5 establishes necessity under these semiparametric conditions, mirroring the parametric Theorems 1 and 2.

Q: What is σ-optimality and why is it needed?

A: When the dimension K of µ exceeds 1, the integrated average excess risk criterion R({δn}; µ0) — which integrates over Lebesgue measure on R^K — may be infinite for all decision sequences in D, making the criterion uninformative. σ-optimality approximates the improper Lebesgue prior on h by a sequence of proper priors indexed by σ, and requires that the decision rule minimize the resulting criterion for all σ. Theorem 3 shows that the limiting behavior of σ-optimal rules coincides with that of the Bayes rule δ*n(·; π), preserving the practical implementation.

Q: How is the optimal pricing application structured and what role do revealed-preference bounds play?

A: A monopolist observes repeated cross-sections of individual demands across B budget sets and must choose a price vector from D = O ∪ C, where O contains observed prices and C contains counterfactual prices. For observed prices, average demand is identified; for counterfactual prices, only bounds are available. Following Kitamura and Stoye (2019), the space of goods is partitioned into GARP-compatible regions, and sharp bounds on counterfactual demand are computed by solving linear programs over the mass allocated to each region subject to GARP consistency constraints. The reduced-form parameter µ collects empirical choice probabilities across observed budget-region cells, estimated consistently by sample frequencies. The optimal pricing decision averages the linear-program bound solutions across quasi-posterior draws of µ.

Q: How does this approach relate to minimax and conditional Γ-minimax approaches?

A: Full minimax over (θ, µ) requires strong distributional assumptions and tractable finite-sample distributions; the authors note that no minimax treatment rule exists even for binary treatment with binary outcomes and estimated bounds. Conditional Γ-minimax (DasGupta and Studden, 1989; Giacomini, Kitagawa, and Read, 2021) fixes a prior for µ and takes minimax over the set of priors for θ conditional on µ; this is closely related to the authors’ approach but can be conservative when the marginal prior for µ varies. The authors’ framework fixes the marginal prior for µ and takes minimax over θ ∈ Θ0(µ) conditional on µ, which is shown to arise as the equilibrium of a two-player zero-sum game where adversarial nature chooses a prior for θ ∈ Θ0(µ) conditional on µ and the available data for µ.

Q: What is the technical contribution regarding directionally differentiable functions?

A: Hirano and Porter (2009) derived asymptotic optimality for treatment rules under fully differentiable welfare contrasts. This paper extends that theory to settings with directional (but not full) differentiability — a generic feature whenever bounds involve max/min operators or linear program values. The key technical building block is the asymptotic distribution of the quasi-posterior mean of directionally differentiable functions (Propositions 2 and 3 in Appendix C). While Kitagawa, Montiel Olea, Payne, and Velez (2020) characterized the asymptotic behavior of the posterior distribution of such functions, this paper instead characterizes the frequentist distribution of the posterior mean — a distinct and novel contribution to the literature on asymptotics for non-smooth functions (Dümbgen, 1993; Fang and Santos, 2019).

Q: What are the key scope conditions and limitations of the optimality results?

A: The action space D must be finite and discrete (continuous pricing must be approximated by a grid of whole-currency units, as noted in the introduction). The identified set mapping Θ0(·) must be known. Efficient estimation of µ is required, along with a consistent estimator of its asymptotic variance for quasi-Bayes implementation. The optimality criterion assumes “no first-order ties” — the oracle decision must be unique at µ0. The framework is asymptotic (local perturbations around a fixed µ0), and the theory is designed for settings where deriving exact finite-sample optimal rules is intractable. The results do not cover the case where θ affects the data distribution (only payoffs are partially identified, not identification of µ itself).

Partially-identified parameter (θ): A structural parameter — such as the ATE in a target population — about which the data can establish only set membership θ ∈ Θ0(µ), not a point value. The identified set Θ0(µ) is indexed by the point-identified reduced-form parameter µ.

Oracle decision (δo(µ)): The infeasible first-best decision that minimizes maximum risk over the identified set Θ0(µ) for a known value of µ. It serves as the benchmark against which practical rules are evaluated; any data-dependent rule can only do weakly worse.

Maximum risk (R(d, µ)): The supremum of risk r(d, θ, µ) = Eθ[l(d, Y, θ, µ)] over all θ ∈ Θ0(µ) conditional on µ. Under the regret criterion for binary treatment, R(0, µ) = (bU(µ))+ and R(1, µ) = −(bL(µ))−.

Robust welfare contrast (b(µ)): In the treatment assignment application, b(µ) = (bU(µ))+ + (bL(µ))−, whose sign determines the oracle decision: treat if b(µ) ≥ 0. The optimal rule replaces b(µ) with its quasi-posterior mean b̄n.

Directional differentiability: A function f : M → R^k is directionally differentiable at µ0 if limits of (f(µ0 + tn hn) − f(µ0))/tn exist for all sequences tn ↓ 0 and hn → h, yielding a directional derivative ḟµ0[·] that is positively homogeneous but not necessarily linear. Max/min operators and linear program value functions are generically only directionally differentiable, not fully differentiable. This property is what causes plug-in rules to fail.

Quasi-posterior: In semiparametric models, a posterior-like distribution for µ formed by combining a limited-information Gaussian quasi-likelihood N(µ̂, (nÎ)−1) with a prior π, yielding πn(µ|Xn) ∝ exp(−½(µ − µ̂)T(nÎ)(µ − µ̂))π(µ). Used in place of a full Bayesian posterior when the exact likelihood of the data-generating process is unavailable.

σ-optimality: An optimality concept that replaces the improper Lebesgue prior on local perturbations h ∈ R^K with a sequence of proper priors indexed by σ, used when the average excess risk criterion is infinite for K > 1. Theorem 3 establishes that the σ-optimal decision rule converges to the Bayes rule as σ → ∞.

Plug-in rule (δplug_n): A decision rule formed by substituting an efficient point estimate µ̂ directly into the oracle decision: δplug_n = δo(µ̂). Optimal when R(d, µ) is fully differentiable (Corollary 1), but generically sub-optimal under partial identification because directional differentiability of R(d, µ) breaks the asymptotic equivalence between the plug-in and Bayes rules.

Organizational Change and Reference-Dependent Preferences

Mon, 01 Jan 0001 00:00:00 +0000

Schmidt and von Wangenheim develop a dynamic model of organizational change in which workers have reference-dependent preferences — specifically loss aversion and social comparisons — to explain several empirically observed patterns that standard models cannot easily account for: organizational inertia in normal times, sudden productivity jumps during crises, persistent total factor productivity (TFP) differences across firms in the same industry, and effort and wage compression within firms.

The motivating empirical puzzle is the early-1980s collapse of the Great Lakes iron ore and steel industry, which had been geographically shielded from foreign competition for over 100 years. When Brazilian competitors undercut prices, the industry responded by roughly doubling labor productivity within a few years — not through new technology or capital investment, but through organizational improvements and more efficient use of existing capital (Schmitz 2007). The broader puzzle is Syverson’s (2004) finding that at the four-digit industry level, the 90th-percentile firm has TFP 1.9 times that of the 10th-percentile firm, a gap that cannot be explained by observable input differences.

The model features a principal (firm owner) bargaining with loss-averse workers (represented by a union) over organizational change — represented as a worker effort level x that adapts the firm to the state of technology θ. Workers’ reference point is a convex combination of the status quo contract and their rational expectations of the agreed contract, with weight α on the status quo. Loss aversion parameter λ > 0 means that losses relative to the reference point are weighted more heavily than gains.

The core static result (Proposition 1) is that loss aversion drives a wedge of 1 + αλ between the workers’ marginal cost and the firm’s marginal benefit of organizational change. Below a threshold θ defined by ∂v(x₀,θ)/∂x = 1 + αλ, there is complete inertia: the firm does not change the effort level at all. Above θ, the firm adjusts effort, but to x(θ) < x^ME(θ), undershooting the materially efficient level. Higher λ or higher α both widen the inertia range and reduce the amount of implemented change (Proposition 2).

A crisis — modeled as a cost shock that makes the status quo contract generate negative profits, threatening firm closure — changes workers’ outside option from their current utility U₀ to the unemployment utility of zero. Workers are now willing to accept either wage cuts or effort increases to keep their jobs. Crucially, because both concessions are perceived as losses of equal size by workers, the firm prefers to increase effort rather than cut wages, since increasing effort is more productive when x < x^ME. The model thus provides a microfoundation for downward nominal wage rigidity: in a recession, workers make concessions through harder work rather than wage cuts.

In the infinite-horizon dynamic model, workers accumulate a quasi-rent over time equal to αλ(x_{t-1} − x₀), which represents compensation paid for past effort increases. This quasi-rent is what the firm expropriates during a crisis, allowing a discontinuous jump in effort toward the materially efficient level. Firms founded at different times or hitting different idiosyncratic shocks will therefore have different effort histories and different productivity levels, generating persistent TFP differences even among firms with identical technologies. When forward-looking players anticipate the possibility of crisis, inertia in normal times actually widens further (x̃(θ) ≤ x(θ)), because firms rationally delay effort adaptation knowing it will be cheaper to implement change during a crisis.

The expectations-management extension (Section 4) introduces a moral-hazard problem with a manager who chooses the probability of successful change. Because a higher probability of change raises the workers’ expectation-based reference point and reduces their perceived adaptation cost, the firm’s optimization problem becomes convex when the cost of effort for management is sufficiently low relative to (1−α)λΔx. This delivers a bang-bang result: the principal induces either full implementation (p = 1) or no change (p = 0), never an interior probability. This formalizes the management-consulting advice that commitment and urgency are essential to organizational change.

The social-comparisons extension (Section 5) shows that when workers compare their wages and effort to colleagues, the firm optimally compresses effort differences across workers — inducing the less productive worker to work more than efficiency requires and the more productive worker to work less. If productivity differences between workers are sufficiently small, the firm sets identical effort levels. Wage compression follows from effort compression. To avoid the cost of social comparisons entirely, it may be optimal for the firm to split into separate legal entities whose workers no longer form a common reference group — a new explanation for organizational unbundling.

Q: What is the core mechanism by which loss aversion generates organizational inertia in normal times? A: Workers have a reference point that is a convex combination (weight α on status quo, weight 1−α on rational expectations) of their current contract and the expected new contract. Because workers perceive an effort increase above their reference effort as a loss, the firm must pay a wage premium of αλ per unit of additional effort on top of the material effort cost of 1. This raises the effective marginal cost of implementing change from 1 to 1 + αλ, so the firm only implements change when the marginal revenue of effort strictly exceeds 1 + αλ. Below the threshold technology level θ (defined by ∂v(x₀,θ)/∂x = 1 + αλ), there is complete inertia and the firm keeps x* = x₀.

Q: How does a crisis break the inertia? A: A crisis is a cost shock large enough to make the firm’s profits negative under the status quo contract, so the firm would close unless workers make concessions. Workers’ outside option shifts from their accumulated utility U₀ to the unemployment utility of zero. Because wage cuts and effort increases are both perceived as losses of equal magnitude, the firm prefers to demand effort increases (which raise revenue) over wage cuts (which do not). At the margin, when workers are at zero utility, the loss-aversion terms cancel from the marginal rate of substitution, and the firm can push effort up to the materially efficient level x^ME — a discontinuous jump.

Q: Why do wages not fall during a recession in this model? A: Workers perceive both wage cuts and effort increases as losses of equal per-unit utility cost. Since increasing effort by one unit and cutting wages by one unit impose the same utility cost on workers but effort increases raise firm revenue while wage cuts do not, it is always more efficient for the firm to extract concessions through higher effort rather than lower wages. The firm therefore first drives effort to x^ME before cutting wages, and cuts wages only if the zero-utility constraint still is not binding at x^ME. This provides a microfoundation for Bewley’s (1999) observation that wages do not fall during recessions.

Q: Where does the quasi-rent exploited during a crisis come from? A: Every time the firm implements an effort increase in normal times it must compensate workers with a permanent wage increase to cover both the permanent higher effort cost (x_{t}−x_{t-1}) and the one-time behavioral adaptation cost αλ(x_{t}−x_{t-1}). Because the compensation for the adaptation cost must be spread over all future periods as a permanent payment, workers accumulate a quasi-rent that by period t equals αλ(x_{t-1}−x₀) above their initial utility U₀ = w₀−x₀. This is the rent the firm expropriates in a crisis to fund the discontinuous effort increase.

Q: How does the dynamic model generate persistent TFP differences across firms in the same industry? A: Firms founded at different times start with different initial status-quo effort levels relative to the current technology θ. Because each firm’s path of organizational adaptation is history-dependent — inertia regions, timing of crises, and accumulated quasi-rents all depend on when the firm was founded and what idiosyncratic shocks it experienced — firms that start later (or hit crises earlier) can remain more productive than older firms for extended periods. The numerical example with v(x,θ) = θ ln(x), α = 0.5, λ = 1, δ implied parameters shows that a firm founded when θ = 7 at the materially efficient point can maintain a substantial productivity advantage over a firm founded when θ = 4 that has accumulated inertia, even though both firms have access to the same technology.

Q: Does rational anticipation of a future crisis increase or decrease inertia in normal times? A: It strictly increases inertia. When players assign probability µ > 0 to a crisis each period, forward-looking workers demand higher compensation for effort increases in normal times — specifically, the per-period compensation for behavioral adaptation cost rises from (1−δ)αλ to γ = (1−δ(1−µ))αλ, which is increasing in µ. Simultaneously, the firm anticipates that effort adaptation will be cheaper to achieve in a crisis and therefore delays effort increases. The result is that the inertia threshold shifts from x(θ) to x̃(θ) ≤ x(θ), a strictly wider inertia region (Proposition 6).

Q: What is the expectations-management result and what drives it? A: When a manager chooses the probability of successful change p at cost c(p) = (c/2)p², the wage the firm must pay workers is concave in p (equation 22): w = x₀ + p(1+λ)Δx − p²(1−α)λΔx + U₀. The concavity arises because a higher p raises the expectation-based component of the reference point, lowering workers’ perceived adaptation cost. When c < (1−α)λΔx, this makes the principal’s profit function convex in p, so the optimum is at a corner: the principal induces either p = 1 (full implementation) or p = 0 (no change). Even when an interior solution obtains, a decrease in α (more weight on expectations) increases p. This formalizes the practitioner prescription that organizational change requires convincing everyone that change is certain and unavoidable.

Q: What is the effort and wage compression result under social comparisons? A: When each worker compares his situation to his colleague’s, with weight β on the peer’s wage and effort in forming the reference point, the firm must pay both workers a social-comparison premium of λβ(x₂−x₁) per unit of effort difference (Lemma 5). The firm therefore optimally compresses effort differences: it induces the less productive worker to exert effort above his efficient level and the more productive worker below his efficient level, at first-order conditions ∂v₁/∂x = 1 − 2λβ and ∂v₂/∂x = 1 + 2λβ respectively. If the productivity difference is small enough (specifically if ∂v₂(x*,θ)/∂x < 1 + 2λβ at the equal-effort point), the firm sets x₁* = x₂* = x*, eliminating wage inequality entirely (Proposition 8).

Q: Why might it be optimal for a firm to split into separate entities? A: Social comparisons impose costs on the firm by requiring higher wages for both workers (each receives a premium of λβ(x₂−x₁) regardless of their relative rank) and by distorting effort levels away from their efficient values. If workers employed by legally separate firms no longer treat each other as part of their reference group — because β falls to zero across firm boundaries — the firm can eliminate these comparison costs by spinning off activities into independent entities. This provides an efficiency rationale for organizational unbundling that does not rely on asset specificity or transaction costs, addressing what the authors call the “Williamson puzzle.”

Q: What are the implications for older workers and for social insurance policy? A: Older workers have two compounding reasons to be more resistant to organizational change: shorter remaining time horizons reduce the present value of permanent wage compensation for adaptation costs, and Gächter, Johnson, and Herrmann (2022) report that loss aversion λ increases with age, income, and wealth. Both factors raise the cost of implementing change with older workers. For social insurance, generous unemployment benefits or policies preventing layoffs (such as short-time work schemes) reduce workers’ concession costs in a crisis, weakening the mechanism by which crises trigger change. The model suggests this may contribute to slower technology adoption in countries with stronger labor market protections.

Q: What empirical facts from the existing literature does the model account for? A: The model accounts for: (1) Syverson’s (2004) finding of a 90th/10th percentile TFP ratio of 1.9 in four-digit US industries; (2) the iron ore and steel case study (Schmitz 2007) in which labor productivity doubled within a few years of a competitive shock with no new technology; (3) Bloom et al.’s (2014) correlation between more intense competition and higher TFP; (4) Holmes and Schmitz’s (2010) survey finding that competitive shocks raise industry productivity mainly through survival and improvement of existing firms; (5) Bewley’s (1999) downward nominal wage rigidity; and (6) Hjort, Li, and Sarsons (2022) on multinational firms using headquarters wages as reference points for wages in low-wage locations.

Loss aversion (λ): The parameter measuring the degree to which workers weight losses relative to their reference point more heavily than gains. A meta-analysis (Brown et al. 2023) across 607 empirical estimates finds an average loss aversion parameter of 1 + λ = 1.955. In this paper, λ > 0 means workers perceive a wage cut and an effort increase as losses, raising the effective marginal cost of organizational change by a factor of 1 + αλ.

Reference point (w^r, x^r): The benchmark wage and effort level against which workers evaluate outcomes. Defined as a convex combination of the status quo contract (w₀, x₀) with weight α and the rational expectation of the agreed contract (w^e, x^e) with weight 1−α. Losses occur when the realized wage falls below w^r or the realized effort exceeds x^r.

Organizational inertia: The firm’s failure to implement materially efficient organizational change even when doing so would increase total surplus. In the model, inertia arises because the effective marginal cost of effort to the firm is 1 + αλ rather than 1, so the firm only implements change above a threshold technology level θ. The range of inertia widens with higher λ, higher α, and higher initial effort x₀.

Quasi-rent: The utility accumulated by workers above their initial utility U₀ = w₀−x₀ as compensation for past effort increases. By period t it equals αλ(x_{t-1}−x₀). This quasi-rent is the source of concessions the firm can extract in a crisis: workers accept higher effort (or lower wages) in exchange for keeping their jobs rather than losing this accumulated utility through unemployment.

Behaviorally efficient effort x(θ): The effort level that maximizes joint surplus taking behavioral adaptation costs into account, defined by ∂v(x,θ)/∂x = 1 + (1−δ)αλ in the dynamic model. This is strictly below the materially efficient effort x^ME(θ) (defined by ∂v/∂x = 1) and strictly above the firm’s privately optimal effort in normal times.

Effort compression: The result under social comparisons that the principal optimally reduces the effort difference between workers relative to the efficient allocation — inducing the less productive worker to work more and the more productive worker to work less than efficiency requires. Driven by social-comparison costs λβ(x₂−x₁) that both workers receive as premiums regardless of relative rank.

Expectations management: The strategic use of commitment to high probability of change in order to shift workers’ expectation-based reference point and reduce the perceived adaptation cost. When α is small (rational expectations dominate the reference point), making change more certain lowers the wage cost of implementation, creating a complementarity between commitment and cost reduction that produces the bang-bang result: implement with certainty or not at all.

Patent Term, Innovation, and the Role of Technology Disclosure Externalities

Mon, 01 Jan 0001 00:00:00 +0000

This paper examines how anticipated changes in patent term affect R&D and innovation, using the U.S. ratification of the Trade-Related Aspects of Intellectual Property Rights (TRIPs) agreement in 1995 as a quasi-natural experiment. The central research question is whether and how policy anticipation shapes the short- and long-run dynamics of innovative activity, given ambiguous theoretical predictions: news of a patent term reduction could either deter innovation (by signaling lower future returns) or accelerate it (by inducing innovators to file under the more favorable existing regime before it expires).

The identification strategy exploits a difference-in-differences (DiD) design using two sources of variation across 621 4-digit International Patent Classification (IPC) technological fields. The first is cross-sectional variation in field-specific pending periods — the time between patent application and grant during which monopoly rights are not fully enforceable — which determines whether TRIPs increased or reduced each field’s effective patent term (from 17 years post-grant to 20 years post-application minus the pending period). Fields with average pending periods exceeding three years faced expected reductions; those below faced extensions. On average across fields, TRIPs extended patent term by approximately 473 days (about 15 months), but approximately 45% of fields faced greater than 5% probability that individual patents would receive a term reduction. The second source is time variation from two events: a news event at the end of 1992 (when the Blair House Accord substantially reduced uncertainty about TRIPs adoption) and implementation in June 1995. The empirical sample spans 1985Q1–2000Q4 using PATSTAT patent data, augmented by firm-level R&D data from NBER-Compustat for 2,410 listed U.S. firms.

Three main empirical facts emerge. First (Fact 1), innovation and R&D accelerate more during the anticipation phase (1992Q4–1995Q2) in fields with a higher probability of patent term reduction. A one-percentage-point higher reduction probability corresponds to a 1.4% larger increase in granted patent applications before implementation; a one-month shorter average patent term extension corresponds to a 2.9% larger increase. At the firm level, a one-percentage-point higher reduction probability is associated with a 1.9% increase in annual R&D expenditure (approximately $1.7 million), ruling out the interpretation that rising patent counts merely reflect strategic filing adjustments.

Second (Fact 2), this heightened innovative activity persists for at least five years after implementation. Two years post-implementation, a one-percentage-point higher reduction probability corresponds to 1.44 additional quarterly patents (+2.7% in Poisson estimates), and a one-month shorter term extension corresponds to 3.3 more patents (+5.9%). This persistence is driven by indirect effects: the anticipation-induced burst in patenting generates additional follow-on innovation through technology disclosure externalities linked to cumulative knowledge creation. The elasticity of post-implementation innovation to news-phase innovation is estimated at approximately 2.1.

Third (Fact 3), the direct effect of patent term on innovation — estimated by augmenting the DiD specification to control for field-specific innovation histories — is negative for shorter extensions and consistent with prior literature. A one-month shorter patent term extension reduces quarterly patents by 1.7%, and a one-year reduction reduces them by 20.9%. These estimates align with Budish, Roin, and Williams (2015, 2016), who find that a one-year extension of patent monopoly increases R&D by 7%–22% in pharmaceuticals. The identification is supported by the absence of pre-trends, by the finding that pre-news pending period distributions predict realized post-news variation with coefficients near one (0.957–1.104), and by extensive robustness checks.

Q: What was the effective change in U.S. patent term under TRIPs, and why did it differ across fields? A: TRIPs shifted patent expiry from 17 years after grant to 20 years after application date. Because monopoly rights are only fully enforceable after grant, the effective term became 20 years minus the pending period. Fields with average pending periods shorter than three years received net extensions; fields with longer average pending periods faced net reductions. Cross-field variation in pending periods arises because applications in different technical fields are reviewed by distinct USPTO technical units with different complexity and backlog levels.

Q: What was the news event, and how was anticipation established? A: The paper identifies November 1992 — when the Blair House Accord substantially reduced uncertainty about TRIPs adoption — as the news event, with formal ratification in December 1994 and implementation in June 1995. Documentary evidence confirms anticipation: U.S. business executives were involved in TRIPs negotiations from 1986; the patent term change appeared in a 1991 GATT draft; an Advisory Committee report co-signed by IBM, 3M, Motorola, and others referenced it in August 1992; and a New York Times article noted proposed changes in September 1992.

Q: How is the probability of patent term reduction (PL_j) constructed, and what is its distribution? A: PL_j is the fraction of patents in field j granted before the TRIPs news with a pending period exceeding three years, computed using PATSTAT data on U.S. patents granted between January 1990 and May 1992. Approximately 45% of fields faced a reduction probability exceeding 5%, and 15% faced a probability exceeding 10%. Even fields with an average term extension greater than one year had individual-patent reduction probabilities as high as 40%. A 10-percentage-point increase in PL_j corresponds to approximately a four-month shorter average term extension.

Q: What is Fact 1 and what are its quantitative magnitudes? A: Fact 1 states that during the news phase, innovation and R&D increase relatively more in fields with higher patent term reduction probability and shorter average term extension. One year after the news (two years before implementation), a one-percentage-point higher reduction probability generates 0.19 additional quarterly patents (+0.5% in Poisson estimates); a one-month shorter average extension generates 0.35 additional units (+0.8%). These effects approximately triple one year before implementation. At the firm level, a one-percentage-point higher probability is associated with a 1.9% increase in annual R&D (~$1.7 million) in 1993.

Q: Why does news of a potential patent term reduction accelerate rather than deter innovation? A: Innovators who anticipate a reduction in future patent protection under the new regime have strong incentives to file applications before implementation to secure the longer 17-years-from-grant term while it remains available. The acceleration is therefore consistent with innovators preferring longer protection: they rush to file under the more favorable old regime rather than curtailing innovation. Complementary analyses exploiting within-field dispersion in pending periods find that firms were particularly responsive to scenarios involving adverse policy changes, consistent with loss aversion. The dynamics of the news-phase acceleration are also consistent with an R&D gestation lag of approximately two years, as estimated by Pakes and Schankerman (1984).

Q: What is Fact 2 and what drives the post-implementation persistence? A: Fact 2 states that the heightened innovation in fields with higher reduction probability persists for at least five years after June 1995, even though the direct effect of a shorter patent term is innovation-reducing. Two years post-implementation, a one-percentage-point higher reduction probability corresponds to 1.44 additional quarterly patents (+2.7% Poisson) and a one-month shorter extension to 3.3 additional patents (+5.9% Poisson). The persistence is driven by technology disclosure externalities: the news-phase acceleration generates new patented knowledge that subsequent innovations build upon. Fields where new inventions rely more heavily on past innovations from the same field — proxied by backward citation intensity — display stronger post-implementation persistence.

Q: How does the paper separate direct from indirect (externality-driven) post-implementation effects? A: Following Angrist and Pischke (2009), the paper augments the baseline DiD specification to control for field-specific innovation histories via a lagged moving average of past outcomes and pre-determined field attributes interacted with quarterly fixed effects. The resulting coefficients capture the effect of patent term variation orthogonal to the news-induced innovation dynamics. The direct effect estimates are negative post-implementation (Fact 3), while the overall estimates are positive (Fact 2), confirming that the indirect externality channel outweighs the direct channel in the post-implementation period.

Q: What is Fact 3 and how does its magnitude compare to prior literature? A: Fact 3 states that, controlling for the news shock, a shorter patent term extension leads to a relative decline in innovation post-implementation. The estimated semi-elasticity is 1.7% per one-month increase in patent term and 20.9% per one-year increase. These estimates align with Budish, Roin, and Williams (2015, 2016), who find a 7%–22% increase in pharmaceutical R&D per one-year extension, and with Hemous et al. (2023), whose model implies a 1.2% innovation increase per one-month extension.

Q: What is the estimated elasticity of post-implementation innovation to news-phase innovation, and what does it imply? A: Point estimates imply that one additional patent during the news phase generates approximately 5.1 additional patents post-implementation. Given average patent counts of 408.5 during the news phase and 1,000.3 post-implementation, this corresponds to a percent-to-percent elasticity of approximately 2.1. This elasticity captures the technology disclosure externality channel by which transitory accelerations in patenting generate persistent follow-on innovation.

Q: Why is ignoring anticipation (as in Abrams 2009) a problem for DiD identification? A: Anticipation inflates patenting in fields with higher reduction probability during the pre-implementation period, violating the DiD assumption that pre-implementation outcomes provide an unaffected baseline. For example, between April 1994 and March 1995, average monthly patents in field C12P (high reduction probability) were 15.1 units above pre-news levels, versus only 2.4 in field E05D (low reduction probability). Using this inflated pre-implementation level as the DiD reference baseline reverses the sign of the estimated implementation effect relative to the specification that uses the unaffected pre-news baseline.

Q: What evidence supports the technology disclosure externality mechanism over alternative explanations? A: The paper proxies technological dependence by backward citation intensity at the field level and finds that the news-phase acceleration propagates more strongly into post-implementation innovation in fields where new inventions more heavily cite prior same-field patents. Time-varying measures of technological dependence identify this channel as the primary driver of indirect post-implementation effects. Two alternative mechanisms — changes in technological competition and adjustments in patenting strategies — lack comparable empirical support. The finding is consistent with Hegde, Herkenhoff, and Zhu (2023), who document that permanent increases in knowledge diffusion speed permanently raise follow-on innovation rates.

Q: What are the policy implications of jointly considering anticipation and knowledge spillovers? A: Standard patent term analyses that abstract from anticipation effects and knowledge spillovers may substantially mischaracterize full welfare implications. The paper shows that innovation-policy interventions shape both short- and long-run outcomes, and that near-term variation in innovative activity can itself drive medium- to long-term effects through technological externalities. The estimated semi-elasticities of news, direct, and indirect effects provide empirical calibration targets for normative endogenous growth models used to derive optimal patent term, complementing prior normative recommendations ranging from zero protection (Boldrin and Levine, 2013) to infinite protection (Gilbert and Shapiro, 1990).

Effective patent term: The duration of legally enforceable monopoly granted by a patent, equal to 17 years after grant under the pre-TRIPs U.S. regime and 20 years after application minus the pending period under the post-TRIPs regime. Because enforcement begins only at grant, the pending period directly erodes effective protection.

Patent term reduction probability (PL_j): The field-specific fraction of pre-TRIPs patents with a pending period exceeding three years, representing the probability that individual patent applications in that field obtain a net reduction in patent term under the new 20-years-from-filing rule.

News effect: The incremental change in innovation or R&D at the time of policy announcement, induced by future anticipated changes in patent term, before the new policy enters into force. In this paper’s setting, the news effect is positive: higher reduction probability accelerates patenting as innovators rush to file under the favorable existing regime.

Direct implementation effect: The component of the post-implementation change in innovation attributable to the patent term change itself, isolated by controlling for field-specific innovation histories (i.e., abstracting from the indirect effects of anticipation-induced knowledge accumulation). It is negative for shorter patent term extensions, with a semi-elasticity of 1.7% per one-month increase.

Technology disclosure externality: The mechanism by which newly patented knowledge, disclosed through the patent system, enables subsequent inventors to build on prior innovations, generating follow-on inventive activity. In this paper, the transitory news-phase burst in patenting generates a persistent externality, particularly in fields with high backward citation intensity.

Policy anticipation: The phenomenon whereby forward-looking agents adjust behavior in response to credible news about future policy changes before those changes take effect. In this paper, anticipation induces a pre-implementation acceleration in patenting that temporarily pushes innovation in the opposite direction from the direct long-run effect and generates persistent indirect post-implementation effects through knowledge spillovers.

Pending period: The time between patent application and grant during which USPTO examines the application and during which full monopoly rights are not enforceable. Field-level heterogeneity in pending periods — arising from differences in examination complexity and USPTO unit congestion — is the source of cross-sectional identification in the DiD design.

Patents, News, and Business Cycles

Mon, 01 Jan 0001 00:00:00 +0000

This paper constructs an instrumental variable for technology news shocks using patent applications, relaxing all identifying assumptions traditionally used in the news-shock literature. The IV is the component of patent applications orthogonal to pre-existing beliefs (Survey of Professional Forecasters), contemporaneous and lagged monetary and fiscal policy changes (narrative accounts), and own lags. The instrument recovers news shocks that have no effect on aggregate productivity in the short run but are a significant driver of its trend component. The shock prompts a broad-based expansion in anticipation of the future TFP increase—output, consumption, and investment all rise well before any material increase in TFP is recorded. Despite these positive conditional co-movements, the news shock accounts for only a modest share of macroeconomic fluctuations at business cycle frequencies. Financial markets price in news shocks on impact, while most macro aggregates respond with some delay. Previously circulated as “When Creativity Strikes: News Shocks and Business Cycle Fluctuations.”

In depth

Q1. What is the identification strategy and why does it relax traditional assumptions?

The paper constructs an IV for technology news shocks as the component of patent applications orthogonal to pre-existing beliefs (SPF), narrative accounts of monetary and fiscal policy, and own lags—the sole identifying assumption is that no structural disturbance other than contemporaneous technology news affects the U.S. economy through this IV. Traditional identification requires combining zero restrictions on the impact response of TFP with assumptions about its long-run drivers (e.g., Beaudry-Portier 2006 assumes news shocks are the sole long-run driver of TFP). The patent-based IV avoids all of these assumptions, relying only on the exclusion restriction that patent applications, after controlling for expectations and policy, capture news about future technological change and nothing else.

Q2. How do patent applications contain information about future technology?

Patent applications contain information about potential future technological change because exclusive rights create a powerful incentive to apply as early as possible, making patent applications lead TFP improvements by years, while controlling for contemporaneous economic conditions removes the endogeneity of patent filings to current booms. The length of time between application and the eventual diffusion of the innovation within the economy can be several years. The filing date serves as the first measurable time at which the news occurs, even though the underlying idea predates the application. The component of applications orthogonal to SPF forecasts and policy changes represents news about future technology not driven by current conditions.

Q3. What are the macroeconomic effects of technology news shocks?

Technology news shocks generate a broad-based expansion—output, consumption, and investment all rise well before any material increase in TFP is recorded—and financial markets price in news shocks on impact, while most macro aggregates respond with some delay. The positive conditional co-movements are consistent with optimism about future income and productivity generating pre-emptive expansion. Despite these theoretically attractive features, the news shock accounts for only a modest share of macroeconomic fluctuations at business cycle frequencies.

The finding that news shocks account for only a modest share of macro fluctuations at business cycle frequencies implies that, while identified news shocks behave consistently with the news-driven business cycle hypothesis in qualitative terms, they contribute only modestly to aggregate volatility—a finding that differs from models in which news shocks are a primary driver of cycles. This quantitative finding is informative precisely because the identification is instrument-based and free of the theoretical priors imposed by traditional sign-restriction and FEVD approaches, lending credibility to it as an estimate of the true importance of news shocks.

Key concepts

technology news shock : a shock that raises expectations about future aggregate TFP growth without any immediate change in current TFP; the paper’s IV identifies shocks that have no short-run effect on TFP but are a significant driver of its trend component. patent-based instrument : the component of patent applications orthogonal to pre-existing macroeconomic beliefs (SPF), contemporary monetary and fiscal policy changes (narrative accounts), and own lags; used as an IV for technology news shocks that avoids traditional identifying restrictions. news-driven business cycle hypothesis : the proposition that economic fluctuations can arise from changes in agents’ expectations about future fundamentals (particularly future productivity) even absent any current change in those fundamentals; the paper finds qualitative support but only modest quantitative importance.

Peer Effects in Consideration and Preferences

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a general nonparametric model of discrete choice in which peers influence agents through two distinct channels: (1) the set of alternatives an agent considers (consideration set effects) and (2) the agent’s preferences over those alternatives (preference effects). The framework embeds these peer mechanisms in a continuous-time Markov process where agents revise choices at Poisson alarm-clock rates. A peer is classified as a consideration peer, a preference peer, or both, and the network is encoded as two directed edge sets rather than one.

The central identification challenge is recovering network structure, consideration probabilities, and preferences simultaneously, without relying on exogenous variation in covariates or the menu of available options. The paper shows this is achievable using time-series variation in the choices made by connected agents. The key insight is that consideration peers who adopt alternative v change the probability that the focal agent considers v — entering only the “consideration” term of the conditional choice probability (CCP) — while preference peers who adopt alternatives other than v change only the “conditional-on-consideration” selection probability. These cross-alternative patterns in the CCPs allow the researcher to distinguish the two channels. Once consideration-only peers are isolated, their choices serve as exclusion restrictions that mimic artificial menu variation, enabling nonparametric recovery of preferences.

Identification proceeds in stages: (i) recover the full reference group of each agent from changes in CCPs; (ii) separate consideration-only peers from preference-affecting peers using cross-order effects across alternatives; (iii) distinguish preference-only peers from consideration-and-preference peers under an exclusion restriction (Assumption 4) requiring that an agent with a dual-channel peer also has at least one single-channel peer; (iv) recover consideration ratios Q(v|n+1)/Q(v|n) and then the full choice rule. The results allow arbitrary heterogeneity across agents and do not require exogenous menu variation or covariate shifters.

For continuous-time data (Dataset 1), the CCPs and Poisson rates are exactly identified from the observed revision history. For discrete-time panel data (Dataset 2), identification is generic under a mild eigenvalue condition on the transition rate matrix.

The empirical application studies store-opening decisions by China’s two dominant high-end tea chains — Heytea and Nayuki — across prefecture-level cities from their founding through end-2020. By that date, Nayuki had 485 stores in 57 cities and Heytea had 729 stores in 46 cities, in an industry whose total revenue grew from 42.2 to 83.1 billion yuan between 2017 and 2020. Each firm-market pair is modeled as an agent deciding whether to open a new store. The key exclusion restriction is that the cumulative store count of either firm in geographically neighboring markets shifts consideration probabilities but does not enter marginal profitability directly.

Estimation via maximum likelihood yields four substantive findings: (1) Firms exhibit limited consideration — consideration probabilities for markets with no prior presence by either firm are substantially below one. (2) Stores in neighboring markets significantly raise consideration probabilities for a given market, for both own-firm and rival stores; this peer effect in consideration is described as economically large. (3) Own-market store density raises marginal profitability (density economies) while rival presence lowers it (competitive effects). (4) A full-consideration model that omits the attention stage overestimates the negative competitive effect and underestimates positive density effects.

Counterfactual simulations show that removing attention constraints (full consideration) accelerates market penetration substantially: firms enter new markets earlier and achieve broader geographic coverage. Removing peer effects in consideration only — while retaining attention constraints — slows the diffusion of store openings across neighboring markets, because peer effects in consideration function as an informational cascade. Limited consideration also reduces competition by delaying rival entry into high-profitability markets, explaining a significant share of the geographic concentration in first- and second-tier cities during the early expansion phase. The paper’s scope is limited to settings with repeated, non-durable choices; it does not model forward-looking behavior or multiple equilibria, which the authors note as directions for future research.

Q: What are the two peer-effect channels in the model, and how do they differ structurally? A: A consideration peer influences whether an alternative enters the agent’s consideration set — specifically, the probability Q_a(v | n) that alternative v is considered is a function of the number n of consideration peers currently adopting v. A preference peer influences the choice rule R_a(v | y, C) — the probability that v is selected conditional on it being in the consideration set. Importantly, the paper models the two channels as affecting logically separate stages of the decision process, so the observed CCP factors into a consideration term and a conditional-selection term that respond to distinct sets of peers.

Q: Why does the standard identification approach of varying menus fail here, and how does the paper substitute for it? A: Menu variation requires the researcher to observe the same agent facing different sets of available alternatives, which is unavailable in many empirical settings. The paper replaces exogenous menu variation with endogenous variation generated by consideration-only peers: when a consideration-only peer adopts alternative v, the focal agent’s probability of considering v rises, effectively mimicking the removal of other alternatives from her consideration set. This peer-induced variation in consideration is then used to trace out the choice rule R_a over counterfactual menus without any actual menu changes.

Q: How does the paper separate consideration peers from preference peers in the data? A: The decomposition exploits an asymmetry in how the two peer types appear in the log-CCP. When a consideration peer switches to alternative v, the term ln Q_a(v | .) changes but the conditional-selection term ln D_a(v | .) remains unchanged, because the agent already considers v. Conversely, when a preference peer adopts an alternative other than v, only the conditional-selection term shifts. The paper formalizes this via cross-order effects of peers across alternatives in the CCPs (Propositions 3.1–3.3) and invokes Assumption 4 — requiring at least one single-channel peer when a dual-channel peer exists — to complete the separation.

Q: What is Assumption 4 and why is it necessary? A: Assumption 4 states that if agent a has a peer in N_CR_a (a peer affecting both consideration and preferences), then a also has at least one additional peer affecting only consideration or only preferences. Without this exclusion restriction, the consideration and preference effects of a dual-channel peer are not separately identified from each other; the single-channel peer provides the variation needed to pin down each component separately.

Q: What does Proposition 2.1 establish and what does it require? A: Proposition 2.1 establishes existence and uniqueness of an invariant equilibrium distribution mu over choice configurations, with full support. It requires Assumptions 1 (independent consideration), 2(i) (strictly positive consideration probability for every alternative), and 3(i) (strictly positive probability of selecting any non-default alternative from some reachable consideration set). The continuous-time Poisson structure ensures zero probability of simultaneous revisions, which rules out multiple equilibria in the data-generating process.

Q: How does the paper handle discrete-time panel data, where only periodic snapshots of choices are observed? A: The paper invokes results from Blevins (2017, 2026) to show that the transition rate matrix W of the continuous-time process is generically identified from the discrete-time transition matrix observed at interval Delta, provided the eigenvalues of W do not differ by integer multiples of 2pii/Delta. Once W is identified, the CCPs P and Poisson rates lambda_a are recovered. This result is described as generic, meaning it holds except on a measure-zero set of parameter values.

Q: What data does the empirical application use, and what are the key sample statistics? A: The application uses city-level store registration data sourced from the National Enterprise Credit Information Publicity System (via CnOpenData, 2021), supplemented by regional statistics from the China City Statistical Yearbook (2016–2021). The sample ends in 2020 to avoid COVID-19 demand shifts. By end-2020, Nayuki had 485 stores across 57 cities and Heytea had 729 stores across 46 cities. The high-end tea industry’s total revenue grew from 42.2 to 83.1 billion yuan between 2017 and 2020.

Q: What is the key exclusion restriction in the empirical specification, and why is it plausible? A: Stores in geographically neighboring markets (parameterized by distance bins d(m,m’)) enter the attention index pi_tilde but are excluded from the marginal profit index pi_bar. The rationale is that nearby store counts are informative signals that draw managerial attention to a market (an informational spillover) but do not directly alter the profitability of operating in that market — profitability depends on local demand, competition within the market, and own firm density, not on activity in adjacent markets. This restriction identifies the consideration-only peer channel.

Q: What does the paper find about biases from ignoring limited consideration? A: When the two-stage model (consideration + choice) is replaced by a single-stage full-consideration model, the estimated payoff parameters differ substantially. Specifically, the full-consideration model overestimates the negative effect of competition (rival presence in the same market) and underestimates the positive effect of own-store density. The intuition is that correlated entry patterns driven by shared consideration spillovers are misattributed to payoff interactions when the consideration stage is omitted.

Q: What do the counterfactual simulations show about the role of limited consideration in market dynamics? A: Three counterfactuals are compared against the baseline. Under full consideration (no attention constraints), market penetration is substantially faster — firms enter new markets earlier and achieve broader geographic coverage. Removing peer effects in consideration while retaining attention constraints slows geographic diffusion because the informational cascade that propagates entry to neighboring markets is eliminated. Limited consideration also reduces competition by delaying rival entry into high-profitability markets; markets with high potential demand remain underserved for longer. Collectively, limited consideration explains a significant portion of the geographic concentration of tea chain stores in first- and second-tier cities during the early expansion period.

Q: What forms of heterogeneity does the identification allow, and what does it not require? A: The nonparametric identification results accommodate arbitrary heterogeneity across agents in consideration mechanisms Q_a, choice rules R_a, Poisson revision rates lambda_a, and network positions. The identification requires neither exogenous covariates that shift preferences or consideration, nor variation in the set of available alternatives across observations. It relies solely on time-series variation in the choices made by connected agents, which are endogenous to the model and are themselves identified in the first stage.

Q: How does the paper model history dependence, and does it change the main identification results? A: Section 4.1 extends the model to allow consideration probabilities and choice rules to depend on the agent’s own choice history h_t in addition to the current configuration y. Proposition 4.1 states that under Assumptions 1–4 applied conditional on both y_{at} and h_t, all identification propositions from Section 3.1 remain valid. The extension also allows consideration probabilities to equal one, enabling nontrivial dynamics in consideration sets driven by past choices.

Q: How is the unobservable default handled in the empirical application? A: When the default alternative (e.g., “do not open a store”) is unobserved, the Poisson revision rate lambda_a cannot be separately identified from the CCPs without normalization. The paper normalizes lambda_a = 1 for each agent in the empirical application, treating the revision opportunity rate as fixed and recovering all remaining primitives under this normalization.

Consideration set: The subset C of the full menu Y that agent a actually attends to at the moment of revision; formed before the choice rule is applied. Alternative v enters C independently with probability Q_a(v | n), where n is the number of consideration peers currently adopting v. The default alternative is always in the consideration set.

Conditional choice probability (CCP): P_a(v | y), the ex-ante probability that agent a selects alternative v given choice configuration y; equal to the product of the consideration probability Q_a(v | .) and the conditional-selection probability D_a(v | .), integrated over all possible consideration sets.

Choice configuration: The vector y = (y_a)_{a in A} recording the current alternative selected by every agent in the network simultaneously; the state variable of the continuous-time Markov process.

Consideration-only peer: A peer a’ in N_C_a \ N_R_a whose choices enter the consideration probability Q_a but not the choice rule R_a. Variation in the choices of consideration-only peers serves as an exclusion restriction that mimics artificial menu variation for identifying preferences.

Preference-only peer: A peer a’ in N_R_a \ N_C_a whose choices enter the choice rule R_a but not the consideration probability Q_a.

Cross-order peer effect: The pattern in the CCP by which a consideration peer’s adoption of alternative v changes ln P_a(v | .) but not the conditional-selection component, while a preference peer’s adoption of a different alternative v’ changes the conditional-selection component but not the consideration component; this asymmetry is the key to separating the two channels.

Limited consideration: The situation in which Q_a(v | n) is strictly less than one for at least some alternatives v and peer counts n, so that the agent does not evaluate all available options before choosing; distinct from full rationality in which all alternatives are always considered.

Mean attention index (pi_tilde): The latent index governing the consideration probability in the empirical specification; it depends on own and rival store counts in the same and neighboring markets and on firm fixed effects, but is excluded from the marginal profit index — constituting the empirical exclusion restriction that separates the consideration and payoff channels.

Pigovian Transport Pricing in Practice

Mon, 01 Jan 0001 00:00:00 +0000

This paper reports on the MOBIS experiment, a large-scale randomized controlled trial (RCT) implementing a multi-modal Pigovian transport pricing scheme in urban areas of German- and French-speaking Switzerland. The central research question is whether a first-best transport pricing scheme — one that charges users the full marginal external costs of their travel choices, varying across time, space, and mode — generates meaningful behavioral responses, and how those responses compare to a pure information intervention.

The study recruited participants from urban areas, requiring them to be between 18 and 65 years old and to use a car at least two days per week. After contacting over 90,000 individuals and an initial online screening of 21,800 respondents, 3,656 participants completed the RCT. Each participant agreed to have their daily travel tracked via a smartphone app (“Catch-My-Day”) for eight weeks: four weeks of observation followed by four weeks of treatment. Assignment to treatment and control groups was fully randomized without stratification.

The pricing treatment gave participants a budget equal to their observed external costs during the observation period plus a 20% buffer, from which the external costs of their actual travel were deducted in real time; any remaining balance was theirs to keep. External costs were computed across all modes using official Swiss Federal Roads Office monetization factors, including congestion (via a MATSim-based average marginal cost approach), CO2 climate costs (CHF 136.08/ton), health costs from air pollution (PM10 and NOx), and accident and physical activity effects for active and public modes. Public transport also carried a peak-hour surcharge of CHF 0.10/km for congested zone-pairs. A second “information-only” treatment provided identical information about external costs but imposed no financial charge. A control group received only weekly summaries of kilometers traveled by mode.

The regression framework is a difference-in-differences specification with person, calendar-day, and day-of-study fixed effects, estimated in levels for external-cost outcomes (due to negative values from walking’s net external benefit) and via Poisson Pseudo-Maximum Likelihood for non-negative outcomes.

The pricing treatment reduced total external costs by CHF 0.215 per day (p < 0.01), a 5.1% reduction relative to the control group. The average private cost of transport for the control group during the treatment period was CHF 25.72 per day; the external cost was CHF 4.22 per day, implying that Pigovian pricing raised total transport costs by 16.4% on average. The implied price elasticity of external costs with respect to this price increase is -0.31. The reduction is attributable to mode substitution toward public transport and active modes and to departure time shifting away from peak hours, but not to a reduction in total distance traveled.

The information-only treatment produced a coefficient of -0.087, which is not statistically significant at conventional levels for the full sample. The differential effect of adding pricing to information is -0.127 (marginally significant, p < 0.1), with the pricing increment particularly important for reducing congestion costs. Sensitivity analysis shows that removing the control group and time fixed effects inflates the before-vs.-after elasticity to between -0.57 and -0.71, substantially larger than the preferred estimate of -0.31, underscoring the importance of the experimental design.

Heterogeneity analysis reveals that men respond more strongly than women, German speakers more than French speakers, participants under 30 more than older participants, and those with above-median altruistic values respond significantly even to information alone. Correct knowledge of the definition of external costs (present in 45% of the sample) is a key driver of the pricing treatment effect. These scope conditions — mode availability, urban Swiss context, short 4-week treatment window, mandatory car use eligibility, and the specific external cost monetization framework — bound the generalizability of the elasticity estimate.

Q: What is the main treatment effect of the Pigovian pricing scheme on external transport costs? A: The pricing treatment reduced total external costs by CHF 0.215 per day, which is a 5.1% reduction relative to the control group (p < 0.01). About half of the reduction came from health costs, with congestion and climate costs following in magnitude. The implied elasticity of external costs with respect to the Pigovian price increase is -0.31, meaning a 10% increase in total transport costs from Pigovian pricing would reduce external costs by approximately 3.1% in the short run.

Q: How was the Pigovian price increase calculated, and what was its magnitude relative to private costs? A: The average private cost of transport for the control group during the treatment period was CHF 25.72 per day, and the average external cost was CHF 4.22 per day. The external cost thus represents 16.4% of total (private plus external) transport costs, and dividing the 5.1% reduction in external costs by this 16.4% price increase yields the elasticity of -0.31.

Q: What mechanisms drove the reduction in external costs? A: The reduction resulted from a combination of mode substitution — a shift away from car use toward public transport and active modes — and departure time shifting away from peak hours. Critically, total distance traveled did not decline; the behavioral adjustment operated entirely through changes in how and when people traveled, not in how much.

Q: What was the effect of the information-only treatment? A: The information-only treatment produced a coefficient of -0.087 CHF per day, which was not statistically significant at conventional levels for the full sample. It was statistically significant only for subgroups, notably participants with above-median altruistic values. The differential effect of adding pricing to information (alpha_P minus alpha_I = -0.127) was marginally significant (p < 0.1) and was particularly concentrated in congestion cost reductions, suggesting that the monetary incentive is especially important for internalizing the congestion externality.

Q: Why is the control group critical, and how does removing it affect the estimated elasticity? A: The tracking data show a seasonal negative trend in external costs over the study period; without a control group, this trend would be incorrectly attributed to the treatment, inflating the estimated effect. When both day-of-study and calendar-day fixed effects are removed (approximating a before-vs.-after design without a control group), the estimated elasticity rises to between -0.57 and -0.71, roughly double the preferred estimate of -0.31. This highlights that most prior studies in the literature, which lack control groups, are likely to overestimate treatment effects.

Q: What heterogeneity is observed in the treatment response? A: Men respond more strongly than women to both treatments, with the gender gap particularly pronounced for congestion costs. German speakers respond more strongly than French speakers. Participants under age 30 show stronger responses than older participants. Those scoring above the median on an altruistic values index respond significantly not only to pricing but also to information alone. Participants who correctly defined external costs (45% of the sample) drive the pricing treatment effect; a causal forest analysis confirms knowledge of external costs, age below 30, and language region as key heterogeneity drivers.

Q: How were external costs computed across modes, and what are the key monetization parameters? A: For private road transport, GPS tracks were map-matched using Graphhopper and processed via MATSim modules; emission factors came from the HBEFA 3.3 database, and congestion was assessed via an average marginal cost approach incorporating spillback effects. Externalities were monetized at CHF 136.08/ton for CO2, CHF 515,497–1,358,461/ton for PM10 (rural vs. urban), CHF 7,109/ton for NOx (regional), and a value of travel time savings of CHF 25.77/hour. For other modes, per-km values from the Swiss Federal Roads Office were applied. Walking carries net external benefits (negative external costs), while cycling carries small net external costs because accident costs exceed physical activity benefits.

Q: How was public transport priced in the experiment, and why was it simplified? A: A second-best zonal peak-hour surcharge of CHF 0.10/km was applied to public transport stages between zone-pairs experiencing peak demand, with peak windows set at 7–9 am and 5–7 pm. Full first-best pricing of public transport crowding was deemed infeasible because crowding effects are highly heterogeneous spatially and temporally, often concentrated in very short windows on specific lines, making aggregate distribution unreasonable.

Q: Was there evidence of gaming the mode detection system? A: Because participants could manually correct the app’s algorithmic mode assignments — and the pricing group had an incentive to overclaim low-cost modes — the potential for strategic misreporting was examined. While the analysis could not rule out some gaming, the main results were shown to be robust to excluding potential gamers, suggesting that gaming did not materially distort the treatment effect estimates.

Q: What does the study imply for transport pricing policy? A: The elasticity of -0.31 provides a benchmark for policymakers: a full Pigovian pricing scheme that raises total transport costs by about 16% can be expected to reduce external costs by about 5% in the short run in an urban context. The finding that congestion costs respond more to pricing than to information alone suggests the monetary component is essential for this externality. Heterogeneous responses — particularly the weaker responses by women and French speakers — have distributional implications. The experiment is a proof of concept that first-best transport pricing can generate meaningful behavioral responses, but scaling it would require addressing privacy concerns from GPS tracking, technical infrastructure, and political economy challenges.

Pigovian transport pricing: A pricing scheme that charges each user the marginal external costs of their transport choices — including health, climate, congestion, and noise costs — as they vary across time, space, and mode, intended to internalize the gap between private and social costs of travel.

External costs of transport: Costs borne by society rather than the individual traveler, including congestion (delay imposed on others), climate damages (CO2 emissions), health costs (local air pollution, accidents), and noise; in this paper, computed in real time from tracked trips using official Swiss monetization values.

Average treatment effect (ATE): The difference-in-differences estimate of the causal effect of the pricing or information treatment on outcomes, identified from the randomized assignment and controlling for person, calendar-day, and day-of-study fixed effects.

Mode substitution: The behavioral response in which travelers shift from higher-external-cost modes (primarily car) to lower-external-cost modes (public transport, walking, cycling) in response to pricing, as distinct from reducing total travel distance.

Departure time shifting: The behavioral response in which travelers adjust when they depart to avoid peak-hour congestion surcharges, contributing to reduced congestion externalities without reducing total distance traveled.

Information-only treatment: An experimental arm receiving identical information about external costs as the pricing group but facing no financial charge, used to isolate the informational component of the pricing treatment from the monetary incentive component.

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Policy Diffusion and Polarization across U.S. States

Mon, 01 Jan 0001 00:00:00 +0000

DellaVigna and Kim study the innovation and diffusion of policies across U.S. states using a dataset of over 700 state laws spanning seven decades. The central question is what predicts whether a state adopts a policy — and how those predictors have changed over time. The paper draws on two primary data sources: the State Policy Innovation and Diffusion (SPID) Database (Boehmke et al., 2020), covering 676 policies, and a hand-collected sample of 57 policies from 91 NBER working papers (April 2012–September 2021) that feature state-level policy variation. The combined dataset covers 733 policies adopted from the 1950s onward across the contiguous 48 states.

On policy innovation, the paper finds that state capacity plays only a small role: larger and richer states are only slightly more likely to introduce new policies, innovation originates from both Republican and Democratic states, and the patterns are largely idiosyncratic with respect to observable state characteristics. California is the most frequent innovator, but large states like Florida and Texas rank in the middle.

For policy diffusion, the paper employs both a static Geary’s C clustering statistic (measuring whether the first 10 adopting states cluster geographically or politically relative to a random-diffusion benchmark) and a dynamic logit hazard model estimated separately by decade. The hazard model identifies three similarity channels — geographic, demographic, and political — and allows their coefficients to vary over time.

The central finding is a structural break in diffusion patterns around 2000. From the 1950s to the 1990s, geographic proximity is the dominant predictor of policy adoption: the coefficient on geographic similarity is 0.34 in the 1970s and remains roughly constant at 0.33 in the most recent decade. Demographic similarity is consistently positive and stable (approximately 0.20 in the 1980s, 0.22 in the 2010s). Political similarity — measured by closeness in Republican vote-share from the most recent presidential election — is a modest predictor before 2000, with coefficients between 0.14 (1970s) and 0.17 (1990s). Since 2000, the political similarity coefficient triples: 0.46 in the 2000s and 0.52 in the 2010s, making it by far the strongest predictor. The overall pseudo R-squared rises from 0.13 in the 1970s to 0.19 in the 2010s.

These patterns are more pronounced for policies studied by economists: in the NBER subsample, the political similarity coefficient reaches 0.66 (s.e.=0.09) in the most recent two decades, versus 0.42 (s.e.=0.04) in the SPID sample.

The paper tests whether the increased role of political similarity reflects correlated voter preferences, learning, or competition versus party discipline. Against correlated-preferences explanations: adding cross-state migration flows as a similarity measure reduces geographic predictive power but leaves the political similarity coefficient entirely unchanged; and typical policy-outcome variables (poverty rate, opioid mortality, income) have not become more correlated among politically similar states over time. In favor of party discipline: similarity in unified state government has zero predictive power through the 1990s but a coefficient of 0.42 (s.e.=0.06) in the 2000s–2010s. An event study of switches to unified party control confirms this causally for 1991–2020: switching to unified government raises the probability of passing ideologically aligned laws by approximately 2 percentage points in the four years following the switch, with no pre-trends and no effect on neutral-leaning laws; the same event study for 1950–1990 yields no detectable effect.

COVID policies (77 state laws since October 2019) show strong political similarity in adoption; historical vaccination mandate policies (28 laws since 1975) show no political similarity effect. The paper concludes that rising party polarization at the state level — detectable from the 2000s onward, lagging the Congressional trend by roughly four to five decades — is the primary driver of the shift in diffusion patterns. The authors additionally classify each of the 57 NBER-sample policies by type of diffusion as an input for difference-in-differences research design assessment.

Q: What data do the authors use and what is its scope? A: The main source is the SPID Database (Boehmke et al., 2020), covering 676 policies over seven decades. The authors supplement this with 57 policies hand-collected from 91 NBER working papers (2012–2021) that use state-level policy variation. The combined sample covers 733 policies adopted from the 1950s onward in the contiguous 48 states, with the SPID sample averaging 23 adopting states per policy and the NBER sample averaging 29.

Q: Do states with more resources or larger populations systematically innovate more policies? A: The evidence for a state-capacity hypothesis is weak. There is only suggestive evidence that higher per-capita income predicts being in the top-20% of innovators, and no clear difference in population between the top and bottom innovators. Innovations arise from both Republican and Democratic states. One consistent correlate is urban population share, but overall innovation is largely idiosyncratic with respect to observable characteristics.

Q: What was the dominant predictor of policy diffusion before 2000? A: Geographic proximity was the dominant predictor. The coefficient on geographic similarity in the hazard model is 0.34 in the 1970s and remains stable at approximately 0.33 in the 2010s. Demographic similarity contributes consistently at approximately 0.20. Political similarity before 2000 is modest, ranging from 0.14 in the 1970s to 0.17 in the 1990s — roughly one-third to one-half the magnitude of the geographic coefficient.

Q: How dramatically does political similarity change after 2000, and is this finding robust? A: The political similarity coefficient triples, rising from 0.17 in the 1990s to 0.46 in the 2000s and 0.52 in the 2010s, making it the largest single predictor in recent decades. This pattern is robust across linear probability models, alternative measures of political similarity, alternative thresholds for “closest” states (closest fifth, fourth, third, or half all yield comparable coefficients), and alternative ways of computing adoption counts.

Q: Is the shift toward political diffusion stronger for policies economists study? A: Yes. In the NBER subsample, the political similarity coefficient reaches 0.66 (s.e.=0.09) in the 2000s–2010s, compared to 0.42 (s.e.=0.04) in the SPID sample. Geographic similarity also has somewhat higher coefficients in the NBER sample throughout the period. This implies that the policies most studied for difference-in-differences evaluation are also those most subject to politically-driven diffusion.

Q: What does the Medicaid case study illustrate about political polarization? A: ACA Medicaid expansion spread almost exclusively along partisan lines, with Republican vote-share accurately predicting the year of adoption. Crucially, the states that delayed or declined adoption — higher Republican vote-share states — had a higher share of population that would benefit from the expansion and therefore face a worse policy-need match. By contrast, the original 1966 Medicaid rollout showed no relationship between state political leaning and timing of adoption, and neither did the 1960s–1970s food stamp program expansion.

Q: How do the authors distinguish party discipline from correlated voter preferences as the mechanism? A: Two tests point away from correlated preferences: (1) cross-state migration flows, when added as a similarity measure, absorb geographic predictive power but leave the political similarity coefficient entirely unaffected; (2) typical policy-outcome variables (opioid mortality, poverty rate, income, etc.) have not become more correlated among politically similar states over time, contradicting the hypothesis that local needs or environments have become politically correlated.

Q: What is the direct evidence for party discipline as the operative mechanism? A: The authors construct a measure of similarity based on unified party control (governor and both chambers of the same party). This variable has zero predictive power through the 1990s (point estimate near zero). In the 2000–2020s, the coefficient for unified-government similarity is 0.42 (s.e.=0.06), making it the strongest single predictor of adoption in those decades. States with divided governments show no predictive power of adoption by other divided-government states, further isolating the role of party control.

Q: What does the event-study of switches to unified party control show? A: Switches to unified party control in 1991–2020 produce a statistically significant increase of approximately 2 percentage points in the probability of adopting ideologically aligned laws within four years of the switch, relative to the year before. The effect emerges in year t+1 and is persistent, with no pre-trends, and the effect on neutral-leaning laws is zero, ruling out a simple reduced-gridlock story. The same event study for 1950–1990 detects no effect.

Q: How do COVID state policies compare to historical vaccination policies in terms of political diffusion? A: COVID policies (77 state laws, October 2019–August 2021) show significant political similarity in adoption, consistent with the recent-decade patterns. Vaccination mandate laws (28 policies since 1975) show no political similarity effect whatsoever, with demographic and modest geographic similarity being the relevant predictors. This contrast underscores that political polarization in policy adoption is a recent phenomenon that has spread even to policy areas without prior partisan patterning.

Q: How does partisan polarization at the state level compare temporally to polarization in Congress? A: Congressional polarization (measured by DW-NOMINATE) has been rising since the 1950s. State-level policy polarization, as documented here, does not emerge until the 2000s — a lag of roughly four to five decades. The paper notes it has risen rapidly and has already reached policy domains (such as COVID mandates) that showed no political patterning historically.

Q: Does the diffusion pattern vary across policy types? A: Yes. For economic policies, geography and demographics decline in importance over time with a smaller increase in political predictors. For non-economic (social) policies, geographic importance remains stable while political polarization is especially strong. Political polarization is strongest in Republican-leaning and Democratic-leaning states, and weaker among battleground states, consistent with a party-driven model where ideologically extreme states adopt from each other.

Q: How do the authors classify individual NBER-sample policies by diffusion type? A: Using Geary’s C statistics computed separately for geographic and political clustering for each of the 57 NBER policies, the authors identify three approximate clusters: (1) primarily politically-clustered (e.g., Medicaid expansion); (2) jointly geographically and politically clustered (e.g., ban on asking about past salary history); and (3) largely idiosyncratic, neither geographically nor politically clustered (e.g., anti-bullying laws). This classification has direct implications for assessing identification threats in difference-in-differences designs.

Q: What does the overall predictability of policy adoption look like over time? A: The pseudo R-squared from the logit hazard model rises from 0.13 in the 1970s to 0.19 in the 2010s. The increase in political similarity is large enough not only to surpass geographic similarity as a predictor but to make the overall process of state policy adoption more predictable over time.

Policy diffusion: The process by which a policy adopted in one state subsequently spreads to other states; measured here along geographic, demographic, and political dimensions using a logit hazard model estimated by decade.

Geary’s C statistic: A ratio of weighted to unweighted average pairwise squared differences in adoption status, adapted from spatial statistics (Geary, 1954). Values below 1 indicate clustering; values above 1 indicate anti-clustering. The paper reports 1−C so higher values mean more clustering among similar states.

Policy innovation: First-year adoption of a law in any state; a state is an “innovator” if it adopts in the first year the policy appears anywhere. The paper distinguishes innovation (origination) from diffusion (spread).

Logit hazard model: A discrete-time logit model estimated at the state-year-policy level for all states that have not yet adopted a given policy, with policy-decade fixed effects as a baseline hazard and three time-varying similarity measures (geographic, demographic, political) as key predictors.

Political similarity: Closeness of two states’ Republican vote-shares from the most recent presidential election; the closest third of states in this dimension are used to construct the diffusion measure. Shown to be independent of — and to have grown far more predictive than — geographic similarity since 2000.

Unified party control: A state government in which the governor and both state legislative chambers belong to the same party. The paper shows this is the variable most predictive of politically-driven policy diffusion in the 2000s–2020s, with a coefficient of 0.42 where it was effectively zero before 2000.

Party discipline / party polarization: The paper’s preferred explanation for post-2000 patterns: state politicians increasingly vote and adopt policies along party lines beyond what voter preferences alone would predict, with the effect detectable since the 2000s at the state level, lagging the Congressional polarization trend by roughly four decades.

Political Pressure on the Fed

Mon, 01 Jan 0001 00:00:00 +0000

This paper combines a hand-collected archival data set of over 800 personal interactions between U.S. Presidents and Federal Reserve officials from 1933 to 2016 with a narrative structural VAR to identify shocks to political pressure on the Fed and quantify their macroeconomic effects. The identification strategy exploits the well-documented Nixon-Burns episode of 1971—corroborated by Nixon Tapes recordings and Burns’s personal diary—as a narrative restriction that the spike in personal interactions that year was driven primarily by a political pressure shock rather than by economic conditions. Political pressure shocks are found to (i) increase inflation strongly and persistently, (ii) lead to statistically weak negative effects on activity, (iii) contribute to inflationary episodes outside the Nixon era, and (iv) transmit differently from standard expansionary monetary policy shocks because political pressure can be publicly observed, generating a stronger direct effect on inflation expectations. Quantitatively, increasing political pressure by half as much as Nixon, sustained for six months, is estimated to raise the price level by more than 8%.

In depth

Q1. What is the narrative identification strategy and how is the Nixon-Burns episode exploited?

The identification strategy imposes that the spike in President-Fed personal interactions in 1971 is mainly driven by a political pressure shock, exploiting the well-documented fact that Nixon pressured Burns to ease monetary policy in the run-up to his 1972 re-election. Recordings from the “Nixon Tapes” and Burns’s personal diary corroborate this interpretation: Burns wrote that “the President will do anything to be reelected” and that Nixon urged him to “start expanding the money supply.” Romer and Romer (2004) estimated large easing shocks to monetary policy prior to Nixon’s re-election, contrasting with a large systematic tightening after it, further supporting that Burns eased in response to the pressure. Narrative evidence from Johnson’s pressure in the 1960s is additionally used to strengthen the identification.

Q2. What does the new data on President-Fed personal interactions show?

The paper hand-collects over 800 personal interactions between U.S. Presidents and Fed officials from the historical daily schedules made available by the Presidential Libraries from Franklin D. Roosevelt (1933) through Barack Obama (2016). The average interaction lasts 53 minutes; 36% are one-on-one; 11% occur on weekends; 16% are in social settings such as dinners; 92% involve the Fed Chair and 8% other Fed officials. There is large variation across administrations: President Nixon interacted with Fed officials 160 times, while only 6 interactions occurred under Clinton. These interactions arise endogenously in response to economic conditions, which is why narrative identification is needed to isolate the political pressure component.

Q3. What are the estimated macroeconomic effects of political pressure shocks?

Political pressure shocks are found to increase inflation strongly and persistently, to have statistically weak negative effects on activity, and a pressure shock half as large as Nixon’s sustained over six months is estimated to raise the price level by more than 8%. The weak activity effect distinguishes these shocks from standard demand expansions; the mechanism operates more through expectations channels than through aggregate demand, consistent with the public observability of political pressure on the central bank. The evidence also suggests political pressure shocks contributed to inflationary episodes in periods beyond the Nixon era.

Q4. Why do political pressure shocks transmit differently from conventional monetary policy easing shocks?

Political pressure shocks transmit differently from standard expansionary monetary policy shocks primarily because political pressure on the Fed can be publicly observed, which generates a stronger direct effect on inflation expectations than a private Fed decision to ease. The paper finds a stronger effect of political pressure shocks on inflation expectations relative to the activity effect, consistent with this channel: when the public observes that the President is pressuring the central bank, expected inflation rises even before the Fed acts on that pressure.

Key concepts

President-Fed personal interactions : face-to-face or telephone contacts between U.S. Presidents and Federal Reserve officials recorded in historical presidential daily schedules 1933–2016; used as a noisy observable proxy for political attention to the Fed, from which a political pressure shock series is extracted via narrative restrictions.

political pressure shock : an exogenous, structurally identified shock to the intensity of political influence on Fed policy, isolated using a narrative SVAR restriction that the 1971 Nixon-Burns spike in interactions was driven by political pressure rather than economic conditions.

narrative identification : an approach that imposes sign or zero restrictions on a structural VAR at specific historical episodes known from external archival evidence to be driven predominantly by a particular structural shock; here used to exploit the Nixon-Burns and Johnson-Fed pressure episodes.

Quantifying Supply-Side Climate Policies

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks three questions about supply-side climate policies in the oil market: how do oil companies respond to production-based taxes; what are the aggregate effects of such taxes on global CO2 emissions; and what are the distributional consequences across consumers, producers, and governments? The study addresses a gap in empirical evidence at a time when supply-side restrictions on fossil fuel production are gaining policy traction but the quantitative literature remains limited.

The authors use proprietary company-level data from Rystad Energy’s UCube database covering 49,023 oil assets across 84 countries representing 98.1% of global oil production from 2000 to 2019. They identify 84 production tax reforms (54 increases, 30 decreases) with an average magnitude of roughly 5–6 percentage points. The empirical strategy is a difference-in-differences design that compares a company’s activity in a treated tax regime before and after a reform to the same company’s activity in other regimes over the same period, absorbing company-tax regime fixed effects, company-year fixed effects, and region-year fixed effects. This within-company cross-border comparison is used to test for, and rule out, activity-shifting spillovers. Two-stage least squares instruments the after-tax oil price with production taxes to isolate tax-driven price variation.

The primary behavioral margin is exploration: a one-percentage-point increase in the production tax rate reduces exploration expenditure by 2.6% on average over the study period, growing to 4.1% beyond five years. The elasticity of exploration with respect to the after-tax oil price is 1.96. Reduced exploration translates into fewer discoveries; a one-percentage-point tax increase reduces discovered oil amounts by 4.3% on average and by 8.9% beyond five years. The authors find no statistically significant effect of taxes on production from existing conventional fields, consistent with high adjustment costs for already-producing wells. Unconventional production (shale, oil sands, tar sands) exhibits a statistically significant intensive-margin production response to taxes. Taxes also have no detectable effect on the extraction cost of newly discovered deposits, indicating that firms do not redirect search toward lower- or higher-cost deposits at the margin.

Translating these firm-level responses into market outcomes, the authors build a dynamic field-level model spanning 2020–2100, combining field-by-field production profiles calibrated from Rystad data with demand elasticities of −0.2 and −0.5 drawn from the literature. The existing average production-weighted royalty of 21% already implies an indirect carbon price of approximately $32/tCO2 at a reference oil price of $65/barrel, an order of magnitude above the current global average demand-side carbon price of $3.1/tCO2.

Under a permanent global climate royalty surcharge of 20 percentage points, annual emissions from oil fall by 5–7% in the first five years and by 9–20% in the medium term (by year 2100). The cumulative reduction over 2020–2100 is 85–161 GtCO2, or 1.0–2.0 GtCO2 per year on average. The oil price rises by $8–14/bbl initially and by $23–27/bbl by year 2100. Tax revenue to oil-producing governments increases by $590–870 billion per year; consumer surplus falls by roughly $500–730 billion per year; producer surplus falls by $270–310 billion per year. The policy breaks even in direct economic terms at a social cost of carbon of $72–84/tCO2.

When the surcharge is adopted only by OECD countries (30% of current production, 49% of global exploration), short-term carbon leakage is 16–37%, rising to 58–82% by year 2100 as non-OECD producers increase exploration and development in response to the higher oil price. Net cumulative global emission reductions under the OECD-only scenario are 54–107 GtCO2 (47–73% of what the OECD reduction alone would achieve), roughly two-thirds of the global scenario outcome.

Q: What is the primary behavioral margin through which oil companies respond to production taxes? A: The primary margin is exploration expenditure. A one-percentage-point increase in the production tax rate reduces exploration by 2.6% on average across the study period, growing to 4.1% in the period six to twenty years after the reform. The after-tax oil price elasticity of exploration is 1.96, meaning a 1% increase in the after-tax price raises exploration by approximately 2%. The Poisson regression, which accounts for firms with zero exploration in a regime, yields consistent results, indicating the finding is not driven by firm entry or exit.

Q: Do production taxes affect output from existing oil wells? A: For conventional oil fields, the production response is statistically indistinguishable from zero across all specifications and time horizons, consistent with high adjustment costs making already-producing conventional wells insensitive to tax-driven price changes. Unconventional production (shale oil, oil sands, tar sands, extra heavy oil) is the exception, exhibiting a statistically significant intensive-margin production response to taxes. This asymmetry aligns with Bjørnland et al. (2021), who find that unconventional production is more price-sensitive than conventional production.

Q: Do taxes affect the cost profile of newly discovered deposits? A: No. The paper finds no statistically significant effect of production tax changes on the extraction cost of newly discovered fields, across all specifications and time horizons. This implies that, at the margin, firms do not redirect exploration toward lower-cost or higher-cost deposits in response to taxes; the volume and cost distribution of new discoveries are therefore treated as invariant to the tax regime in the quantitative model.

Q: How does the paper address potential activity-shifting spillovers across countries? A: The paper directly tests for spillovers by including both the own-regime tax rate and the company’s exploration-weighted average tax rate abroad as regressors; the foreign average tax rate has no statistically significant effect on domestic exploration. The analysis is also repeated restricting to small companies operating in two or fewer countries, where spillovers would be most pronounced; the null result on spillovers holds. Dropping these small companies from the main sample leaves the primary estimates unchanged.

Q: How does the paper address the potential endogeneity of tax reforms? A: The event study plots show no statistically significant pre-trends before reforms, supporting the parallel trends assumption. The paper also finds no significant correlation between tax reforms and observable oil-sector or macroeconomic variables in the pre-period. Subsamples minimizing lobbying concerns — private (non-national) oil companies, small companies, companies without pre-existing production in the country, and non-OPEC countries — all yield similar estimates, suggesting that large incumbents’ influence over tax-setting does not drive the findings.

Q: How does the paper handle the staggered difference-in-differences design? A: To address potential bias from heterogeneous and dynamic treatment effects in a two-way fixed effects framework, the paper implements a stacked regression following Cengiz et al. (2019), constructing 18 cohort-specific datasets using never-treated countries as controls. The stacked specification yields significant effects on exploration and discoveries and null results on production and extraction costs, consistent with the main estimates. The stacked event study shows no pre-trends.

Q: What is the implicit carbon price of existing production-based oil taxes? A: At the production-weighted average royalty rate of 21% and a reference oil price of $65/bbl, the existing taxes correspond to an indirect carbon price of approximately $32/tCO2, calculated using a CO2 content of 0.43 tCO2/bbl. This figure is an order of magnitude larger than the current global average demand-side carbon price of $3.1/tCO2 (a production-weighted average including zeros for unpriced emissions). This calculation pertains only to downstream combustion emissions and excludes upstream production emissions.

Q: What are the quantified effects of a global 20-percentage-point climate royalty surcharge on emissions? A: In the first five years, the surcharge reduces annual oil-embedded emissions by 0.7–1.0 GtCO2, a 5–7% reduction. By year 2100, annual reductions reach 1.2–2.6 GtCO2, a 9–20% reduction relative to baseline. The cumulative reduction over 2020–2100 is 85–161 GtCO2 (1.0–2.0 GtCO2 per year on average), representing 17–32% of the remaining carbon budget for 1.5°C warming or 7–14% of the budget for 2°C warming. All ranges span demand elasticities of −0.2 to −0.5.

Q: What happens to the global oil price under a global supply-side surcharge? A: The immediate contraction of unconventional oil production raises the oil price by $8–14/bbl in the short term. As new exploration and field development are suppressed over time, the price effect grows, reaching $23–27/bbl by year 2100. This price increase is roughly equivalent to a global carbon price of $53–63/tCO2 levied on oil consumers in the medium term.

Q: How does the paper analyze distributional incidence under the global surcharge? A: A 20-percentage-point surcharge reduces average annual consumer surplus by $500–730 billion and producer surplus by $270–310 billion per year. Tax revenue to oil-producing governments increases by $590–870 billion per year. The net present value of the aggregate economic loss is $1,000–1,400 billion; the policy breaks even in direct welfare terms at a social cost of carbon of $72–84/tCO2. Oil-producing governments are the primary beneficiaries; both consumers and oil companies lose surplus.

Q: What is the carbon leakage rate under an OECD-only supply-side coalition? A: In the short term, leakage is 16–37%, as non-OECD unconventional producers ramp up output in response to the higher oil price. By 2050 the leakage rate rises to 41–70%. By year 2100 the coalition has reduced annual production by 9,000–9,400 million barrels while non-OECD countries have increased theirs by 5,200–7,800 million barrels, implying a terminal leakage rate of 58–82%. The net cumulative global emission reduction of 54–107 GtCO2 represents 47–73% of what the OECD reduction alone achieves, and roughly two-thirds of the global scenario.

Q: Why are the authors’ supply elasticity estimates somewhat larger than the prior literature? A: The authors offer two reasons. First, their approach captures elasticity through changes in exploration activity rather than only production or field development, a broader and more forward-looking margin. Second, they use tax-driven variation in prices rather than market-price variation; the event studies show that tax reforms produce persistent changes in tax rates and after-tax prices throughout the sample, so firms are likely responding to changes perceived as durable, which would naturally elicit larger responses than responses to short-run price fluctuations.

Q: What are the key limitations and scope conditions of the model? A: The quantification omits upstream (well-to-refinery) emissions and natural gas, meaning the estimated climate effects are conservative. The demand curve is held constant over time, abstracting from long-run substitution toward clean energy. The model does not account for depletion of low-cost reserves beyond 80 years. The empirical elasticities are estimated from tax reforms that may have been perceived as temporary, meaning permanent-policy elasticities could be larger, which would imply both larger emission reductions under a global policy and higher leakage rates under a partial coalition.

Q: How do distributional consequences differ between the OECD-only and global scenarios? A: Under the OECD-only surcharge, OECD consumers and OECD producers both lose surplus, while non-OECD producers and governments everywhere gain — non-OECD governments solely through the oil price increase without bearing any tax burden. The sum of OECD producer surplus losses and non-OECD producer surplus gains is slightly negative overall. The aggregate annual global economic loss under the OECD scenario is $120–170 billion, slightly lower than the global scenario ($130–220 billion), because the oil price increase and quantity reduction are both smaller in the OECD case.

Production-based tax (royalty): A tax levied on gross oil production or gross income from oil, not on profit. Unlike profit-based taxes, these are not deductible against costs and therefore create incentives to curtail exploration and production. In the paper’s framework they are equivalent to a supply-side climate instrument because they reduce the after-tax price received by producers.

Climate royalty surcharge: An additional production-based tax, layered on top of existing taxes, proposed as an explicit supply-side climate policy instrument. Following Prest and Stock (2023), the paper defines this as an ad valorem levy on oil production that implicitly prices downstream CO2 emissions through its effect on the after-tax oil price.

Carbon leakage: The offsetting increase in oil production by non-coalition countries in response to an oil price rise caused by a supply-restricting policy adopted by a subset of producers. Measured as the ratio of the production increase in non-coalition countries to the production reduction in coalition countries, expressed as a percentage.

After-tax oil price elasticity of exploration: The percentage change in exploration expenditure per one-percent change in the after-tax oil price, estimated via 2SLS instrumenting the after-tax price with production taxes. The preferred estimate is 1.96, implying elastic exploration responses to tax-driven price changes.

Extraction cost (breakeven price): The constant oil price at which the net present value of developing a field equals zero, computed using a real discount rate of 7.5%. It is the minimum price at which a field is commercially viable absent profit taxes. In the quantitative model, fields are developed if and only if extraction cost falls below the after-tax oil price.

Indirect carbon price: The implicit CO2 price embedded in a production-based oil tax, calculated as the ad valorem royalty rate multiplied by the oil price and divided by the CO2 content of oil. The paper calculates that the existing average 21% royalty at $65/bbl corresponds to an indirect carbon price of approximately $32/tCO2, applicable only to downstream combustion emissions.

Stacked regression (staggered DiD): A robustness approach to two-way fixed effects with staggered treatment timing, constructing cohort-specific datasets for each treatment year using only never-treated units as controls, thereby avoiding contamination from using already-treated units as comparisons for later-treated units.

Racial Disparities in Federal Sentencing: Evidence from Drug Mandatory Minimums

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies racial disparities in federal criminal sentencing by analyzing abnormal bunching in the distribution of crack-cocaine amounts recorded at sentencing. The identifying variation comes from the Fair Sentencing Act (FSA) of 2010, which raised the 10-year mandatory minimum threshold for crack-cocaine from 50 grams to 280 grams. Because the new 280g threshold was set at a point with essentially zero pre-existing bunching, the author implements a difference-in-bunching design (following Kleven 2016) that compares the pre-2010 distribution of charged drug amounts — treated as the counterfactual — to the post-2010 distribution. The primary data are case-level records from the United States Sentencing Commission (USSC) covering all federal drug cases sentenced 1999–2015, restricted to crack-cocaine offenses (approximately 50,273 cases, of which 83.3% involve black defendants, 9.2% Hispanic, and 7.6% white).

The main finding is that after 2010, the fraction of cases charged with amounts in the 280–290g range increases by 3.3 percentage points overall. This increase is disproportionately concentrated among minority defendants: black and Hispanic offenders are more than 2.5 times as likely as white offenders to be charged with 280–290g after the threshold shifts to that level. Approximately 80% of the excess mass at 280g is drawn from cases that had previously been charged in the 50–280g range, indicating that prosecutors are moving cases upward to cross the new threshold rather than negotiating downward from above it. For black and Hispanic offenders specifically, cases from the 50–280g range account for 88% of the increase at the new threshold.

The author rules out differential drug involvement as an explanation. The pre-2010 distributions of charged amounts from 60–280g are nearly identical across racial groups; a Kolmogorov-Smirnov test fails to reject equality (p-value = 0.792). This implies the post-2010 racial disparity in bunching is a conditional disparity — arising not from differences in underlying drug involvement but from differential treatment of similarly situated defendants.

The paper then traces the bunching to prosecutorial discretion specifically. Drug seizure records (NIBRS, DEA STRIDE), survey data on drug use and selling (NSDUH), and state-level conviction records from Florida all show no change in drug quantities or behaviors at the offender or law enforcement level coinciding with the FSA. Critically, there is no bunching at 280g in drug seizure data, pointing to decisions made after arrest. By contrast, case management files from the Executive Office of the US Attorney (EOUSA) show the fraction of cases recorded in the 280–290g range increases by 7.8 percentage points after 2010. Approximately 22–30% of prosecutors (depending on the detection method) are responsible for the rise in 280g cases. Bunching patterns persist across districts and mandatory minimum thresholds for the same prosecutors, indicating it reflects a prosecutor-level characteristic.

The Supreme Court’s 5-4 decision in Alleyne v. United States (June 2013) raised the evidentiary standard for facts that trigger mandatory minimums and shifted that factual determination to juries. The share of EOUSA cases recorded in the 280–290g range fell from 9.1% (2011–2013) to 6.8% (2014–2016) after Alleyne, and a difference-in-discontinuities design confirms that bunching was partially reined in by this decision.

On the question of discrimination, the racial disparity in bunching cannot be explained by observable defendant characteristics — education, sex, age, criminal history, seized drug amount, or other offense elements. Approximately 70% of the disparity persists after controlling for state-by-post fixed effects and 60% after district-by-post fixed effects. The disparity can be largely explained by a state-level measure of racial animus based on Google search data (Stephens-Davidowitz 2014): prosecutors operating in higher-animus states apply more disparate treatment, a pattern consistent with taste-based rather than statistical discrimination.

Cases charged just above the 280g threshold receive longer sentences than those just below it in the post-2010 period, confirming that prosecutorial bunching has real consequences for sentence length.

Q: What is the central empirical strategy of the paper? A: The paper uses a difference-in-bunching design exploiting the Fair Sentencing Act of 2010, which shifted the 10-year mandatory minimum threshold for crack-cocaine from 50g to 280g. Because the 280g point had essentially zero bunching before 2010, the pre-2010 distribution of charged drug amounts serves as an empirical counterfactual for the post-2010 distribution absent the threshold change. The design allows the author to isolate bunching caused by the new threshold and to test whether that bunching is racially disparate.

Q: What is the main quantitative finding on bunching? A: After 2010, offenders sentenced for crack-cocaine are 3.3 percentage points more likely to be charged with amounts in the 280–290g range (Column 1, Table 2). Black and Hispanic offenders are more than 2.5 times as likely as white offenders to be charged with 280–290g after the threshold change (Column 2, Table 2). This racial gap is the central disparity the paper investigates.

Q: Does the racial disparity in bunching reflect genuine differences in drug involvement? A: No. The pre-2010 distributions of charged amounts from 60–280g are nearly identical across racial groups; a Kolmogorov-Smirnov test fails to reject equality with a p-value of 0.792. Because these pre-period distributions are taken as reflecting true drug involvement, their similarity by race implies the post-2010 disparity is a conditional racial disparity — arising from differential treatment of similarly situated defendants, not from differential drug involvement.

Q: Where in the criminal justice process does the bunching originate? A: The bunching originates in prosecutorial decisions, not at the arrest or law enforcement stage. Drug seizure records (NIBRS and DEA STRIDE) show no bunching at 280g, and survey data (NSDUH) show no post-FSA change in drug use or selling by minority defendants. Florida state-level records show no shift in the share of high drug-weight cases. By contrast, EOUSA case management files — which capture quantities recorded by prosecutors — show an increase of 7.8 percentage points in the fraction of cases in the 280–290g range after 2010.

Q: What fraction of prosecutors engage in this bunching behavior? A: Approximately 29.7% of prosecutors have a higher-than-normal percentage of cases at 280–290g after 2010 under a straightforward outlier criterion. Using the outlier detection procedure from Ridgeway and MacDonald (2009), approximately 22% are flagged as outliers. A Bayesian shrinkage method estimates approximately 30% (SE = 0.042) of prosecutors engage in this bunching. The behavior persists across districts and across multiple mandatory minimum thresholds for the same prosecutors, indicating it is a durable prosecutor-level characteristic.

Q: What evidence links the bunching to upward manipulation rather than downward negotiation? A: Approximately 80% of the excess mass at 280g is drawn from cases previously charged in the 50–280g range rather than from cases above 290g. For black and Hispanic offenders the share is 88%. This pattern indicates prosecutors are pushing amounts upward past the new threshold to secure longer sentences, not negotiating amounts downward from above the threshold — reversing the direction assumed in prior qualitative discussions.

Q: What was the effect of Alleyne v. United States on bunching? A: The Supreme Court’s 5-4 decision in Alleyne (June 2013) raised the evidentiary standard for facts triggering mandatory minimums and assigned those factual determinations to juries rather than judges. The share of EOUSA cases in the 280–290g range fell from 9.1% in 2011–2013 to 6.8% in 2014–2016. A difference-in-discontinuities design confirms that bunching expanded in the run-up to Alleyne and was partially curtailed afterward, providing additional evidence that the bunching reflects prosecutorial manipulation rather than genuine drug amounts.

Q: Can observable defendant characteristics explain the racial disparity in bunching? A: No. The racial disparity in bunching persists after controlling for education, sex, age, criminal history, seized drug amount, and other offense elements. Approximately 70% of the disparity remains after controlling for state-by-post fixed effects and 60% after controlling for district-by-post fixed effects. The disparity exists among observably similar defendants, ruling out the hypothesis that it is driven by correlated case characteristics.

Q: What evidence distinguishes taste-based from statistical discrimination? A: The racial disparity in bunching is largely explained by a state-level measure of racial animus constructed from Google search data (Stephens-Davidowitz 2014): prosecutors in higher-animus states apply more racially disparate treatment. Because statistical discrimination would predict disparate outcomes based on informative case characteristics rather than on the ambient racial attitudes of the jurisdiction, the correlation with racial animus is more consistent with taste-based discrimination than with statistical discrimination.

Q: Does bunching at 280g have real consequences for sentence length? A: Yes. Cases charged just above the 280g threshold receive longer sentences than those charged just below it in the post-2010 period, confirming that the mandatory minimum threshold is binding and that prosecutorial bunching translates into materially longer sentences for the affected defendants.

Q: How does this paper contribute relative to Rehavi and Starr (2014)? A: Rehavi and Starr (2014) linked arrest to sentencing records to show black offenders receive harsher sentences, driven by prosecutorial charging of mandatory minimums, but acknowledged that unobserved differences in criminal conduct within offense codes remained a concern. This paper addresses that concern by using the pre-2010 distribution of charged amounts as a counterfactual for drug involvement, documenting near-identical pre-period distributions by race, and tracing the post-FSA disparity through multiple data sources to isolate prosecutorial decisions specifically. The paper also quantifies the fraction of prosecutors involved and tests discrimination mechanisms.

Q: What is the relationship between this paper’s findings and the policy goals of the Fair Sentencing Act? A: The FSA achieved its stated goal of narrowing racial gaps attributable to the crack-powder disparity in mandatory minimum thresholds, and in line with prior work the author confirms a net decline in sentences after 2010. However, the increase in bunching at 280g by prosecutors — disproportionately applied to black and Hispanic defendants — dampened the FSA’s effectiveness. The paper thus documents a strategic response by a subset of prosecutors that partially offset the reform’s intended benefits for minority defendants.

Q: How robust are the main bunching estimates? A: The 3.3 percentage point overall increase and the 2.5x racial disparity are robust to various sample restrictions, inclusion of state fixed effects, time trends, state-specific time trends, offender-level controls, Logit/Probit/Poisson models, wider bunching range definitions (e.g., 280–380g), inclusion of cases with weights coded as a range, and alternative standard error calculations. Including range-coded cases actually exacerbates the estimated degree of bunching and the racial disparity.

Bunching (in this paper’s sense): An excess mass of cases charged with a drug amount at or just above the mandatory minimum threshold, defined operationally as a disproportionate concentration of cases in the 280–290g range relative to the counterfactual distribution. Bunching reflects discretionary upward adjustment of charged amounts by prosecutors to trigger longer mandatory minimum sentences rather than true drug seizure quantities.

Difference-in-bunching design: An empirical strategy adapted from Kleven (2016) that compares the actual post-2010 distribution of charged drug amounts to the pre-2010 distribution as a counterfactual for what the post-2010 distribution would have looked like absent the FSA threshold change. The method exploits the fact that the 280g threshold was a point of essentially zero bunching before 2010.

Conditional racial disparity in bunching: A racial gap in the probability of being charged at 280–290g that remains after conditioning on similar underlying drug involvement, operationalized by the near-identical pre-2010 distributions of charged amounts from 60–280g across racial groups. The conditional disparity isolates differential treatment from differential conduct.

Prosecutorial discretion (in this context): The legal authority of federal prosecutors to determine the drug quantity attributed to a defendant for sentencing purposes, which is not strictly bound to the amount physically seized at arrest. Prosecutors can rely on informant testimony, conspiracy attribution, or approximations to establish amounts above what was seized, giving them effective control over whether the mandatory minimum threshold is crossed.

Taste-based discrimination: Racially disparate prosecutorial behavior that cannot be explained by observable case characteristics or informative statistical inference about defendant conduct, and that correlates instead with ambient state-level racial animus. In this paper’s framing, taste-based discrimination is distinguished from statistical discrimination by its correlation with the Stephens-Davidowitz racial animus measure rather than with defendant or offense characteristics.

Mandatory minimum threshold (in federal crack-cocaine sentencing): A drug quantity cutoff — set at 50g before 2010 and 280g after the FSA — above which federal law mandates a sentence of at least 10 years unless specific departure conditions are met. The threshold creates a sharp discontinuity in expected sentence length that gives prosecutors an incentive to place cases just above it.

State-level racial animus measure: A proxy for the prevalence of racially prejudiced attitudes in a state, constructed by Stephens-Davidowitz (2014) from Google Trends search volume data (2004–2007) for a specific racial slur and its plural, normalized by total search volume. Used here as a predictor of the size of the racial disparity in prosecutorial bunching across states.

Religion, Education, and the State

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies how Indonesia’s Islamic education sector responded to one of the largest state-driven mass schooling expansions in history — the SD INPRES program (Sekolah Dasar Presidential Instruction) launched in 1973 — and whether that program achieved its secular nation-building objectives. The research question is three-part: Did Islamic schools enter or exit markets where the state built more primary schools? How did religious school choice shift across cohorts? And did the program advance secular identity formation among exposed individuals?

The empirical setting is Indonesia in the 1970s onward. Under SD INPRES, the government used windfall oil revenues to build more than 61,000 primary schools between 1973 and 1980, allocating construction across districts proportional to the non-enrolled primary-school-age population. Because Islamic schools were historically more prevalent in underserved areas, this rule produced a strong positive correlation between SD INPRES intensity and pre-existing Islamic school density — the same markets where the state expanded were precisely those with the greatest Islamic education presence.

The authors use several novel data sources: administrative registries covering nearly 220,000 secular and 160,000 Islamic schools with establishment dates; six rounds of the National Socioeconomic Survey (Susenas) from 2012–18; the Indonesia Family Life Survey (IFLS, 1993–2014); a 2018–19 curriculum timetable registry (SIAP) covering nearly 20% of madrasa; and a 2016 political/religious attitudes survey. Identification relies on difference-in-differences (DID) exploiting cross-district variation in SD INPRES intensity, the synthetic DID approach of Arkhangelsky et al. (2021) for robustness to violations of parallel trends, and a staggered village-level event study using the Borusyak et al. (2024) estimator.

The main findings are as follows. First, Islamic schools did not exit markets where the state expanded — they entered in greater numbers. A one standard deviation increase in SD INPRES construction led to 1.4 additional Islamic school entries per district above a mean of 1.9 per district in 1972. Entry was competitive at the primary level, where new madrasa (MI) entered at twice the baseline annual rate in the years immediately following INPRES construction, and strategic at the secondary level, where Islamic junior secondary schools (MTs) peaked 6–9 years after INPRES entry as graduates sought continued education. The Islamic sector financed this expansion through waqf (inalienable religious endowments), informal taxation (infaq, zakat), and revenues from a concurrent rice price spike; entry responses were stronger in villages with above-median waqf endowments and above-median potential rice yields.

Second, rather than converging toward secular curricula, newly established Islamic schools in high-INPRES districts devoted more time to religious content. Each additional SD INPRES is associated with a 1.2 percentage point increase in the religious curriculum share among newly created madrasa, with increases of 1.3 and 2.4 percentage points at the primary and junior secondary levels respectively — the latter equaling 82% of the cross-school standard deviation. Some of this increase came at the expense of Pancasila/civic education and national language instruction.

Third, while SD INPRES reduced Islamic primary school enrollment by roughly 7%, it increased overall Islamic school attendance: each additional SD INPRES increased the likelihood of attending any Islamic school by approximately 5%, as demand for secondary education outweighed substitution at the primary level. Female students exhibited stronger secondary-level demand effects, amplified in districts with a concurrent state ban on the Islamic veil in public schools.

Fourth, SD INPRES did not advance its ideological objectives. In the 1977 and 1982 elections, Golkar’s vote share fell and the Islamic PPP’s rose by 0.5–1.0 percentage points per SD INPRES school in high-INPRES districts. Among exposed cohorts, SD INPRES did not increase Pancasila proficiency, national language use at home, or support for secular governance, but did increase Arabic literacy by approximately 3% per additional SD INPRES. Exposed cohorts also prayed more frequently, fasted more during Ramadan, gave more to charity, and expressed greater pilgrimage intentions. These religious patterns were transmitted to children of exposed cohorts, who were more likely to attend Islamic schools themselves.

Q: What was the allocation rule for SD INPRES and why did it create confrontation with Islamic schools? A: Presidential Instruction No. 10/1973 allocated school construction across districts proportional to the non-enrolled primary-school-age population in 1971. Because Islamic schools historically served underserved populations, this rule meant the state built more schools precisely where Islamic education was most prevalent. The paper shows graphically and in Table 1 that the number of SD INPRES schools built is strongly correlated with the pre-existing stock of Islamic schools, conditional on district population and enrollment.

Q: How large was the Islamic sector’s entry response to SD INPRES at the district level? A: In the standard DID specification (Table 2, panel a), a one standard deviation increase in SD INPRES schools led to 0.013 more Islamic schools per district-year per 1,000 children, equivalent to 1.4 additional Islamic school entries in the average district relative to a mean of 1.9 Islamic schools per district in 1972. The synthetic DID (panel b) delivers positive and slightly larger estimates, indicating the result is not an artifact of diverging pre-trends.

Q: What was the timing of the Islamic sector entry response at the village level? A: Using the Borusyak et al. (2024) estimator on a balanced panel from 1960 to 1999, the paper finds (Figure 4) that INPRES construction is followed by a jump in Islamic school entry. Primary madrasa (MI) entered at twice the baseline annual rate in the years immediately following INPRES construction and this elevated rate persisted for six years before reverting to baseline. Islamic junior secondary entry (MTs) peaked around years 6–9 after SD INPRES construction, consistent with newly graduated primary students seeking continued schooling.

Q: How did the Islamic sector finance its expansion? A: The sector relied on waqf endowments (inalienable religious land assets), informal faith-based contributions (infaq), and obligatory alms (zakat). Fortuitously, the initial year of SD INPRES coincided with a large spike in the global price of rice, Indonesia’s main agricultural commodity, boosting harvest revenues channeled through informal Islamic taxation. Table 3 shows that entry responses were significantly stronger in villages with above-median waqf endowments and above-median potential rice yields, and these heterogeneous effects did not arise in non-INPRES periods or for non-Islamic private schools. Survey data from 2007–13 further show higher rates of informal taxation in villages with Islamic schools built during this period.

Q: Did Islamic schools converge toward secular curricula under competitive pressure from SD INPRES? A: No. Table 4 shows that madrasa established in high-INPRES districts after 1972 devote more time to religious content, not less. Each additional SD INPRES is associated with a 1.2 percentage point increase in the share of classroom time devoted to religious subjects among newly created Islamic schools, with increases of 1.3 percentage points at the primary level and 2.4 percentage points at the junior secondary level — the latter equal to 82% of the cross-school standard deviation. Similar patterns hold for Arabic instruction, and the junior secondary increase comes partially at the expense of Pancasila/civic education and national language instruction.

Q: Did curriculum differentiation responses vary with local religious ideology? A: Yes. Appendix Table A.14 shows a stronger curriculum differentiation response in markets with greater historical support for conservative Islam, proxied by Islamic political party vote shares in the 1950s elections. The paper also constructs a school-name-based predicted ideology index using a ridge shrinkage estimator and finds (Appendix Table A.15) that madrasa entering high-INPRES districts after the program onset have a more religious ideology on this measure.

Q: What happened to the formalization of the Islamic sector? A: Figure 5 and Appendix Table A.6 show that formal madrasa entry increased as a share of all new school entry, while informal Islamic schools (pesantren, diniyah) declined as a share of all new schools and all new Islamic schools. This formalization mirrors the organizational structure of state schools (primary-to-secondary progression), facilitating switching between public and religious schools and providing option value to moderate but still religious families. Crucially, the newly entering formal madrasa introduced more religious curriculum than incumbent madrasa, so formalization did not reduce religious instruction.

Q: What was the net effect of SD INPRES on Islamic school attendance? A: Table 5 shows that SD INPRES reduced the likelihood of attending Islamic primary school by roughly 7% per additional SD INPRES school but increased Islamic secondary attendance, with the net effect being a roughly 5% increase in the likelihood of attending any Islamic school (column 4). This finding holds in both DID and synthetic DID. The IFLS validation (Appendix Table A.18) confirms decreased Islamic elementary attendance and increased Islamic junior secondary attendance, consistent with the Susenas results.

Q: How does selection into secondary education affect the religious schooling results? A: The authors address selection using parametric (Heckman 1976) and semiparametric (Newey 2009) selection-correction procedures, using exposure to a 1960s pilot compulsory schooling program as an exclusion restriction. Table 6, panels (c) and (d), show that selection-adjusted estimates are broadly consistent with unadjusted estimates, with similar signs and magnitudes. The selection-corrected estimates approximately identify a local average treatment effect among compliers: those induced to attend elementary school were less likely to attend Islamic elementary; those induced to continue to secondary were more likely to attend Islamic secondary.

Q: How did gender shape the effects of SD INPRES on religious school choice? A: Table 7 shows that SD INPRES had more limited impacts on total schooling for women than men (consistent with Duflo 2001) but that the secondary-level demand effect toward Islamic schools was stronger for women. Table 8 shows that within high-INPRES areas, the SD INPRES-induced increase in Islamic secondary education is three times larger for women in districts with greater exposure to the 1982 state ban on the Islamic veil in public schools, and this differential is specific to Islamic schooling rather than total schooling.

Q: Did SD INPRES strengthen or weaken the secular ruling regime’s political standing? A: It weakened it. Table 10 shows that in the 1977 and 1982 elections, Golkar’s vote share decreased and the Islamic PPP’s vote share increased in high-INPRES districts, in the range of 0.5–1.0 percentage points per SD INPRES school. This represents a 1.5–3.0% change in PPP vote share and a 0.5–1.0% change in Golkar vote share per standard deviation in SD INPRES intensity. The PPP gained most in areas where SD INPRES had the greatest potential to draw students away from Islamic schools.

Q: Did SD INPRES produce a secular ideological shift among exposed cohorts? A: No. Table 11 shows that SD INPRES did not increase self-reported Pancasila proficiency, national language use at home, national language literacy, or attitudes in favor of secular governance. By contrast, Arabic literacy increased by approximately 3% per additional SD INPRES among exposed cohorts, indicating that Islamic schooling exposure rather than secular schooling drove literacy gains in that language.

Q: Did SD INPRES increase religiosity among exposed cohorts? A: Yes. Table 12 shows that SD INPRES increased prayer frequency, fasting during Ramadan, charitable giving, and pilgrimage intentions among exposed cohorts. These effects on prayer and fasting are stronger among women, consistent with the stronger shift toward Islamic secondary schooling found in Table 7. These outcomes are consistent with greater exposure to Islamic education increasing religiosity rather than the secular curriculum reducing it.

Q: Were the effects on religious identity and Arabic literacy transmitted to the next generation? A: Yes. Table 13 shows that SD INPRES increased Arabic literacy among the children of exposed cohorts, and that children of exposed cohorts were more likely to attend Islamic schools themselves. These intergenerational results confirm that the preference for Islamic education instilled during the SD INPRES era persisted into the next generation rather than converging toward secular norms over time.

Q: What are the key robustness checks for the school entry results? A: Several checks support causal interpretation. The Roth and Rambachan (2022) procedure finds no systematic pre-trends in the standard DID. Historical Podes data from 1980, 1983, 1990, and 1993 confirm the post-1973 increase in Islamic school entry, addressing survival bias in the 2019 registry. Results are robust to allowing differential trends in waqf endowments, Muslim population share, Islamic party vote shares, historical Arab immigration, Islamist insurgency, and Transmigration resettlement. The heterogeneous entry responses by waqf and rice yield do not appear in non-INPRES periods or for non-Islamic schools.

Q: What do the results imply for the political economy of education reform more broadly? A: The paper argues that state capacity to homogenize culture through education is limited when strong non-state actors can mobilize their own resources and provide differentiated alternatives. Rather than crowding out religious schools, state expansion triggered competitive entry, curriculum differentiation, and formalization in the religious sector, producing an equilibrium where both sectors expanded simultaneously with distinct clienteles. The findings imply that the long-run cultural effects of education programs cannot be evaluated without accounting for equilibrium responses by competing non-state providers.

SD INPRES (Sekolah Dasar Presidential Instruction): Indonesia’s 1973 mass public primary school construction program, financed by oil windfalls, which built more than 61,000 elementary schools between 1973 and 1980 by allocating schools to districts proportional to the non-enrolled child population; the program’s explicitly secular nation-building objectives brought it into direct confrontation with the Islamic education sector.

Waqf: Inalienable Islamic religious endowments — of land, agricultural assets, or other property — that under Islamic law can only be used for religious or charitable purposes and cannot be seized or repurposed by the state; in this paper, the pre-existing waqf base in a village serves both as a long-run financing mechanism for Islamic school construction and as an index of Islamic sector organizational capacity.

Madrasa: Formal day Islamic schools operating at the same primary-to-secondary grade levels as secular state schools, teaching standard academic subjects alongside a religious curriculum (including Islamic law, doctrine, ethics, Qur’an, Arabic, and history of the Prophets) that averages 26% of total instruction hours; distinct from the more informal pesantren (boarding schools) and madrasa diniyah (afternoon Qur’anic study schools).

Curriculum differentiation: The strategy by which newly entering madrasa in high-INPRES districts increased the share of classroom time devoted to religious and Arabic instruction rather than converging toward the secular state curriculum; measured as classroom hours devoted to Islamic subjects, Arabic, Pancasila/civic education, and national language instruction from 2018–19 SIAP timetable data.

Pancasila: The official secular nationalist ideology of the Indonesian state, consisting of five principles (monotheism, humanitarianism, national unity, democracy, and social justice) intended to transcend ethnic and religious divisions; SD INPRES sought to transmit Pancasila through civic education and national language instruction as part of its homogenizing nation-building agenda.

Synthetic difference-in-differences (SDID): The Arkhangelsky et al. (2021) estimator used throughout the paper, which reweights and matches pre-INPRES trends in Islamic school construction across high- and low-INPRES exposure districts to deliver estimates more robust than standard DID to violations of parallel trends; applied with a binary treatment indicator (districts above the 51st percentile in INPRES intensity).

Formalization: The documented shift in the composition of the Islamic sector after SD INPRES, whereby formal madrasa (organized along the same grade-level progression as state schools) increased as a share of all new Islamic school entry while informal pesantren and diniyah declined as a share; interpreted as a competitive response that expanded parental option value without sacrificing religious instruction intensity.

Sanctions and the Exchange Rate

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Core Argument

Itskhoki and Mukhin develop a tractable open-economy model with financial market segmentation — in which only the government sector (including state banks and exporting firms) can intermediate cross-border capital flows — to study how trade and financial sanctions affect the nominal exchange rate. Their first main result is a Lerner-symmetry equivalence: sanctions limiting a country’s exports or freezing its foreign assets depreciate the exchange rate, while sanctions limiting imports appreciate it, even though both types of policies have exactly the same effect on real allocations, including household welfare and government fiscal revenues. The mechanism is direct — export sanctions reduce the supply of foreign currency, requiring depreciation to restore market clearing, whereas import sanctions reduce the demand for foreign currency, requiring appreciation — and because real income effects are identical, the exchange rate movement is not informative about effectiveness: one cannot evaluate the effectiveness of sanctions based solely on the dynamics of the exchange rate. Beyond direct trade sanctions, increased precautionary savings in foreign currency also depreciate the exchange rate when they are not offset by the sale of official reserves or financial repression of foreign-currency savings. Applying the calibrated model to Russia’s post-invasion experience, the dynamics of the ruble exchange rate following Russia’s invasion of Ukraine in February 2022 are quantitatively consistent with the combined effects of these forces calibrated to the observed sanctions and government policies; the combined effect from 2.5 years of sanctions corresponds to a permanent decline in consumption of 0.9% in Russia, while the net effect is close to zero for the rest of the world, and the freeze of FX reserves together with import tariffs act as a positive transfer from Russia to the rest of the world while quantity restrictions on exports raise world energy prices and generate global welfare losses.

In depth

Q1. Q: What is the core theoretical result on trade sanctions and the exchange rate?

A: Proposition 1 establishes that permanent sanctions on imports (raising import prices P*_t by τ) are equivalent in their effect on import consumption and welfare to a combination of permanent sanctions on exports (reducing export prices Q*_t by τ) and a partial seizure of foreign assets (reducing F*_0 by τ). Both sets of sanctions produce the same path of reduced import quantities and the same welfare loss. However, sanctions on exports cum foreign-asset seizure are associated with an additional depreciation of the exchange rate by τ percent relative to import sanctions. This equivalence is a manifestation of Lerner (1936) symmetry extended to a dynamic international macro environment.

Q2. Q: What is the intuition for the opposite exchange rate movements under import versus export sanctions?

A: Both kinds of sanctions shrink the country’s feasible import consumption set equivalently in real terms, but they operate through different channels. Export sanctions directly reduce the inflow of foreign currency (export revenues fall), so the exchange rate must depreciate to discourage import demand and bring it in line with the reduced budget. Import sanctions raise the price of foreign goods directly; without an offsetting movement, this would create excess demand for domestic non-tradables. To eliminate the excess demand and leave export revenues partially used, the exchange rate must appreciate. In both cases, the import demand schedule — CF_t = (E_t P*_t / P_t)^{-θ} γ Y_t — pins down the exchange rate that supports the same equilibrium import allocation.

Q3. Q: Does fiscal equivalence also hold, even when the government relies primarily on exports for revenue?

A: Yes. Proposition 1 and the surrounding analysis show that the equivalence result for export and import sanctions extends to the fiscal balance, even when the government relies exclusively on exports for fiscal revenues. The mechanism is a general equilibrium adjustment in the exchange rate: depreciation (under export sanctions) partially ameliorates the impact by increasing the local-currency purchasing power of export revenues, while appreciation (under import sanctions) has the opposite effect. The net fiscal-balance effect of both kinds of sanctions ends up being the same.

Q4. Q: What role does the financial market segmentation assumption play?

A: The paper assumes a form of financial market segmentation in which only the government sector (including state banks and exporting companies) can intermediate capital flows across the border, subject to international restrictions. This captures both the withdrawal of foreign investors from the Russian market and the segmentation of Russian households from the international financial market due to external sanctions and domestic capital controls. Under this structure, exports and FX reserves are the key sources of currency supply to the economy, and imports plus domestic foreign-currency savings are the key sources of currency demand; the equilibrium exchange rate is determined by the balance of these in the domestic market. Ricardian equivalence for foreign-currency savings does not hold when κ > 0 in the household utility function, so government reserve policy has real effects.

Q5. Q: What is the role of precautionary savings demand for foreign currency?

A: Households have foreign-currency bonds in their utility function reflecting a precautionary (hedging) demand for future purchases of foreign tradables, parameterized by a shock Ψ_t. When financial conditions collapse — the local stock market crashes, domestic deposits face inflation and bank-run risk, and access to foreign assets is constrained — Ψ_t rises above the real value of household FX savings, creating pressure to accumulate foreign-currency savings despite low expected returns. With inelastic inflow of foreign currency from exports (due to financial sanctions) and no feasible FX reserve sale, a large jump-depreciation is required to restore equilibrium by curbing the increased demand for foreign currency via lower expected returns and higher import prices. The effect is transitory: it dies out as households accumulate enough FX savings. The optimal government response is to sell FX reserves to accommodate household demand without an exchange rate devaluation.

Q6. Q: What happens when FX interventions are infeasible?

A: When the central bank’s reserves are frozen by sanctions or otherwise unavailable, the government can use financial repression to offset the exchange rate effects of financial shocks. Specifically, by imposing fees on purchasing and withdrawing foreign currency — thereby reducing the household return on foreign-currency deposits R*_H below the international rate R*_t — the central bank can suppress foreign-currency demand. While financial repression is suboptimal in a representative-agent economy, it may be second-best in heterogeneous-agent economies or economies with balance-sheet effects. Importantly, the exchange rate remains allocative even under financial sanctions and financial repression; it is not rendered irrelevant by these policies.

Q7. Q: How do the results change when Russia is modeled as a large economy in the commodity market?

A: Section 3 extends the analysis to an economy that is large in the world commodity market, modeling Russia as a large commodity exporter, and spelling out specific policy instruments. The paper shows that import prices and export revenues still constitute a sufficient statistic for the macroeconomic effects on the economy under sanctions. However, the welfare implications for the rest of the world depend crucially on whether sanctions take the form of trade taxes or quantity restrictions. A price cap on exported commodities can replicate a tax on exports, achieving the desired wealth transfer to the coalition. In contrast, imposing quantity restrictions on a large commodity exporter reduces global supply and drives up world energy prices, hurting the sanctioned economy when it lowers export revenues, but also imposing substantial costs on senders.

Q8. Q: How does the paper calibrate the model to Russia’s ruble dynamics, and how well does it fit?

A: The paper employs two calibration strategies. The first reproduces the ex-ante calibration from the 2022 working paper version based on scant data available in the first months after the invasion, without targeting any exchange rate moments. This calibration provides a remarkable out-of-sample fit, predicting accurately the dynamics of the ruble in the following two years. The second is an ex-post calibration that infers structural shocks to perfectly match observed dynamics of Russian imports, exports, commodity prices, domestic output, official FX reserves, inflation, and the exchange rate. Both approaches agree on the decomposition of exchange rate dynamics and confirm the quantitative importance of the theoretical mechanisms.

Q9. Q: What does the calibrated decomposition say about the phases of ruble dynamics?

A: The initial sharp depreciation in the first weeks after the invasion is mostly driven by increased precautionary demand for foreign currency. The frozen FX assets translate into modest losses of permanent income (only about 3% depreciation), but the asset freeze and sanctions on the Central Bank had a much larger indirect effect by limiting the capacity to accommodate the financial shock with FX interventions. One month out, trade shocks begin to dominate: import restrictions curb FX demand, while the spike in energy prices elevated Russian export revenues, increasing foreign-currency inflows. These forces combined neutralize capital outflows and the surge in financial FX demand, explaining the sharp appreciation of the ruble by summer 2022 (about 30% stronger than pre-war by June). Over time, import quantities recovered as parallel imports and new trade linkages were established, and export revenue inflows contracted as commodity prices declined, bringing the exchange rate back to and then about 20% weaker than pre-war levels.

Q10. Q: What are the welfare and fiscal consequences quantified by the calibrated model?

A: The initial exchange rate depreciation boosted fiscal revenues by 12%, amplified further by greater export revenues starting in the second month. These effects were offset in the medium run by the exchange rate appreciation due to trade sanctions, with net real income turning negative starting from April 2022. International sanctions decrease long-run real government revenues by about 4%, mostly due to a reduction in export revenues. The combined effect from 2.5 years of sanctions corresponds to a permanent decline in consumption of 0.9% in Russia — vastly larger than conventional estimates of the cost of a business cycle — and close to zero on net for the rest of the world. Consistent with the theoretical results, the freeze of FX reserves and import tariffs act as a positive transfer from Russia to the rest of the world, while quantity restrictions on exports result in higher energy prices, lower consumption, and global welfare losses.

Q11. Q: Why cannot the exchange rate be used to evaluate the effectiveness of sanctions in real time?

A: Because import sanctions and export sanctions generate opposite exchange rate movements while having exactly the same effect on real allocations, welfare, and fiscal balance, there is no one-to-one mapping between the exchange rate and welfare under sanctions. A strong exchange rate (appreciation) after sanctions may reflect import restrictions — which are just as effective in reducing real income as export restrictions that would have caused depreciation. Conversely, a weak exchange rate need not imply sanctions are ineffective; it may simply reflect that sanctions took the form of export or asset-freeze measures. The ruble’s rapid appreciation through summer 2022 illustrates this: rather than indicating that sanctions failed, it was largely consistent with the combination of import restrictions and high commodity prices, while the underlying real income effect was substantially negative.

Key Concepts

Lerner symmetry (macroeconomic version): The principle, originating in Lerner (1936), that a uniform import tariff and a uniform export tax yield the same real economic outcomes — the same allocation and welfare — but are sustained by a differential movement in relative prices (appreciation versus depreciation). In the paper’s context, both import and export sanctions of equivalent magnitude reduce the real income of the sanctioned economy by the same amount and produce the same path of import consumption and welfare, even though they move the exchange rate in opposite directions.

Financial market segmentation: The model’s departure from standard international macro in which only the government sector (including state banks and exporting companies) can intermediate cross-border capital flows, subject to international restrictions. Households cannot freely access international financial markets. This makes exports and FX reserves the only sources of foreign-currency supply to the domestic economy, and imports plus domestic foreign-currency savings the only sources of demand, so the exchange rate is determined entirely by the domestic balance of these flows.

Precautionary foreign-currency demand shock (Ψ_t): A shock that raises the household bliss-point for real foreign-currency bond holdings above the current stock, capturing a collapse in the supply of alternative savings vehicles (domestic stocks, bank deposits, access to foreign assets). In the model it enters households’ utility directly; an increase in Ψ_t above real FX savings creates depreciatory pressure on the exchange rate when not offset by FX reserve sales or financial repression.

Financial repression (in the model): Government suppression of the household rate of return on foreign-currency deposits R*_H below the international rate R*_t, implemented via fees on purchasing and withdrawing foreign currency. It offsets the depreciatory effect of a precautionary savings shock without requiring FX reserve sales, at the cost of a distortion in the domestic financial market. The paper notes Russia introduced such fees in March–April 2022.

Sufficient statistic for macroeconomic effects: When the sanctioned economy is large (as Russia is in global energy markets), import prices and export revenues still constitute a sufficient statistic for the macroeconomic effects of sanctions on the economy — i.e., the same pair of variables summarizes welfare, fiscal, and exchange rate outcomes regardless of the specific instrument used to impose sanctions, provided the terms of trade deterioration is the same.

Price cap (as an export tax equivalent): A price cap on a sanctioned country’s exported commodities can replicate the effect of a tax on exports from the coalition’s perspective, achieving the same real-income transfer from the sanctioned country to the rest of the world without reducing global supply (as quantity restrictions do). This distinguishes it from quantity restrictions on exports, which reduce global energy supply and impose welfare costs on the coalition.

Summary based on LSE Research Online accepted version. AI-assisted, human review pending.

School Choice and the Housing Market

Mon, 01 Jan 0001 00:00:00 +0000

Grigoryan (2021) develops a unified general-equilibrium framework that jointly models school assignment mechanisms and the housing market to evaluate the welfare and distributional consequences of replacing traditional neighborhood assignment (NA) with the Deferred Acceptance (DA) mechanism. The paper fills a gap in the matching theory literature, where preferences and priorities are typically treated as exogenous, by making residential choices endogenous: families first observe which school assignment mechanism the district announces, then optimally select a neighborhood given market-clearing prices and other families’ choices, and finally children are assigned to schools through the announced mechanism.

The model features a continuum of families, each with a type defined by valuations over all neighborhood–school pairs, a finite set of neighborhoods and schools (one school per neighborhood), and competitive equilibrium prices. Three mechanisms are compared: NA (each child attends the neighborhood school), DA without neighborhood priority (DA), and DA with neighborhood priority (DN), where neighborhood residents receive priority at their local school.

The paper’s first major result (Theorem 3) is that DN unambiguously generates weakly higher aggregate welfare than NA. The proof exploits the fact that DN preserves NA’s option — families can still guarantee admission to the neighborhood school by living there — while additionally allowing families to access seats at other schools that go unclaimed by neighborhood residents. Although price effects under DN can make some individual families worse off relative to NA, aggregate welfare (inclusive of house sellers) is always weakly higher under DN. In simulations with 1,000 students, 10 neighborhoods, and 10 schools, DN yields average aggregate welfare gains of 2.40% relative to NA across the 18 parameter configurations studied.

The welfare comparison between DA (without neighborhood priority) and NA is ambiguous in the general model: simulations show DA producing gains as large as +5.65% and losses as large as −18.26% relative to NA, depending on the degree of preference alignment across families (parameter α) and the variance in school capacities (parameter γ). DN also dominates DA in aggregate welfare under two sufficient conditions — identical ordinal preference rankings over neighborhoods and schools (Assumption 1 or 2) — though counterexamples exist when these assumptions fail.

The second major result (Theorem 5, Corollaries 1–2) concerns the welfare of lowest-income families, defined as those with budget (maximum willingness to pay for housing) equal to zero or sufficiently close to zero. Under two jointly sufficient conditions — (1) neighborhoods that are underdemanded (zero-priced) under NA remain underdemanded under DA/DN, and (2) the schools in those underdemanded neighborhoods are themselves underdemanded — both DA and DN generate weakly higher welfare for the lowest-income families than NA. These conditions hold whenever families share common ordinal preference rankings (Corollary 1) and in the uniform economy where each valuation profile is equally likely (Corollary 2). The conditions are shown to be approximately necessary in a robustness sense (Theorem 6): for any economy violating them, an arbitrarily close economy exists in which a positive measure of zero-income families prefer NA. In simulations, DN raises lowest-income welfare by an average of 26.51% and DA by an average of 38.25% relative to NA.

The paper also proves existence of a competitive equilibrium for the continuum economy under DA and DN via the Schauder-Tychonoff fixed-point theorem (Theorem 2), exploiting the continuity of school assignment probabilities in families’ neighborhood choices. In discrete economies, assignment externalities can preclude equilibrium existence, but approximate equilibria exist in sufficiently large discrete markets and all welfare comparisons carry over approximately. The existence proof technique applies to general assignment games with externalities including peer preferences and complementarities.

Scope conditions: results are derived for a model without direct peer externalities or endogenous school quality; a supplementary extension to local public financing finds that the aggregate welfare superiority of DA over NA may not survive when school spending is capitalized into housing prices, though the lowest-income welfare sufficiency conditions of Theorem 5 do extend to that environment.

Q: What is the core research question and why does the housing market matter for evaluating school choice?

A: The paper asks how replacing neighborhood assignment with the Deferred Acceptance mechanism affects aggregate welfare and the welfare of the lowest-income families, accounting for the fact that families choose where to live in response to the school assignment mechanism. The housing market matters because under neighborhood assignment families can guarantee enrollment at a preferred school by purchasing a house in that school’s neighborhood; switching to DA changes these strategic incentives, alters equilibrium prices, and therefore changes who ends up in which neighborhood before any school assignment takes place. Ignoring residential choices would miss this feedback loop between assignment rules and housing demand.

Q: What are the three mechanisms compared, and how do they differ?

A: Neighborhood assignment (NA) assigns each child to the school in their neighborhood with certainty. DA without neighborhood priority allocates seats by student preference rankings and lottery numbers, with market-clearing cutoffs determined iteratively; no residential location confers a priority advantage. DN (DA with neighborhood priority) works like DA but grants neighborhood residents a priority of 1 at their local school and 0 at all other schools, effectively guaranteeing neighborhood families a seat at their local school while filling remaining seats by lottery among non-neighborhood applicants.

Q: What does Theorem 3 establish, and what is the intuition for why DN dominates NA in aggregate welfare?

A: Theorem 3 establishes that for any competitive equilibrium under DN and any competitive equilibrium under NA, aggregate welfare is weakly higher under DN. The intuition is that DN preserves all options available under NA — a family can always choose the neighborhood corresponding to its most-valued school and be guaranteed admission there — while additionally providing access to seats at other schools not claimed by their own neighborhood residents. The proof maps DN’s CE onto a Walrasian equilibrium of a continuum assignment game and invokes the welfare-maximization property of such equilibria from Gretsky, Ostroy, and Zame (1992).

Q: Why is the welfare comparison between DA and NA ambiguous?

A: Under NA, families with the highest cardinal valuations for a particular school can guarantee admission by purchasing a house in that neighborhood, and this targeted sorting can raise aggregate welfare when preferences over schools are strongly aligned. Under DA (without neighborhood priority), no location guarantees school admission, so families lose this signaling device; but DA allows families to live in preferred neighborhoods without sacrificing school quality, which raises welfare when preferences are heterogeneous. Neither effect dominates in general: in simulations, DA ranges from −18.26% to +5.65% relative to NA across the parameter space.

Q: What role do neighborhood priorities play as a “signaling device,” and when does DN dominate DA?

A: Neighborhood priorities allow families to credibly signal high valuations for a school by choosing to live in that school’s neighborhood, analogously to signaling devices in matching markets without money. When families have identical ordinal preference rankings over neighborhoods and schools (Assumptions 1 or 2), DN generates weakly higher aggregate welfare than DA because any DA assignment probability can be replicated under DN by mixing over neighborhoods, but the converse is not true. Counterexamples exist when preference rankings differ across families, so the DN-over-DA dominance is not universal.

Q: What are the sufficient conditions for lowest-income families to prefer DA/DN to NA, and how tight are they?

A: The two joint conditions are: (1) neighborhoods that have zero price (are underdemanded) under NA also have zero price under DA or DN after the mechanism switch; and (2) the schools located in those underdemanded neighborhoods are themselves underdemanded (have zero admission cutoffs) under DA/DN. Condition (1) reflects that the poorest neighborhoods are unlikely to become highly sought-after merely because the assignment mechanism changed. Condition (2) is consistent with the empirical finding of Owens and Candipan (2019) that in large US metropolitan areas the poorest neighborhoods typically have underperforming schools. Theorem 6 shows these conditions are approximately necessary: any economy violating them is arbitrarily close to one where a positive measure of zero-budget families prefer NA, so robustness requires them.

Q: What do the simulations show about the magnitude of welfare effects for lowest-income families?

A: In simulations with 10 lowest-income families (budgets of 0.05) among 1,000 total, DN raises lowest-income welfare by an average of 26.51% relative to NA and DA raises it by an average of 38.25% relative to NA, across the 18 parameter configurations. The gains are larger when preferences for neighborhoods and schools are less correlated (lower α) and when school capacities are more uniform (higher γ). DA consistently outperforms DN for lowest-income families in the simulations, even though DN dominates NA in aggregate welfare more reliably.

Q: How does the paper handle equilibrium existence given the externalities created by residential choices?

A: Because a family’s expected utility from a neighborhood depends on other families’ neighborhood choices (through their effect on school assignment probabilities), standard existence results for assignment games do not directly apply. For the continuum economy, the author proves that school assignment probabilities under DA/DN are equicontinuous in families’ neighborhood choices, which enables application of the Schauder-Tychonoff fixed-point theorem to guarantee the existence of a competitive equilibrium (Theorem 2). In finite discrete economies, assignment externalities can prevent equilibrium existence (illustrated by an example in Appendix B), but approximate equilibria exist for sufficiently large discrete markets, and all welfare comparisons hold approximately.

Q: How does the paper’s model relate to and extend prior theoretical work on school choice and welfare?

A: Prior theoretical work (e.g., Calsamiglia et al. 2015; Xu 2019; Avery and Pathak 2020) uses stylized models with single-parameter family types, identical ordinal school rankings, supermodular valuations, and no preferences over neighborhoods. This paper allows an unrestricted preference domain — families have arbitrary valuations over all neighborhood–school pairs — which generates novel findings: in the general model, lowest-income families do not necessarily benefit from DA (contrary to Calsamiglia et al. and Xu), aggregate welfare comparisons between DA and NA are ambiguous (whereas they are trivially resolved in the special cases of prior work), and neighborhood priorities can be welfare-improving even relative to DA without priorities.

Q: Does the paper address the extension to endogenous school quality or local public financing?

A: In Supplementary Appendix B, the model is extended to allow school spending to be financed by local property taxes, making school quality endogenous to neighborhood housing values. In that environment, the aggregate welfare superiority of DA/DN over NA may not hold: DA attracts non-neighborhood applicants to high-priced neighborhoods, and if those schools are a poor match for those applicants absent the spending, social welfare may fall — a result analogous to Barseghyan et al. (2013). However, the paper reports that the sufficiency conditions for lowest-income family welfare comparisons (Theorem 5) do extend to the local public financing environment, preserving the distributional results.

Q: What does the paper say about alternative mechanisms such as Immediate Acceptance (Boston mechanism) and Top Trading Cycles?

A: The Supplementary Appendix studies these alternatives. For Immediate Acceptance (IA), the paper shows that when there are neighborhood priorities, lowest-income families may prefer DA to IA, echoing the finding that IA is not strategyproof and may disproportionately hurt low-income families who are worse at gaming the system or have worse outside options (Pathak and Sonmez 2008; Calsamiglia et al. 2015). Top Trading Cycles and further extensions are also analyzed in the Supplementary Appendix, though detailed results are not developed in the main text.

Neighborhood Assignment (NA): The baseline mechanism under which each family’s child is automatically enrolled in the school located in their chosen residential neighborhood, with no option to attend schools outside that neighborhood.

Deferred Acceptance without Neighborhood Priority (DA): A strategyproof centralized assignment mechanism in which seats are allocated by families’ stated preference rankings and lottery numbers via market-clearing admission cutoffs; residential location confers no priority advantage at any school.

Deferred Acceptance with Neighborhood Priority (DN): A version of DA in which families residing in a neighborhood receive priority 1 at their neighborhood school and priority 0 at all other schools, guaranteeing neighborhood residents a seat at their local school before remaining seats are allocated by lottery to non-neighborhood applicants.

Competitive Equilibrium (CE): A pair of neighborhood choices and a price vector such that (1) each family optimally selects the neighborhood maximizing expected utility net of price (subject to budget), (2) neighborhood capacities are not exceeded, and (3) neighborhoods with excess capacity are priced at zero.

Underdemanded Neighborhood/School: A neighborhood whose equilibrium price is zero (excess housing supply) or a school whose admission cutoff is zero (excess capacity), meaning any applicant who lists it can gain admission.

Assignment Externality: The indirect dependence of a family’s expected utility on other families’ neighborhood choices, which operates through the effect of the population distribution across neighborhoods on the family’s school assignment probabilities under DA or DN. This externality can preclude competitive equilibrium existence in discrete economies.

Aggregate Welfare: The utilitarian sum of all families’ expected utilities from their neighborhood–school assignments, not netting out neighborhood prices (so it includes the welfare of house sellers as passive agents); the comparison criterion for Theorems 3 and 4.

Signaling Device (neighborhood priority as): The interpretation that neighborhood priorities allow families to credibly reveal high valuations for a school by choosing to live in that school’s neighborhood, analogously to signaling instruments in matching markets without monetary transfers; the mechanism through which DN can improve welfare relative to DA.

Selection in Surveys: Using Randomized Incentives to Detect and Account for Nonresponse Bias

Mon, 01 Jan 0001 00:00:00 +0000

This paper addresses nonresponse bias in surveys — the distortion that arises when survey participants differ systematically from nonparticipants in ways that correlate with the survey’s outcomes of interest. The authors develop and apply methods to detect and correct for nonresponse bias using randomized financial incentives embedded in the survey design itself.

The empirical application is the “Norge i Koronatid” (NiK) survey, conducted by Statistics Norway in April–May 2020 to study the immediate labor market consequences of Norway’s COVID-19 lockdown. The NiK survey has two features that make it unusually well-suited for studying nonresponse bias: (1) it is linked to full-population administrative data, providing a verifiable ground truth for the entire Norwegian adult population; and (2) survey invitees were randomly assigned to one of five financial incentive levels (0%, 1%, 5%, 7%, or 10% probability of receiving a 1,000 NOK prepaid card), generating exogenous variation in participation rates. The final sample of 10,000 randomly drawn adults achieved a 47.4% participation rate.

The administrative data reveal large, statistically significant nonresponse bias across all six labor market outcomes examined. Participants in the high-incentive arm had on average roughly 930 USD (30%) higher monthly pre-lockdown earnings than the full population, and were 10.8 percentage points (19%) more likely to be employed. Standard corrections for selection on observable characteristics — including propensity-score reweighting on age, gender, immigration status, schooling, and municipality-level variables — fail to eliminate this bias. For the high-incentive arm, reweighting on individual characteristics more than doubles the nonresponse bias for earnings loss and employment loss measures relative to unweighted estimates, meaning that observable-based corrections can make things worse, not better.

A key finding is that higher participation rates do not imply lower nonresponse bias. The high-incentive arm, with the highest response rate, exhibited larger nonresponse bias than the no-incentive arm. Marginal participants — those induced to respond by higher incentives — had much stronger pre-lockdown labor market attachment (average earnings of 6,806 USD/month vs. 3,666 USD/month for inframarginal participants) but suffered substantially greater lockdown impacts: 32.3% became furloughed or unemployed versus only 3.4% of inframarginal participants.

Existing methods designed to handle selection on unobservables also perform poorly. Worst-case (Manski) bounds contain the truth but are very wide: employment before lockdown is bounded between 30% and 83% against a true value of 57%. Monotone response selection assumptions produce bounds that do not contain the population quantities for any of the six outcomes, because the marginal survey response function is empirically non-monotone. A Heckman parametric selection model produces point estimates inconsistent with the ground truth (e.g., estimating 51% pre-lockdown employment against the true 57%).

Investigation of participation timing reveals that reminder emails attract a qualitatively different type of respondent than incentives do. This motivates the paper’s central methodological contribution: a two-dimensional participation model that distinguishes “active” nonparticipants (those who received the invitation and chose not to respond because the incentive was insufficient) from “passive” nonparticipants (those who never received or attended to the invitation but who may respond to reminders). These two groups have labor market outcomes that differ from participants in opposite directions, which is why single-dimensional monotone selection models fail. The two-dimensional model, exploiting both incentive randomization and the timing of responses, produces bounds that contain or are closer to the ground truth than all other methods examined — for example, bounding pre-lockdown employment at [48%, 63%] around the true value of 57%.

The paper is scoped to a high-quality, randomly sampled, administrative-data-linked survey conducted during a period of acute economic disruption. The authors note the patterns observed may differ outside crisis periods, though the methods developed apply generally.

Q: How prevalent is nonresponse bias discussion in economics research, and what methods do researchers currently use? A: A systematic review of survey-based papers in top-five economics journals from January 2015 to August 2020 found that nearly half of studies omit any discussion of nonresponse bias despite often high nonresponse rates. Among studies using researcher-collected survey data, the average nonresponse rate is 50%; rates reach as high as 87%. When researchers do address nonresponse, 47% of own-survey papers compare sample means to a reference population and 16% apply reweighting on observables; virtually none use methods that address selection on unobservables.

Q: How was the NiK survey designed to enable testing for nonresponse bias? A: The 10,000-person random sample was assigned to five incentive groups with probabilities of receiving a 1,000 NOK credit card set at 0%, 1%, 5%, 7%, and 10%, yielding expected payoffs ranging from 1.1 USD to 11 USD. Because group assignment was random, the groups are probabilistically identical ex ante, so differences in average responses across groups — given an exclusion restriction that incentives do not directly affect answers — provide a direct test for nonresponse bias. Participation rates across the aggregated no/low/high incentive groups were 45.7%, approximately 47.6%, and approximately 51.7%, respectively; the joint test of equal participation across groups rejects with p-value < 0.01.

Q: How large is nonresponse bias in the NiK survey as measured against the administrative ground truth? A: Across all six administrative outcomes and all three incentive arms, joint tests of no nonresponse bias are rejected with p-values < 0.01. High-incentive arm participants had pre-lockdown monthly earnings roughly 930 USD (30%) above the population mean, and were 10.8 percentage points (19%) more likely to be employed. The high-incentive arm’s estimated post-lockdown employment rate of 58% overstates the true rate by 8 percentage points; a researcher comparing this to the true pre-lockdown rate of 57% would erroneously conclude employment was essentially unchanged, when in fact it dropped 7 percentage points.

Q: Does correcting for observable characteristics remove nonresponse bias? A: No. After reweighting by propensity scores constructed from age, gender, immigration status, schooling, and municipality or individual-level characteristics, joint tests of zero remaining nonresponse bias are rejected with p-values < 0.01 for each specification and incentive arm. In some cases, reweighting on individual characteristics more than doubles the nonresponse bias — for example, for earnings loss and employment loss measures in the high-incentive arm — meaning that standard observable-based corrections can amplify rather than reduce bias. Robustness checks using machine learning algorithms, class weights, imputation, and richer covariate sets including lagged outcomes yield the same conclusion.

Q: Does nonresponse bias in survey responses (not just administrative outcomes) differ across incentive arms? A: Yes. For survey-elicited outcomes, average responses differ significantly across incentive arms, with all joint equality tests rejected at p < 0.1. For example, 10.4% of high-incentive participants reported applying for UI benefits versus 7.5% in the no-incentive group. Estimated UI expenditure as a share of Norway’s 2020 social insurance budget varies from 13.2% (no-incentive arm) to 18.4% (high-incentive arm), illustrating the policy stakes.

Q: Do higher response rates reduce nonresponse bias? A: Not in this survey. The no-incentive arm, with the lowest participation rate (45.7%), exhibits smaller nonresponse bias than the high-incentive arm (51.7% participation). This finding contradicts standard guidance from the U.S. Office of Management and Budget and J-PAL research guidelines, which equate higher response rates with lower bias risk. The authors note that J-PAL has subsequently updated its guidance in response to this paper’s findings.

Q: How do marginal participants (induced by higher incentives) differ from inframarginal participants? A: Marginal participants — those who participate only under high incentives but not without them — had average pre-lockdown monthly earnings of 6,806 USD versus 3,666 USD for inframarginal participants (p-value 0.08), indicating much stronger pre-lockdown labor market attachment. Post-lockdown, both groups had similar earnings (approximately 3,600–3,800 USD/month). Consistent with this, 32.3% of marginal participants became furloughed or unemployed after the lockdown versus 3.4% of inframarginal participants. Notably, marginal and inframarginal participants do not differ significantly on observable background characteristics (age, gender, immigrant status, schooling; joint test p-value 0.70), confirming that selection is on unobservables.

Q: Why do existing methods designed to handle selection on unobservables fail? A: Worst-case (Manski) bounds contain the truth but are too wide to be informative — pre-lockdown employment is bounded at [30%, 83%] against a true value of 57%. Adding randomized incentives as instruments tightens bounds only modestly (8.5% width reduction for employment before lockdown). Monotone response selection assumptions fail because the empirically estimated marginal survey response function is non-monotone: for employment, the probability first decreases and then increases as a function of willingness-to-participate. The Heckman parametric selection model gives point estimates inconsistent with the ground truth for most outcomes (e.g., 51% estimated pre-lockdown employment vs. 57% true).

Q: What motivates the two-dimensional participation model? A: Analysis of participation timing shows that reminder emails attract a qualitatively different type of respondent than incentives alone. Reminders have a larger proportional effect on participation in the no-incentive group than in the high-incentive group, both in absolute and proportional terms. Early respondents (responding to initial contact) had lower pre-lockdown earnings and employment than late respondents (responding to reminders). This implies that the two types of unobservables — resistance to incentive and probability of receiving the invitation — are associated with outcomes that move in opposite directions, producing a non-monotone marginal survey response function that single-dimensional models cannot capture.

Q: How does the two-dimensional model work and what are its results? A: The model distinguishes active nonparticipants (saw the invitation, declined because the incentive was too low — more likely to be employed and higher earners) from passive nonparticipants (did not receive or attend to the invitation — more likely to have been adversely affected by the lockdown). By exploiting both the randomized incentive variation and the timing of responses (initial contact vs. reminder), the model partially identifies population mean outcomes under shape restrictions on the joint distribution of the two unobservables. For pre-lockdown employment, the model produces bounds of [48%, 63%] bracketing the true value of 57%, compared to worst-case bounds of [34%, 83%] and monotone selection bounds that do not contain the truth. Improvements are largest for pre-lockdown levels outcomes where the two types of nonparticipants differ most.

Q: What are the practical recommendations for survey researchers? A: Embedding randomized incentives in surveys at little or no additional cost enables an inexpensive test for nonresponse bias that does not require linked administrative data. When such a test detects bias, researchers should apply the two-dimensional model rather than relying on observable-based reweighting or conventional selection models. The question of who participates matters at least as much as how many participate; surveys should be designed to characterize and correct for selection, not merely to maximize response rates.

Nonresponse bias: The difference between the mean response among survey participants and the true population mean, arising when the decision to participate is correlated with the outcome of interest. Distinct from sampling bias; it persists even with a randomly drawn sample.

Selection on unobservables: Nonresponse bias that remains after conditioning on all observed characteristics. In the NiK survey, marginal and inframarginal participants are indistinguishable on observable demographics but differ dramatically in labor market outcomes, providing direct evidence that unobservables drive selection.

Marginal vs. inframarginal participants: Under the Imbens-Angrist monotonicity condition, inframarginal participants would respond at any incentive level; marginal participants respond only at higher incentive levels. Their average responses are separately identified using an IV regression with the incentive as instrument.

Marginal survey response (MSR): The function m(u) = E[Y*_i | U_i = u], giving the average outcome for individuals at the uth quantile of willingness to participate. The MSR is nonparametrically identified for u in [0, p(z_high)]; its empirically non-monotone shape in the NiK data explains why monotone selection assumptions produce bounds that miss the ground truth.

Active vs. passive nonparticipants: Active nonparticipants received the survey invitation and declined because the incentive was insufficient; they tend to have higher labor market attachment. Passive nonparticipants never received or attended to the invitation but may respond to reminders; they tend to have been more adversely affected by the lockdown. This distinction motivates the two-dimensional model.

Two-dimensional participation model: A model of survey participation with two unobservables — resistance to incentive (determining active nonresponse) and probability of receiving the invitation (determining passive nonresponse). By exploiting both incentive randomization and the timing of responses (initial contact vs. reminder), the model produces bounds or point estimates on population means that are narrower and closer to ground truth than single-dimensional alternatives.

Exclusion restriction for incentives: The assumption that randomly assigned incentives affect participation rates but do not directly affect participants’ answers to survey questions. This is required for incentives to serve as valid instruments for testing and correcting nonresponse bias; the authors test and find no evidence that it is violated.

Should Monetary Policy Care about Redistribution? Optimal Monetary and Fiscal Policy with Heterogeneous Agents

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question. Should monetary policy deviate from price stability to address redistributive concerns in an economy with heterogeneous agents? The paper jointly solves for optimal monetary and fiscal policy under commitment in a Heterogeneous Agent New Keynesian (HANK) environment with incomplete insurance markets for idiosyncratic risk, nominal frictions (Rotemberg price adjustment costs), and aggregate technology shocks.

Framework. The model is a Bewley-style incomplete-markets economy populated by a continuum of agents who differ in their idiosyncratic labor productivity histories. Agents save in two assets — nominal public debt and real capital shares — and face nominal borrowing constraints. Intermediate firms operate under monopolistic competition and face quadratic price adjustment costs. The government has up to five fiscal instruments: linear taxes on real capital income, on nominal asset income, and on labor income; lump-sum transfers; and one-period public nominal debt. Monetary policy controls the path of the nominal interest rate, and thereby inflation.

Three fiscal regimes are analyzed:

Regime 1 — Full optimal fiscal policy. When both capital taxes (on real and nominal asset returns) and a labor tax are freely optimizable and time-varying, the paper proves analytically (Proposition 1) that optimal monetary policy implements exact price stability at all periods. The intuition is that linear capital taxes replicate all direct redistributive channels of inflation (return effects and Fisher effects), while the labor tax replicates all indirect general-equilibrium channels (real wage effects). Hence fiscal tools are sufficient substitutes for any redistributive role of inflation, and the Rotemberg price-adjustment loss makes any deviation from zero inflation strictly costly. This equivalence result extends Correia et al. (2008) to environments with heterogeneous asset holdings, capital, and both real and nominal assets.

Regime 2 — Exogenous fiscal rules (constant or modestly time-varying taxes). Using a standard quarterly calibration for the US (capital tax 36%, labor tax 28%, transfers 8% of GDP; Frisch elasticity 0.5; price adjustment cost κ=100; TFP shock persistence 0.95, standard deviation 0.31% per quarter; wealth Gini 0.73), the paper solves for optimal inflation dynamics numerically via a “timeless perspective” — i.e., around the long-run equilibrium. Under Fiscal Rule 1 (constant marginal tax rates, debt-stabilizing transfer rule), the maximum change in the inflation rate following a one-standard-deviation negative TFP shock is 0.01%, and the annualized standard deviation of inflation is 0.020%. Under Fiscal Rule 2 (labor tax falls by 0.2 percentage points on impact from 28% to 27.8%, capital tax rises by 0.2 percentage points from 36% to 36.2%), inflation volatility is slightly lower and aggregate consumption volatility is also reduced, confirming that even simple time-varying fiscal rules dominate optimal inflation as an insurance device. The aggregate welfare gain from implementing optimal inflation relative to constant inflation (Π=1) is 0.002% in consumption-equivalent terms, with the gain concentrated among low-productivity agents (up to 0.01%), while high-productivity agents who can self-insure experience a near-zero gain.

Regime 3 — Constrained-optimal fiscal policy. Holding the capital tax constant while optimizing over the labor tax (or vice versa), and calibrating Pareto weights via an inverse-optimal-taxation approach to match the observed US steady-state fiscal system, the paper finds that optimal inflation volatility remains small at a standard deviation of 0.01%, again confirming the dominance of fiscal over monetary instruments for redistribution.

Robustness. A simple two-agent economy calibrated closer to Bhandari et al. (2021b) — with a steeper Phillips curve (κ=20, slope ~6%), higher IES (1/σ=1/2), and highly unequal profit distribution (parameter ν=10 so high-productivity agents receive nearly all profits) — generates an inflation response on impact of 0.17%. Introducing a countercyclical fiscal rule (even a simple one) in this more volatile calibration reduces optimal inflation volatility by one order of magnitude, from 0.68% to 0.07%, and the on-impact response from 0.15% to less than 0.01%.

Methodological contribution. The analysis relies on two innovations: (i) a Lagrangian approach adapted from Marcet and Marimon (2019) that introduces the concept of “net social value of liquidity” for each agent, greatly simplifying first-order conditions; and (ii) a truncation method (LeGrand and Ragot 2022a,c) that represents incomplete-market heterogeneity by grouping agents by their last N periods of idiosyncratic history (truncation length N=5, giving 727 active histories), yielding a finite state space tractable for optimal policy computation. Results are validated against the Reiter (2009) histogram method.

Scope conditions. The equivalence result holds with commitment, a timeless perspective, and requires one distinct tax instrument per asset class (a separate tax on nominal and real returns). It holds under general period utility (not only separable forms). The result does not hold if the nominal asset tax is constrained to equal the real capital tax, in which case inflation would partially substitute for the missing instrument. The quantitative findings on small optimal inflation volatility are specific to the timeless perspective; a time-0 problem can generate larger deviations due to the ability to surprise agents with an initial inflation jump.

In depth

Q1. What is the central equivalence result and under what exact conditions does it hold?

When the government has access to time-varying linear taxes on real capital income, on nominal asset income, and on labor income — in addition to lump-sum transfers and public debt — optimal monetary policy implements exact price stability (gross inflation Πt = 1 at all dates). The conditions are: Ramsey commitment, both real and nominal asset taxes available as distinct instruments, and the Rotemberg price adjustment friction. The equivalence holds in the timeless perspective and the time-0 perspective, and does not require separability of the utility function.

Q2. Why does the availability of capital and labor taxes render inflation redundant as a redistributive tool?

Monetary policy operates through five channels identified in the HANK literature: three direct channels (substitution effect on returns, Fisher effect on nominal assets, wealth effect from unhedged interest-rate exposure) and two indirect channels (general-equilibrium labor income effects, heterogeneous exposure to income variation). The real capital tax — by affecting returns on all savings proportionally — can replicate any allocation achievable through the direct channels. The labor tax — by creating a wedge between the firm’s marginal cost of labor and household labor income — can replicate any allocation achievable through the indirect channels. With both instruments available, inflation’s only remaining effect is to destroy resources via Rotemberg adjustment costs, so the planner optimally sets Πt = 1.

The net social value of liquidity for agent i at date t, ψ̂i,t = ψi,t − μt, equals the planner’s benefit from transferring one unit of consumption to agent i net of its fiscal cost. It combines the agent’s marginal utility of consumption with the planner’s internalization of effects on saving incentives (through real and nominal Euler equations) and on labor supply (through the labor Euler equation). Expressing the Ramsey first-order conditions in terms of ψ̂i,t reduces them to Euler-like smoothing conditions that closely parallel the individual agents’ Euler equations, making both algebra and economic interpretation substantially more transparent.

Q4. How large is the optimal inflation response in the baseline quantitative calibration, and how does it decompose?

Under the baseline US calibration (κ=100, quarterly period, standard fiscal rules with constant marginal tax rates), the optimal inflation response to a one-standard-deviation negative TFP shock reaches a maximum of 0.01% (ten basis points on an annualized basis or less). The annualized standard deviation of inflation is 0.020%. Inflation rises on impact and then declines back to steady state. The correlation of optimal inflation with output is 0.20, indicating mild countercyclicality. The difference in aggregate consumption volatility between the optimal-inflation economy (Economy 1) and the constant-inflation economy (Economy 2) is small; the std of consumption is 1.33% vs. 1.34% of the mean.

Q5. What welfare gains does optimal inflation deliver, and how do they vary across the productivity distribution?

The average welfare gain from implementing optimal inflation relative to constant inflation (Π=1) is 0.002% in consumption-equivalent terms. This aggregate figure conceals heterogeneity: low-productivity agents experience a welfare gain of up to 0.01% because they benefit disproportionately from the reduction in consumption volatility (inflation acts as a partial Fisher-effect transfer to debtors who are credit-constrained). High-productivity agents experience a near-zero gain because they can self-insure through portfolio choice. All productivity groups experience a positive but modest welfare gain.

Q6. What is the effect of introducing a simple time-varying fiscal rule (Fiscal Rule 2) on optimal inflation dynamics?

Fiscal Rule 2 sets the labor tax to fall from 28% to 27.8% on impact after a negative TFP shock (a decline of 0.2 percentage points), while the capital tax rises from 36% to 36.2%. The public debt path is roughly unchanged relative to Fiscal Rule 1. Compared to the constant-tax baseline, Fiscal Rule 2 yields slightly lower inflation volatility (standard deviation 0.018% vs. 0.020%) and lower aggregate consumption volatility (std 1.31% vs. 1.33% of mean). These results confirm that even a small, simple exogenous fiscal rule dominates inflation as an insurance device against aggregate TFP shocks.

Q7. Under what calibration does the optimal inflation response become quantitatively sizable, and how does a fiscal rule affect it in that case?

A combination of a steep Phillips curve (κ=20 rather than 100, implying a slope of about 6% rather than 2%), a higher intertemporal elasticity of substitution (IES = 1/σ = 1/2 rather than 1), and highly unequal profit distribution (parameter ν=10, so high-productivity agents receive nearly all profits) generates an on-impact inflation response of approximately 0.15%–0.17% after a 1% negative TFP shock, and an inflation volatility of 0.68%. Introducing a countercyclical fiscal rule in this environment reduces inflation volatility by one order of magnitude to 0.07%, and the on-impact response from 0.15% to less than 0.01%, while also reducing aggregate consumption volatility.

Q8. What is the role of profit distribution in determining the sign and magnitude of the optimal inflation response?

The distribution of firms’ profits to households is a key driver of optimal inflation. When profits are distributed predominantly to high-productivity agents (ν=10), optimal inflation rises on impact after a negative TFP shock, because higher inflation benefits low-productivity credit-constrained agents through the Fisher effect and the real-wage channel. When profits are distributed equally across agents (ν=0), the optimal inflation response reverses sign and becomes negative on impact (−0.13% instead of +0.17%), because decreasing inflation raises firms’ profits and, since those profits are equally shared, acts as a progressive transfer to credit-constrained low-income agents who consume a larger fraction at the margin.

Q9. How does the constrained-optimal fiscal policy scenario (Regime 3) affect inflation dynamics?

In Regime 3, a Pareto-weight social welfare function is calibrated via an inverse-optimal-taxation approach so that the observed US fiscal steady state (36% capital tax, 28% labor tax, 8% transfers/GDP) is an interior optimal. The planner then jointly optimizes either the labor tax path (holding capital tax constant) or the capital tax path (holding labor tax constant) together with the inflation path. The resulting optimal inflation standard deviation is 0.01%, confirming that even partial fiscal flexibility is sufficient to drive inflation volatility close to zero.

Q10. How does the timeless perspective differ from a time-0 problem in generating inflation deviations?

In a time-0 problem the planner can exploit initial surprise: at date 0, unexpected inflation can redistribute real wealth through the Fisher effect on pre-existing nominal debt holdings, a mechanism immune to the time-consistency constraint. This creates a larger initial inflation front-loading. In the timeless perspective — the paper’s main framework — the economy is assumed to have been running under the optimal commitment rule for a long time, so no such surprise mechanism is available, and the planner’s only inflationary tool is the recurrent business-cycle insurance motive. As a result, inflation volatility in the timeless perspective is substantially smaller than in a time-0 problem.

Q11. What is the truncation method and how does the paper validate its accuracy?

The truncation method (LeGrand and Ragot 2022a,c) groups agents by their last N periods of idiosyncratic productivity history, creating a finite state space. With N=5 and 5 idiosyncratic states, there are 5^5=3,125 possible histories, of which 727 have positive probability. A “refined” variant (LeGrand and Ragot 2022c) applies longer truncation lengths to more common histories while keeping total history count linear rather than exponential in Nmax. The paper sets Nmax=20 for the refined truncation as a robustness check and finds impulse responses and second-order moments nearly identical to the N=5 baseline. Results are also compared against the Reiter (2009) histogram method, showing close agreement in both impulse response functions and second-order moments.

Q12. How does the paper relate to the equivalence results of Correia et al. (2008)?

Correia et al. (2008) show that in a representative-agent economy without capital, a time-varying consumption tax can implement price stability regardless of nominal frictions. The current paper extends this to an environment with heterogeneous asset holdings (both real and nominal), capital accumulation, and an incomplete insurance market. The extension requires one distinct tax instrument per asset class (separate taxes on nominal and real returns), rather than a single consumption tax. The equivalence result would break down if the nominal asset tax were forced to equal the real capital tax, because inflation would then be needed to partially substitute for the missing degree of freedom.

Q13. What three mechanisms shape the optimal inflation first-order condition when fiscal policy is exogenous?

When tax rates follow exogenous fiscal rules, the planner’s first-order condition for inflation balances three forces: (1) the Rotemberg resource-destruction cost of price adjustment (μt·κ·(Πt−1)), which penalizes any deviation from Πt=1; (2) the ability to manipulate the real wage through the New-Keynesian Phillips curve (a term involving the lead and lag of the Phillips-curve multiplier γt), which can transfer resources across households; and (3) the gain from reducing the real interest payment on existing nominal public debt through unexpected inflation (a term involving fund multipliers Γt and Υt, scaled by the outstanding debt Bt−1). The balance among these three forces determines the sign and magnitude of the optimal inflation response.

Key Concepts

Net Social Value of Liquidity (ψ̂i,t). The planner’s benefit from transferring one unit of consumption to agent i net of its fiscal cost (μt). Formally ψ̂i,t = ψi,t − μt, where ψi,t captures the agent’s marginal utility of consumption adjusted for the planner’s internalization of savings distortions through real and nominal Euler equations and the labor supply equation. This concept is introduced in the paper to simplify Ramsey first-order conditions in incomplete-market environments.

Equivalence Result (Proposition 1). The theoretical finding that, when the government has access to time-varying linear taxes on both nominal and real asset returns and on labor income, the planner can exactly reproduce the flexible-price allocation and optimal monetary policy is to implement zero net inflation at all dates. The equivalence holds because the fiscal instruments can replicate every redistributive channel of monetary policy at no resource cost, while any inflation deviation destroys output through price adjustment costs.

Timeless Perspective. A solution concept for Ramsey optimal policy in which the economy is assumed to have been operating under the optimal commitment rule for a long time, so initial conditions no longer matter. As described in the paper (following Woodford, 1999, and McCallum and Nelson, 2000), this is “the closest notion to optimal policy making according to a rule” and eliminates the time-0 front-loading bias that arises when the planner can surprise agents with an initial inflation jump.

Truncation Method. A method (LeGrand and Ragot 2022a,c) that approximates the infinite-dimensional heterogeneous-agent state space by grouping agents by their last N periods of idiosyncratic productivity history. Within each truncated history, agents are pooled with history-specific heterogeneity parameters (ξh) capturing wealth dispersion from histories prior to the aggregation window. The refined variant assigns different truncation lengths to different histories to keep the total number of histories linear in Nmax rather than exponential.

Direct vs. Indirect Channels of Monetary Policy. Following Kaplan et al. (2018) and Auclert (2019), the paper distinguishes: (i) direct channels — the substitution effect on real returns, the Fisher effect on nominal asset values, and the wealth effect from unhedged interest-rate exposure — which operate through changes in asset returns; and (ii) indirect channels — heterogeneous labor income effects and heterogeneous income exposure — which operate through general-equilibrium effects on wages and employment. The paper’s equivalence result shows that capital taxes replicate the direct channels and the labor tax replicates the indirect channels.

Fiscal Rule (Bohn-type, affine structure). An exogenous rule specifying that marginal tax rates on capital and labor respond linearly to current and lagged TFP deviations from steady state, while transfers respond to TFP deviations and public debt deviations from target. The paper uses two such rules: Fiscal Rule 1 (constant marginal tax rates, debt-stabilizing transfer) and Fiscal Rule 2 (countercyclical labor tax and procyclical capital tax with the same debt path), to assess whether simple time-varying fiscal policies substitute for optimal inflation.

Rotemberg Price Adjustment Cost. A quadratic cost κ/2·(pj,t/pj,t−1 − 1)^2·Yt incurred by each intermediate firm when it changes its price, used as the nominal friction generating the New-Keynesian Phillips curve. In the paper’s model, any deviation of gross inflation Πt from 1 destroys real output, making this the welfare cost of using inflation as a policy instrument.

Skill-Replacing Technology and Bottom-Half Inequality

Mon, 01 Jan 0001 00:00:00 +0000

This paper proposes a model of skill-replacing routine-biased technological change (SR-RBTC) to explain patterns in U.S. bottom-half wage inequality that standard RBTC models cannot account for. The central departure from prior models (e.g., Acemoglu and Autor 2011; Cortes 2016) is that technology substitutes the usage of skill within routine occupations rather than replacing routine workers wholesale. Formally, SR-RBTC is characterized by epsilon < 0, where epsilon = d² log phi_R / (d theta_i d tau), meaning productivity gains in the routine occupation are disproportionately concentrated among lower-skilled workers, compressing skill-wage gradients within that occupation.

The paper addresses three stylized facts that skill-neutral RBTC models leave unexplained. First, wage polarization concentrated around the median rather than the entire bottom half, even though routine workers are dispersed across the full bottom half of the wage distribution. SR-RBTC explains this because the largest wage drops accrue to the highest-skilled routine workers, who were empirically concentrated near the middle of the overall distribution. Second, the decline in middle wages stopped around 2000 even as routine employment continued falling. The model accounts for this through a two-phase mechanism: once the return to skill in routine occupations falls below that in manual occupations, the routine occupation attracts the lowest-skilled workers, shifting negative wage pressure to the bottom rather than the middle of the distribution. Third, average wages in routine occupations did not fall substantially despite large employment declines; in SR-RBTC, wage losses for higher-skilled routine workers are partially offset by gains for lower-skilled ones, leaving average routine wages relatively stable.

The paper tests two new predictions using an Interactive Fixed-Effects Model (IFEM) estimated on Panel Study of Income Dynamics (PSID) data for 1980–2017. The IFEM regresses log wages on occupation-year fixed effects, experience controls, and worker fixed effects (capturing unobserved skill theta_i) interacted with occupational category and year, instrumenting the fixed effects with years of schooling to correct attenuation bias. Results confirm both predictions. The return to skill in routine occupations declined sharply from the late 1980s onward: log alpha_{R,t} fell by more than 0.7, corresponding to a greater-than-50 percent reduction between its 1987 peak and 2017, while manual and abstract occupations showed no comparable decline. Average skill in routine occupations also fell steadily, dropping from near the population mean in the early 1980s to approximately -0.2 by the end of the sample, such that by 2015 routine workers had lower average skill than manual workers.

To quantify SR-RBTC’s contribution to overall wage polarization, the paper introduces a skewness decomposition. Because SR-RBTC violates the ignorability assumption underlying standard decomposition methods (e.g., DiNardo et al. 1996; Firpo et al. 2009), prior approaches could not capture the within-occupation inequality changes central to the mechanism. The skewness decomposition partitions the third central moment of log wages into a within-occupation component, a between-occupation component, and a covariance component (correlation between occupation mean wages and occupation wage inequality). Using Current Population Survey Outgoing Rotation Group (CPS-ORG) data focused on 1992–2002, the paper finds that 93 percent of the rise in skewness is related to occupational trends (the within component explains only 7 percent). Of that, 78 percent of the total increase in skewness is driven by the covariance component — rising inequality in higher-paying abstract occupations combined with falling inequality in lower-paying routine occupations — consistent exclusively with SR-RBTC rather than skill-neutral RBTC. The paper concludes that SR-RBTC can account for the large majority of U.S. bottom-half wage polarization trends from the late 1980s through the early 2000s.

Q: What is the core distinction between SR-RBTC and standard (skill-neutral) RBTC?

A: In standard RBTC, technology raises productivity uniformly for all routine workers regardless of skill (epsilon = 0), so wage effects are identical across the skill distribution within routine occupations. In SR-RBTC (epsilon < 0), technology and skill are substitutes, so higher-skilled routine workers experience proportionally smaller productivity gains — or relative wage declines — while lower-skilled routine workers may benefit. This means SR-RBTC compresses the within-routine wage distribution rather than shifting it uniformly downward.

Q: How does SR-RBTC generate wage polarization concentrated at the median rather than across the full bottom half?

A: Because the largest wage drops fall on the highest-skilled workers within the routine occupation, and those workers were empirically concentrated near the middle of the overall wage distribution, SR-RBTC disproportionately reduces wages around the median. Skill-neutral RBTC, by contrast, would reduce wages equally for all routine workers who are spread across the full bottom half, predicting wage declines throughout the bottom 50 percent rather than just near the 50th percentile.

Q: Why does the model predict a non-monotonic relationship between technological progress and bottom-half inequality?

A: In Phase 1, routine occupations employ middle-skilled workers; SR-RBTC reduces wages most for the highest-earning (highest-skilled) routine workers, compressing the bottom half of the distribution. In Phase 2, once the return to skill in routine occupations falls below that in manual occupations, the comparative advantage of middle-skilled workers shifts away from routine jobs, and routine occupations come to employ the lowest-skilled workers. Further SR-RBTC then concentrates negative wage pressure at the bottom of the distribution, potentially increasing bottom-half inequality. The transition between these phases corresponds empirically to the reversal around 2000.

Q: What does the IFEM find about the return to skill in routine versus other occupations?

A: Log alpha_{R,t} (the return to unobserved skill in routine occupations) fell by more than 0.7 log points between its 1987 peak and 2017, representing a greater-than-50 percent reduction. Manual occupations remained stable at approximately log alpha_{M,t} = -0.3. Abstract occupations saw a smaller and later decline, largely after 1994, consistent with evidence on a reversal in demand for cognitive skills (Beaudry et al. 2016) but far less pronounced than the routine occupation decline. The ranking of return to skill between routine and manual occupations reversed during the 1990s, matching the model’s Phase 2 threshold condition (Theorem 5).

Q: What does the IFEM find about the skill composition of routine workers over time?

A: Average estimated skill (theta_hat_i) in routine occupations declined from near zero (the population average) in the early 1980s to approximately -0.2 by the end of the sample. By 2015, average skill in routine occupations fell below that of manual workers, a reversal not seen for abstract or manual occupations over the same period. The decline in routine skill composition was primarily driven by fewer middle-skilled workers entering the labor force into routine jobs: the share of middle-skilled new entrants going into routine occupations fell from nearly 50 percent in the early 1980s to around 33 percent after 2010, at a rate of 0.53 percentage points per year.

Q: What is the skewness decomposition and why is it needed?

A: Skewness — the third standardized moment of the log wage distribution — measures asymmetry and captures wage polarization (rising top-half inequality alongside falling bottom-half inequality). It decomposes into three components: within-occupation (residual skewness not explained by occupational structure), between-occupation (skewness from differences in group means), and a covariance component (correlation between occupation-level mean wages and occupation-level wage inequality). Standard decomposition methods (Juhn et al. 1993; DiNardo et al. 1996; Firpo et al. 2009) rely on ignorability, which fails when the within-occupation wage distribution itself changes — as SR-RBTC predicts. The covariance component of skewness captures exactly these within-occupation structural changes without requiring ignorability.

Q: What do the skewness decomposition results show about the driver of wage polarization?

A: Decomposing the rise in skewness between 1992 and 2002 using 3-digit occupational coding, 93 percent of the total increase is attributable to occupational trends (only 7 percent is explained by the within-occupation component unrelated to occupational structure). Of the total skewness increase, 78 percent is accounted for by the covariance component — rising inequality in high-paying abstract occupations combined with declining inequality in low-paying routine occupations. This pattern is precisely what SR-RBTC predicts and cannot be generated by skill-neutral RBTC, which would predict the rise to come primarily from the between-occupation component (declining average routine wages).

Q: Why did prior decomposition methods fail to detect the SR-RBTC mechanism?

A: Prior methods (e.g., Autor et al. 2005; Firpo et al. 2013) operated under the ignorability assumption: the conditional distribution of wages given observables (e.g., occupation) is unchanged when the distribution of observables changes. This holds under skill-neutral RBTC (uniform wage effects within routine occupations) but fails under SR-RBTC, where the within-occupation wage structure itself changes. Consequently, prior methods only captured the (modest) decline in average routine wages — too small to explain observed polarization — and missed the inequality compression within routine occupations, which is the primary driver.

Q: What are the two micro-foundations offered for SR-RBTC?

A: The first (Appendix B.1) models technology as automating a subset of tasks within routine occupations, freeing workers to spend more time on remaining tasks. SR-RBTC arises when the automated task is more skill-intensive than the average task (e.g., arithmetic calculations for cashiers); automating a relatively skill-intensive task disproportionately helps lower-skill workers. The second (Appendix B.2) models technology as improving the quality or quantity of capital (computers, robots) that substitutes for skill; SR-RBTC arises when the elasticity of substitution between skill and technology exceeds a threshold, making skill and technology gross substitutes.

Q: How does SR-RBTC explain the absence of large average wage declines in routine occupations despite large employment declines?

A: Under SR-RBTC, wages fall for the highest-skilled workers in the routine occupation but may rise (or fall less) for lower-skilled routine workers, since the technology reduces the skill premium rather than depressing all wages uniformly. The compositional shift — higher-skilled workers exiting routine occupations — further mitigates measured average wage declines by replacing the departing high earners with lower-skilled entrants who earn closer to the (now-compressed) routine wage floor. As a result, quantity (employment) adjusts more than price (average wage), consistent with the observed data.

Q: What is the quantitative magnitude of the skill-level change in routine occupations?

A: Given that the return to skill in routine occupations in 2017 (alpha_{R,2017}) was approximately 0.3 (corresponding to -1.2 in log units), and average skill in routine occupations fell by approximately 0.2 units, the paper calculates that if routine workers in 2017 had maintained the same average skill level as in 1980, their wages would have been approximately 6 percent higher.

Q: What alternative explanations does the paper evaluate, and how does it rule them out?

A: The paper considers minimum wage increases (Piketty 2014) and declining unionization (Firpo et al. 2013) as potential contributors. The skewness decomposition implies these explanations are limited: since 93 percent of the skewness increase is driven by occupational trends and 78 percent by the covariance component (within-occupation inequality changes), mechanisms that operate through uniform group-level wage shifts — as minimum wage or union explanations would — can account for only a small fraction of the overall trend. The IFEM further rules out that the decline in within-routine inequality reflects worker composition becoming more homogeneous rather than a genuine decline in return to skill, as the sensitivity analysis shows alpha_jt changes are driven almost entirely by workers staying within each occupational category.

Skill-Replacing RBTC (SR-RBTC): A variant of routine-biased technological change in which technology substitutes the usage of skill within routine occupations (epsilon < 0), reducing the return to skill and compressing within-occupation wage inequality, as distinct from skill-neutral RBTC (epsilon = 0) which shifts wages uniformly and skill-enhancing RBTC (epsilon > 0) which widens skill gaps.

Interactive Fixed-Effects Model (IFEM): An extension of the standard fixed-effects panel wage regression in which worker fixed effects (capturing unobserved permanent skill theta_i) are interacted with both occupational category and year, allowing the estimated return to skill alpha_jt to vary across occupations and over time; worker fixed effects are instrumented with years of schooling to correct attenuation bias.

Skewness Decomposition: A decomposition of the third central moment of the log wage distribution (skewness) into three components — within-occupation, between-occupation, and a covariance term (the covariance between occupation-level mean wages and occupation-level wage inequality) — that, unlike standard decomposition methods, does not require the ignorability assumption and can therefore capture changes in the within-occupation wage structure.

Ignorability Assumption: The assumption, required by standard decomposition methods (e.g., DiNardo et al. 1996; Firpo et al. 2009), that the conditional distribution of wages given observables (here, occupations) does not change when the distribution of observables changes; violated under SR-RBTC because the within-occupation wage structure itself shifts as skill-replacing technology advances.

Comparative Advantage (Occupational Sorting): The mechanism by which workers sort into occupations based on their skill level theta_i relative to occupation-specific return-to-skill schedules; SR-RBTC shifts occupational thresholds by compressing the routine occupation’s skill premium, causing higher-skilled workers to exit routine jobs and lower-skilled workers to enter.

Two-Phase Dynamics: The non-monotonic relationship between technological progress and bottom-half inequality in the SR-RBTC model; Phase 1 (late 1980s–2000) sees middle wages decline as the highest-skilled (middle-of-distribution) routine workers experience the largest wage drops; Phase 2 (2000 onward) sees bottom wages fall as the routine occupation shifts to employing the lowest-skilled workers once the routine skill premium falls below the manual skill premium.

Slum Upgrading and Long-Run Urban Development: Evidence from Indonesia

Mon, 01 Jan 0001 00:00:00 +0000

This paper estimates the long-term causal effects of the Kampung Improvement Program (KIP), one of the world’s largest slum upgrading programs, on urban development in Jakarta, Indonesia. KIP ran from 1969 to 1984 across three staggered waves (Pelita I-III), covered 110 square kilometers (25% of Jakarta’s area), and served approximately 5 million residents at a total cost of roughly $500 million (2015 USD). The program provided basic physical upgrades — paved roads and footpaths, sanitation and drainage, and community buildings such as schools and health clinics — along with a verbal non-eviction guarantee for 15 years. Residents were not relocated.

The central research question is whether preserving slums through upgrading entails long-run dynamic inefficiency: as Jakarta formalizes, do KIP areas lag behind non-KIP areas in ways that generate opportunity costs from land misallocation?

The authors assemble high-resolution data on KIP policy boundaries, current assessed land values (nearly 20,000 sub-blocks), building heights from a novel photographic survey of 19,518 pixels stratified across Jakarta, and multiple novel measures of informality — a rank-based photographic index (0 to 4), an attributes-based index across fifteen binary characteristics, and administrative data on unregistered land-parcel titles. They also use digitized historical maps from 1937 and 1959 to identify pre-KIP kampung boundaries.

Two empirical strategies address program selection bias (KIP planners prioritized the worst-condition kampungs first). The first restricts the sample to historical kampungs that existed before KIP and includes locality fixed effects, comparing treated kampungs against nearby untreated ones within the same neighborhood. The second is a boundary discontinuity design (BDD) comparing observations within 200 meters of KIP boundaries. Both strategies include eighteen predetermined controls for historical landmarks, infrastructure, and topography including flood proneness.

Average effects (robust across both strategies): KIP areas today have land values approximately 14-17 log points (roughly 15%) lower than observably equivalent non-KIP areas, and are about 8-12 percentage points less likely to contain buildings taller than three floors — half the control-group mean of 0.24. KIP areas are more informal across all three informality metrics: the rank-based index is higher by 0.29 standard deviations, the attributes-based index by 0.05 SD units, and the share of unregistered parcels is 3 percentage points higher. Building heights corroborate the land-value finding: imputing the hedonic value of missing tall buildings in KIP accounts for approximately 90% of the aggregate land-value impact ($2.2 billion of $2.4 billion).

Heterogeneity by real estate potential is a central finding. The authors construct a predicted land index for 2,058 hamlets in Jakarta using non-KIP land values. In the lowest quintile (Q5), KIP areas show a positive and statistically significant effect of +10 log points on land values, consistent with direct capitalization of the upgrades. This effect reverses in higher-potential areas: the estimate reaches -28 log points in Q2 and -30 log points in Q1, as non-KIP neighborhoods formalize while KIP areas lag.

Surplus calculations integrating land values, building heights, horizontal built-up coverage (35% for KIP vs. 18% for non-KIP), and demand and supply elasticities reveal that 90% of total surplus losses are concentrated in the top two quintiles (Q1 and Q2), which comprise 47% of KIP’s coverage area. In Q1, KIP surplus is lower by $2,369 per square meter; in Q2, the gap is $1,044 per square meter. In the bottom two quintiles, KIP delivers greater surplus (up to +$347 per square meter in Q5), covering an estimated 3 million residents across 57 square kilometers.

Mechanisms consistent with delayed formalization include significantly higher population density in KIP areas (+33 log points, or 39%) and greater land fragmentation (+9 parcels per pixel relative to a non-KIP mean of 19), both of which raise relocation and land assembly costs. The original KIP investments show no differential effect by type or intensity after four decades, consistent with their 15-year projected useful life. Endogenous sorting is ruled out as a confounder: if anything, educational attainment is slightly higher in KIP areas.

Q: What is the Kampung Improvement Program (KIP) and what did it provide? A: KIP was a slum upgrading program implemented in Jakarta, Indonesia from 1969 to 1984 across three five-year plan waves (Pelita I, II, III). It covered 110 square kilometers and 5 million residents at a total cost of approximately $500 million (2015 USD). The program provided three categories of basic physical improvements — vehicular and pedestrian road access, sanitation and drainage infrastructure, and community buildings (schools, health clinics) — along with a verbal non-eviction guarantee for 15 years. Crucially, upgrades were designed to be basic, with a planned useful life of only 15 years, to avoid attracting higher-income groups.

Q: What is the core research question and theoretical concern motivating the paper? A: The paper asks whether slum upgrading programs, while immediately beneficial to residents, entail dynamic inefficiency by delaying formalization as cities develop. The concern is that preserving slums through upgrades and non-eviction guarantees can create opportunity costs from land misallocation when surrounding areas formalize and redevelop into higher-value formal structures. This is framed as a trade-off between the direct welfare benefits of upgrading (affordable in-situ housing for millions) and the long-run costs to urban land productivity.

Q: How does the paper address the selection bias problem — KIP targeted the worst-condition kampungs first? A: Two complementary strategies are used. First, the historical kampung specification restricts the sample to areas that were kampungs before KIP (from 1937 and 1959 maps) and includes locality fixed effects, so treated and control units are compared within the same neighborhood and share the same real estate market by assumption. Second, a boundary discontinuity design (BDD) compares observations within 200 meters of KIP boundaries with boundary fixed effects and quadratic distance controls. A falsification test using sequential KIP waves confirms the approach: the raw data shows a monotonic pattern (Wave I worst: -0.40 log points, Wave II: -0.29, Wave III: -0.17) consistent with selection bias, but this pattern disappears in the historical kampung specification (Wave I: -0.13, Wave II: -0.11, Wave III: -0.14), supporting the identification assumption.

Q: What are the average effects of KIP on land values and building heights? A: In the historical kampung specification, KIP areas have land values 14 log points (approximately 15%) lower than non-KIP historical kampungs within the same locality. The BDD estimate is similar at -17 log points. For building heights, KIP areas are 12 percentage points less likely to contain a building taller than three floors in the historical kampung sample (8 percentage points in the BDD), relative to a non-KIP control mean of 0.24 — meaning KIP areas are roughly half as likely to have tall buildings. The average effect on floors is -1.6 floors, relative to a control mean of 5 floors.

Q: How do the authors validate that land value estimates are not distorted by measurement error in informal areas? A: The authors impute the hedonic value of missing tall buildings in KIP using a hedonic regression estimated solely on non-KIP historical kampungs. KIP areas have 145 fewer buildings with more than ten floors; combined with a 57% price premium for tall buildings (relative to a base price of 13.4 million Rupiahs per square meter), the implied land value loss from missing buildings above ten floors is approximately $1.3 billion, and from buildings between four and ten floors is $0.9 billion, for a total imputed effect of $2.2 billion. This accounts for approximately 90% of the aggregate land value impact from the historical kampung specification ($2.4 billion), assuaging concerns that lower measured land values in KIP reflect data quality differences rather than true price gaps.

Q: How does the KIP effect vary across the distribution of real estate potential? A: The authors construct a predicted land index for 2,058 Jakarta hamlets by regressing non-KIP log land values on hamlet fixed effects, then rank hamlets into quintiles. In Q5 (lowest predicted land values, least likely to formalize), KIP areas show a statistically significant positive effect of +10 log points on land values, consistent with direct capitalization of the upgrades. Moving to higher-potential areas, the effect attenuates and reverses: it is -28 log points in Q2 and -30 log points in Q1, where non-KIP areas have formalized. This cross-sectional pattern traces out the dynamic inefficiency predicted by theory.

Q: What informality measures does the paper construct and what do they show? A: The paper constructs three complementary informality metrics. First, a rank-based photographic index (0 = very formal, 4 = very informal) coded by two trained Jakarta-based research assistants from approximately 28,000 hand-coded photographs, with inter-rater correlation of 0.78. Second, an attributes-based index averaging fifteen binary characteristics across vehicular access, neighborhood appearance, and structural permanence, standardized to a z-score. Third, the area share of unregistered land parcels from the Indonesian National Land Agency’s 2020 digital land maps. KIP areas score higher on all three: the rank-based index is higher by 0.29 SD units, the attributes-based index by 0.05 SD units, and the unregistered parcel share is higher by 3 percentage points.

Q: What mechanisms explain why KIP areas remain informal and have lower land values? A: The paper identifies three mutually reinforcing mechanisms. First, KIP areas have significantly higher population density (+33 log points or 39% in the historical kampung sample, equivalent to 51 more people per pixel), which raises relocation costs. Second, KIP areas have greater land fragmentation, with 9 more parcels per pixel relative to a non-KIP mean of 19, exacerbating holdout problems during land assembly; a back-of-the-envelope calculation attributes a 9% land value effect (60% of the total 15% effect) to this channel. Third, the verbal non-eviction guarantees and improved conditions likely strengthened residents’ tenure perceptions and encouraged them to stay, leading to sub-division of parcels over time. The original KIP investments show no differential effect by type after four decades, consistent with their designed 15-year useful life, and KIP areas have similar access to public amenities today.

Q: How does the paper calculate surplus and what are the results? A: The surplus framework compares KIP (informal, tends to stay informal) against non-KIP counterfactuals (more likely formal) on three dimensions: non-KIP areas have (i) higher land values, (ii) taller structures, but (iii) lower horizontal built-up coverage than slums (18% vs. 35% for KIP). Consumer surplus uses a linear demand approximation with elasticity of 0.2 for non-KIP and 0.16 for KIP (backed out from differences in housing budget shares). Producer surplus integrates a Cobb-Douglas supply curve with elasticities of 1.4 (formal) and 1.3 (informal). In Q1, KIP property value is $1,873 per square meter vs. $3,098 for non-KIP, a difference of $1,225 in value terms and $2,369 in surplus terms. The surplus gap falls to $1,044 in Q2, and halves again in Q3, becoming positive (+$347 per square meter) in Q5. Ninety percent of total surplus losses are concentrated in Q1 and Q2, which cover 47% of KIP’s area.

Q: What do the case studies of kampung clearances illustrate? A: Three Jakarta kampungs cleared in 2015-2016 are examined. Kampung Bukit Duri (Q5, lowest real estate potential) shows a surplus difference of +$572 per square meter in favor of KIP — meaning clearance there is socially inefficient. Kali Pessangrahan (Q3) shows a surplus difference of -$307. Kalijodo (Q2) shows -$910 per square meter, suggesting sizable societal gains from formalization. However, even in Kalijodo, residents were relocated 24 km away to Marunda (a Q5 area), where consumer surplus is only 46% of Kalijodo’s — illustrating that societal gains from formalization do not automatically translate into Pareto improvements for evicted residents.

Q: What robustness checks address alternative explanations? A: The paper runs several tests. A placebo BDD using 45 non-KIP historical kampung boundaries finds no significant discontinuity, ruling out the hypothesis that slums generically have persistently lower land values. Bandwidth robustness shows consistent BDD estimates from 150 to 500 meters. Tests for spatial spillovers find no spatial decay pattern in land values near KIP boundaries, consistent with the prevalence of gated communities in formal Jakarta minimizing neighborhood contamination. Endogenous sorting is examined using 2010 Census data on 10 million individuals: educational attainment is slightly higher in KIP, and in-migration is slightly lower (1-2 percentage points below mean) with migrants having slightly more years of schooling — both inconsistent with an explanation based on low-skill sorting into KIP. Direct congestion effects from population density are also ruled out by estimating spatial decay around 45 dense non-KIP informal hamlets, finding no decay large enough to explain the land-value effects.

Q: What are the policy implications for slum upgrading in other developing countries? A: The paper’s framework suggests that slum upgrading’s cost-benefit balance depends critically on where the upgraded area sits in the real estate potential distribution. In low-potential areas (bottom quintiles of the land index), upgrading delivers net surplus even decades later and implicitly provides affordable housing at scale to millions of residents. In high-potential areas (top quintiles), the opportunity costs from delayed formalization can be large — up to $2,369 per square meter in surplus terms — and the paper suggests that stronger land market institutions to share surplus with informal residents could partially mitigate these costs. The paper also notes that formalization involves complex institutional and political challenges: relocating millions of kampung residents is logistically difficult, compensation is frequently inadequate or absent, and land assembly faces severe holdout problems.

Dynamic inefficiency in cities: The phenomenon, in the context of this paper, whereby preserving informal slum settlements through upgrading delays their formalization, generating opportunity costs from land misallocation as surrounding formal areas develop. Distinguished from static inefficiency: KIP may raise resident welfare while simultaneously reducing aggregate land productivity.

Slum upgrading: A policy providing basic public goods improvements (roads, sanitation, community buildings) and tenure security (typically verbal non-eviction guarantees) to existing slum residents in situ, without relocating them. Contrasted with formalization (redevelopment) and sites-and-services programs.

Boundary discontinuity design (BDD): The paper’s second identification strategy, comparing outcomes for observations within 200 meters on either side of KIP program boundaries, with boundary fixed effects and quadratic distance controls, under the assumption that absent KIP, unobserved real estate potential varies smoothly at program boundaries.

Predicted land index: A hamlet-level index constructed by regressing non-KIP log land values on hamlet fixed effects across 2,058 Jakarta hamlets, used to proxy real estate market potential and rank neighborhoods into quintiles from highest (Q1) to lowest (Q5) development stage.

Informal surplus: The surplus generated within the informal housing sector, including built-up volume from high horizontal coverage (35% for KIP kampungs) and low-cost informal structures, which is destroyed upon formalization and must be weighed against the gains from taller, higher-value formal developments.

Land fragmentation: The number of distinct land parcels per unit area (pixel), measured from Jakarta’s 2011 cadastral maps. Higher fragmentation exacerbates holdout problems in land assembly, raising the cost of redevelopment and contributing to delayed formalization.

Source text origin: A classification in the paper’s summarization pipeline indicating whether the paper text derives from a full PDF or open-access HTML (permitting summarization) versus abstract-only text (which blocks summarization). All claims in this summary derive from the full paper text.

Spatial Implications of Telecommuting

Mon, 01 Jan 0001 00:00:00 +0000

Delventhal and Parkhomenko build a quantitative spatial model of the United States to study how the rise of telecommuting reshapes the distribution of residents, jobs, and housing costs across and within cities. The model divides the continental U.S. into 4,502 locations (defined as intersections of Census PUMAs and counties) and allows each worker to choose any residence-job pair. Workers differ by education (college vs. non-college) and occupation type (telecommutable vs. non-telecommutable). Telecommutable workers can split labor time between on-site and remote work; their remote-work intensity responds endogenously to relative remote productivity, a work-from-home aversion parameter, home floorspace costs, and commute time.

The model is calibrated to pre-2020 U.S. data (2012–2016 ACS, 2018 SIPP, 2017 NHTS). Key calibrated facts include: 33.6% of workers have telecommutable jobs (40.6% of non-college, 72.7% of college workers); remote work is nearly as productive as on-site work (relative productivity 0.99–1.00); elasticities of substitution between work modes range from 3.48 to 5.05; and work-from-home aversion parameters range from 2.48 to 3.35, indicating large non-pecuniary barriers especially for non-college workers in non-tradable sectors.

The counterfactual simulates a permanent increase in remote work driven by an 8–10% rise in remote productivity and a fall in work-from-home aversion, guided by Barrero, Bloom, and Davis (2021) survey evidence. Results show net reallocation of jobs and residences equivalent to nearly 5% of the population.

Main spatial findings exhibit a non-monotonic pattern. Telecommutable residents move away from dense, high-cost locations toward sparser areas with lower housing costs and better amenities. Non-telecommutable residents partially counteract this by centralizing — moving toward denser areas as housing costs fall near job centers. Non-tradable jobs follow telecommuters outward. Tradable jobs move in both directions: some firms relocate to low-density areas with newly accessible remote worker pools; others expand in the largest, most productive city centers as office space costs fall and the catchment area of workers widens.

In aggregate: the average worker lives 47% farther (in commuting time) from their workplace but spends 25% less time commuting, because average remote-work frequency rises by 1.1 days per week. The share of workers living in one commuting zone and working in another increases from 24.6% to 34%. Average income falls marginally by 1%, masking large gains for telecommutable workers and losses for non-telecommutable workers. Average floorspace prices fall by 2%; non-tradable prices rise by 2.6%. Overall welfare increases by an average of 12.7%, driven by gains for telecommutable workers, while non-telecommutable workers experience net losses.

The model predicts a partial reversal of the “Great Divergence”: skill sorting falls both within and across commuting zones, residential income inequality across CZs falls, and house price dispersion falls both within and across cities. These predictions are directionally consistent with 2019–2023 data.

Scope conditions: results are for a permanent shock to the full-time U.S. workforce as modeled in 2012–2016; the model does not predict the end of big cities but rather a reallocation at the margin. The model shows that the introduction of telecommuting narrows the parameter range guaranteeing a unique spatial equilibrium, because remote-capable firms can draw from a broader worker catchment area, amplifying agglomeration forces.

Q: What are the four stylized facts about pre-2020 telecommuting that discipline the model? A: Fact 1: telecommutability is higher for college workers and those in tradable industries — 68.8% of college-tradable workers can work from home versus 18.9% of non-college non-tradable workers. Fact 2: among telecommutable workers, uptake is also higher for college-tradable workers (38% actually work from home at least one day per week) than for non-college non-tradable workers (21%). Fact 3: the distribution of remote-work frequency is bimodal — most workers are either fully on-site or fully remote, with the bimodality less pronounced for college-tradable workers where hybrid (1–4 days/week) accounts for over 11% of paid workdays. Fact 4: there is a positive relationship between work-from-home frequency and distance from the job site, consistent with telework reducing effective commuting costs.

Q: How is the counterfactual shock calibrated and what drives it? A: The counterfactual raises remote-work productivity by 8–10% across all worker types and simultaneously reduces work-from-home aversion, guided by Barrero, Bloom, and Davis (2021) survey evidence that 25–30% of paid workdays will be remote post-pandemic, compared to about 8% in 2018. The authors consider both a technology shock (productivity increase) and a preference shock (aversion decrease) as mechanisms, consistent with their view that multiple hypotheses about the COVID-19 telework shock are plausible and non-exclusive.

Q: How do residents reallocate in response to the rise in telecommuting? A: Net reallocation of residents equivalent to nearly 5% of the population occurs. Telecommutable residents decentralize — moving to less dense areas with lower housing costs and better amenities — because the cost of choosing a residence far from work falls. Non-telecommutable residents partially centralize, moving toward denser locations in larger metro areas, because housing costs fall in locations with short commutes, making them more affordable.

Q: How do jobs reallocate? A: Non-tradable jobs follow the decentralization of residents (their source of demand) monotonically to less dense locations. Tradable jobs move in both directions: some firms relocate to low-density areas that can now access a larger pool of remote workers at lower real estate costs; others expand operations in the highest-productivity city centers, benefiting from both an expanded catchment of remote workers and a decline in the high cost of office space.

Q: What are the aggregate commuting implications? A: The average worker lives 47% farther in commuting time from their workplace in the counterfactual, yet spends 25% less time commuting, because average remote-work frequency increases by 1.1 days per week. The share of workers living in one commuting zone and working in another rises from 24.6% to 34%, which the authors note may call into question current administrative definitions of commuting zones and have major impacts on travel patterns.

Q: What are the welfare and income effects? A: Overall welfare increases by an average of 12.7%, but this masks very unequal distribution: telecommutable workers experience large gains while non-telecommutable workers suffer losses. Average worker income falls marginally by 1%, reflecting sizable gains for remote-capable workers offset by losses for those who cannot telecommute. Average floorspace prices fall by 2%, while non-tradable goods prices rise by 2.6%.

Q: What does the model predict for the “Great Divergence”? A: The model predicts a significant re-convergence across multiple dimensions: skill sorting falls both within and across commuting zones, residential wage inequality across CZs falls, and house price dispersion falls both within and across cities. The authors find that commuting zones with higher college shares in 2019 experienced slower growth in college shares 2019–2023, and that there is a negative correlation between average wages by CZ in 2019 and wage growth 2019–2023 — both consistent with model predictions.

Q: How does the model validate against post-2019 data? A: The authors show that their counterfactual results are positively correlated with observed changes in population, jobs, and housing rents since 2019. Within-city price variance has already converged in 2019–2023 data, consistent with model predictions. CZ-level patterns of skill concentration and wage growth also move in the direction the model predicts.

Q: Is the COVID-19 shock better described as a technology shock or a preference shock? A: The authors test both. To replicate observed changes in remote-work frequency using only a productivity shock requires a 55–99% jump in remote productivity, which yields implausibly large wage gains for remote-capable workers of 47–82%. The preference-based scenario yields results more consistent with observed data, supporting the view that a preference shock — changes in norms, attitudes, and institutional policies — is the primary driver.

Q: What happens to real estate prices when supply and amenities are held fixed? A: When real estate supply, productivity, and amenities are all held fixed, residential prices jump by 16% and commercial prices fall by 16%. The authors note this mimics the bifurcated shift in real estate values observed during the pandemic years, suggesting that supply responses and amenity adjustments are important for dampening the price effects in the full model.

Q: How does the model handle the uniqueness of spatial equilibrium, and how does telecommuting affect it? A: In a standard quantitative spatial model, agglomeration forces are dampened by the finite pool of workers willing to commute daily to a productive location. When telecommuting is introduced, productive locations can draw workers from a much broader catchment area, amplifying agglomeration forces and narrowing the range of parameter values for which a unique equilibrium is guaranteed. The authors establish conditions under which uniqueness is preserved.

Q: What are the model’s three main advantages over more stylized spatial models of remote work? A: First, by including 4,502 locations, the model can predict how far telecommuters will move from their jobs — a key variable for real estate markets and commuting patterns. Second, it can represent changes in the distribution of workers across different work-from-home frequencies, which is crucial as hybrid work has emerged as the dominant post-pandemic arrangement. Third, it predicts how the location of jobs (not just residents) changes, which has important implications for city centers.

Q: What is the overall welfare conclusion regarding non-telecommutable workers and income inequality? A: Non-telecommutable workers suffer welfare losses from the rise of remote work, even as overall average welfare rises by 12.7%. The overall income inequality — as opposed to spatial wage dispersion — does not fall. The authors note this means the spatial re-convergence does not translate into a broader reduction in income inequality, which they flag as an important limitation for policy.

Telecommutability: the ability of a worker’s occupation to be performed from home, measured using Dingel and Neiman (2020) occupational classifications; varies by education and industry, with 68.8% of college-tradable workers telecommutable versus 18.9% of non-college non-tradable workers.

Work-from-home aversion (ς): a preference parameter representing tastes, norms, and institutional policies that create non-pecuniary barriers to remote work; calibrated to range from 2.48 to 3.35 across worker types, higher for non-college workers in non-tradable sectors.

Hybrid work: an arrangement in which a telecommutable worker splits paid workdays between on-site and remote work (1–4 days per week from home); the model’s bimodal distribution of work-from-home frequency replicates the empirical observation that most workers are either fully on-site or fully remote, with hybrid most prevalent among college-tradable workers.

Catchment area: the pool of workers from which a firm can practically hire, which widens under telecommuting because workers no longer need to commute daily; this widening amplifies agglomeration forces and narrows the parameter range guaranteeing a unique spatial equilibrium.

Great Divergence: the multi-decade trend (documented in Moretti 2012 and related work) of spatially concentrating talent, income, and housing costs in a small number of large, high-skill cities; the paper predicts a partial reversal — “Great Re-Convergence” — driven by the rise of telecommuting.

Productive externalities (agglomeration): local productivity in the model depends on employment density; remote workers participate in these externalities only partially (parameter ψ ∈ [0,1]), so the shift to remote work can reduce agglomeration benefits in city centers.

Source text origin: the paper’s own classification of the text on which a summary is based (full PDF, open-access HTML, or abstract-only); the paper’s CLAUDE.md rules mandate that abstract-only summaries are blocked.

State Capacity as an Organizational Problem

Mon, 01 Jan 0001 00:00:00 +0000

Mastrorocco and Teso study how the internal organization of a state evolves during national development, framing state capacity as an organizational — specifically a principal-agent — problem. Using a new micro-database covering the U.S. federal bureaucracy from 1817 to 1905, they ask: once rulers have incentives to build a state apparatus, how do they organize it to perform its functions across a vast territory, and what drives transitions between organizational forms?

The dataset is constructed from every issue of the Official Register of the United States published between 1817 and 1905 (44 biennial volumes, 15,801 pages digitized). It records full name, state of birth, state of appointment, occupation, salary, department, office, and location for 304,410 unique federal employees across 810,942 employee-year observations. The authors reconstruct the bureaucracy’s four-layer hierarchy (department → office/bureau → division → local office), link employees over time to track careers, categorize all 11,930 occupation codes into five tiers, and geo-code 9,651 places of employment to 1890 county boundaries.

The paper first documents three sets of descriptive facts. On growth: the federal workforce expanded very slowly before the 1860s and then rapidly, with geographic expansion accounting for none of state growth before 1859 but roughly 29% after. On location: state presence responded positively to local manufacturing activity (a one standard deviation increase in manufacturing employment share raises presence probability by 1.3 percentage points), but distance from Washington DC significantly attenuated this relationship in 1817–1859 and not in 1861–1905. On organization: before the 1860s, employee turnover was high and spiked sharply at presidential transitions (reaching 72% of employees departing in 1861), supervisors’ departures strongly predicted subordinates’ departures (a one-for-one supervisor exit raised subordinate turnover probability by 37% pre-1841), and managerial delegation outside DC was stagnant or declining. After the 1860s, turnover trended down (35% at the 1897 transition), the supervisor-subordinate career link weakened materially, and field managers tripled relative to the 1850s.

The authors argue that high monitoring costs in the early century made trust-based, personalistic organization the second-best solution to principal-agent problems. The limited supply of sufficiently trusted individuals constrained geographic expansion, delegation, and total size. As railroad and telegraph networks lowered communication and transportation costs, monitoring capacity increased, enabling a transition to a Weberian bureaucracy no longer constrained by trust supply.

The causal identification strategy uses the staggered expansion of the railroad network. For each county and decade (1820–1900), the authors compute the minimum-travel-time route from the county centroid to DC using Donaldson and Hornbeck (2016) data on railroads, steamboat waterways, coastal routes, and land routes. The specification includes county fixed effects, state-by-decade fixed effects, and controls for local railroad presence in the county and for the county’s market access, so the identifying variation comes from distant changes in the network that altered travel time to DC without directly affecting the county’s local economy or trade access.

Results: a one standard deviation decrease in travel time to DC raises the probability of federal state presence by approximately 3 percentage points (about 8% of the mean), raises log employment similarly, raises the probability of observing a local managerial layer by approximately 3 percentage points (about 8% of the mean), and reduces employee turnover by approximately 2 percentage points (about 4% of the mean turnover rate). Placebo tests confirm that travel time to other major economic centers does not predict state presence. Telegraph network data (1845–1852, Wang 2020) yield consistent results. An additional test using the post-Civil War decline in Southern-born employee shares shows that better railroad connection to DC narrowed the North-South employment gap, consistent with monitoring substituting for trust-based selection.

Scope conditions: the paper covers the civilian executive branch of the federal government, excluding the Postal Office, navy yards, and the engineer department; results are robust to restricting to states already in the union at the start of the sample, ruling out frontier-specific dynamics.

Q: What is the central theoretical claim of the paper? A: The paper argues that state capacity is fundamentally an organizational problem shaped by principal-agent constraints. When communication and transportation costs are high, the government cannot effectively monitor distant agents, so the second-best solution is to staff the bureaucracy with trusted individuals connected through personal networks. This personalistic form limits size and delegation because the supply of sufficiently trusted individuals is inherently scarce. Technological reductions in monitoring costs allow a transition to a Weberian bureaucracy based on procedural oversight rather than trust, removing the supply constraint on organizational growth.

Q: What data source does the study rely on, and what time period does it cover? A: The study draws on the Official Register of the United States, a biennial government publication listing all federal employees, digitized for every issue from 1817 to 1905. The resulting dataset includes 304,410 unique employees and 810,942 employee-year observations, with each record carrying name, state of birth, state of appointment, occupation, salary, department, office, location, and — through hierarchical reconstruction — position in a four-layer chain of command.

Q: How did the size of the U.S. federal bureaucracy evolve over the nineteenth century? A: Growth was slow before the 1860s. The first Register for 1817 listed 1,056 employees across 33 pages; the 1905 volume listed over 120,000 employees across 1,254 pages. Geographic expansion contributed zero to state growth before 1859 — the share of counties with any federal employee hovered around 15% from 1817 to 1859 — but contributed approximately 29% of growth after 1859, when county presence rose to 24% by 1871, 38% by 1881, and 61% by 1905.

Q: What were the three sources of state growth, and how did their relative importance change? A: The authors decompose growth into: (1) functions (new offices/bureaus), (2) geographic expansion (new counties), and (3) intensity (more employees per county-office pair). Before 1859, growth was entirely driven by functions (~40%) and intensity (~60%), with zero contribution from geographic expansion. After 1859, geographic expansion accounted for ~29%, intensity for ~32%, and functions for ~39% of growth.

Q: How did employee turnover behave across the century, and what pattern emerges at presidential transitions? A: Turnover trended upward through the late 1850s and then declined. During presidential transitions, the rate rose from 52–53% in 1841 and 1845 to 60–63% in 1849 and 1853 and peaked at 72% in 1861; it then fell to 55% in 1869, 44–48% in 1885/1889/1893, and 35% in 1897. Turnover was consistently lower in DC than in the field: controlling for year-bureau-position fixed effects, being employed in DC was associated with a 40% reduction in turnover probability.

Q: How tight was the link between supervisors’ and subordinates’ careers, and how did it change? A: Before 1841, moving from none to all supervisors leaving an organizational unit increased subordinate turnover probability by 37 percentage points. The effect was similar between 1841 and 1859, then dropped substantially to 22 percentage points in the following twenty-year period, and remained roughly constant after 1881. This pattern is consistent with the early bureaucracy relying on chains of personal trust that broke when a supervisor departed.

Q: What evidence describes the evolution of delegation outside DC? A: The number of field managers did not grow between 1817 and 1859 — it actually declined in the 1820s and was flat through the mid-1850s — and then tripled by 1905 relative to the 1850s level. The probability that workers in a local office had an additional managerial layer between them and DC was unchanged between pre-1841 and 1841–1859, increased by 5 percentage points between 1861 and 1881, and by 6 percentage points post-1881.

Q: How does the paper measure monitoring capacity for the causal analysis? A: The primary measure is travel time in hours from each county centroid to Washington DC, computed decade by decade (1820–1900) as the minimum-cost route across the available railroad network, steamboat waterways, coastal routes, and land routes, using data from Donaldson and Hornbeck (2016). A second, complementary measure is the number of telegraph connections between a county and DC using data from Wang (2020) for 1845–1852.

Q: What is the identification strategy for the railroad analysis, and why are controls for local railroads and market access important? A: The specification includes county fixed effects, state-by-decade fixed effects, an indicator for whether the county itself has railroad (LocalRailroad), and the county’s market access. County fixed effects mean beta is identified within-county from changes over time. Controlling for local railroad removes the direct correlation between local construction and local economic growth. Controlling for market access removes the effect of distant rail expansion on trade flows that raised agricultural land values and manufacturing activity. The remaining variation in travel time to DC — coming from distant network changes that altered the DC-county connection without affecting local conditions or broader trade access — is the identifying source.

Q: What are the main quantitative effects of reduced travel time to DC? A: A one standard deviation decrease in travel time to DC is associated with: (1) approximately 3 percentage point increase in the probability of federal state presence (~8% of the mean); (2) a similar magnitude increase in log employment conditional on presence; (3) approximately 3 percentage point higher probability of an additional managerial layer (~8% of the mean); and (4) approximately 2 percentage point reduction in employee turnover (~4% of the mean turnover rate).

Q: How do placebo tests support the monitoring interpretation? A: The authors show that, conditional on the same controls, travel times from a county to a set of other major economic centers are not associated with larger federal state presence. Since these other cities had no role as monitoring headquarters, the absence of an effect for them and the presence of an effect specifically for DC is consistent with the channel operating through the government’s ability to supervise agents from the capital, rather than through generic economic connectivity.

Q: What does the telegraph evidence add, and what is its limitation? A: Telegraph data (1845–1852, Wang 2020) show that counties with more telegraph connections to DC have larger state presence, more managerial delegation, and lower turnover, consistent with the monitoring mechanism. The limitation is that the authors have limited ability to address the endogeneity of telegraph network timing — the telegraph analysis is treated as corroborating evidence rather than the primary causal identification.

Q: How do the Southern-born employee results illuminate the trust mechanism? A: After the Civil War, the share of Southern-born federal bureaucrats fell sharply, consistent with reduced trust toward individuals from former Confederate states. However, counties that became better connected to DC via railroad expansion experienced a relative increase in the share of Southern-born employees. This shows that when monitoring costs fell, the government was willing to hire individuals from groups with lower baseline trust — monitoring substituted for trust as the mechanism ensuring agent performance.

Q: Does federal state presence crowd out state and local government? A: No. The presence of federal bureaucrats is positively correlated with the presence of state and local government employees at the county level, suggesting complementarity rather than substitution across levels of government.

Q: What alternative mechanisms do the authors consider and how do they address them? A: Three alternatives are discussed. First, demand shocks (Civil War debt repayment, industrialization) could explain the post-1860s expansion; the empirical specifications control for year fixed effects to absorb aggregate time-varying incentives, and the identification relies on differential cross-county variation in DC connectivity. Second, patronage as an electoral tool is consistent with spoils-driven turnover spikes but cannot explain why better-connected counties show lower turnover before civil service reform. Third, cognitive models of the firm (lower communication costs complement managerial problem-solving even without agency problems) could also predict the positive delegation result; the authors note they cannot empirically distinguish the monitoring and cognitive channels, and both may contribute.

Q: What are the implications for developing countries today? A: The authors suggest that their findings from nineteenth-century U.S. history may apply to understanding why modern Weberian bureaucracies remain elusive in many developing countries. Where communication infrastructure is limited and monitoring costs remain high, personalistic organizational forms based on trust networks may persist as constrained optima — not failures of will or design, but rational responses to structural conditions. Infrastructure investment that lowers monitoring costs could be a precondition for bureaucratic modernization.

Personalistic state organization: The paper’s term for the organizational form that prevails when monitoring costs are high. It is characterized by staffing decisions based on personal character, moral reputation, and relationships of trust between principals and agents — and between supervisors and subordinates — rather than on formal procedural monitoring of performance. Frequent turnover at leadership transitions and constrained delegation are defining features, because the supply of trusted individuals is limited.

Weberian bureaucracy: In the paper’s usage (following Weber 1978), a modern state organization defined by a fixed hierarchy of officials monitored through procedural rules rather than personal trust, lower turnover, and effective delegation of managerial power to geographically dispersed units. The paper treats this as the organizational form enabled by low monitoring costs.

Monitoring capacity: The principal’s (politicians in DC and their cabinets) ability to observe and evaluate the behavior of agents (federal employees) throughout the territory. In the paper’s operationalization, monitoring capacity is proxied inversely by travel time and communication cost between DC and the county: lower travel time and more telegraph connections mean higher monitoring capacity.

Geographic expansion component: One of three decomposed sources of state growth. Defined as the increase in state size attributable to the state becoming present in more county locations. This component contributed zero to federal growth before 1859 and approximately 29% of growth after 1859.

Employee turnover: In the paper’s measurement, the share of employees who leave the federal bureaucracy in a given year. The paper distinguishes politically-driven spikes at presidential transitions — reaching 72% of employees in 1861 — from the secular trend, which rose through the late 1850s and then declined, reaching 35% by the 1897 transition.

Delegation of managerial power: The probability that a local county office has an additional managerial layer between its workers and DC, rather than reporting directly to the bureau-level supervisor in Washington. The paper uses this as its measure of whether decision authority has been decentralized to the field.

Trust substitution: The paper’s mechanism linking monitoring capacity to organizational form. In the absence of effective monitoring, principals substitute trust for oversight — selecting agents whose personal loyalty, moral character, or political alignment gives the principal confidence they will not shirk or defect. As monitoring costs fall, trust becomes less necessary as a screening device, and the trust-constrained supply limit on organizational growth is relaxed.

Structural Change, Land Use and Urban Expansion

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks how cities grow in the process of structural transformation — specifically, whether urban expansion occurs at the intensive margin (higher density within a fixed area) or the extensive margin (larger area). The authors document and explain a persistent decline in urban density in France since 1870, and develop a spatial general equilibrium model in which endogenous land use — land allocated either to agriculture or housing — is the key mechanism linking structural change to urban sprawl.

The central empirical fact is striking: between 1870 and 2015, the area of the 100 largest French cities increased by a factor of roughly 30, while their population grew by only a factor of about 4, implying that average urban density fell by a factor of roughly 8. This density decline was fastest over 1950–1975, coinciding with the acceleration of structural change (France’s rural exodus). Since the mid-nineteenth century, approximately 15% of French land has been reallocated away from agricultural use — more than the total artificially-used land in France today (about 9%).

The theoretical mechanism operates through the opportunity cost of urban expansion. Agricultural land at the urban fringe must earn its marginal product in the rural sector; this agricultural rent pins down the cost of converting land to urban use. When agricultural productivity is low, farmland is expensive relative to income (the “food problem”), households devote large shares of resources to food, and cities remain small in area and very dense. As agricultural productivity rises — the engine of structural change — workers leave rural areas, farmland values fall relative to income, and cities can expand cheaply at their fringes. Simultaneously, richer households spend more on housing. Both forces cause urban area to grow faster than urban population, generating a sustained decline in average density.

The model also predicts a “hockey-stick” path for housing prices: during structural change, the extensive margin expansion of cities limits the rise in urban land rents despite growing housing demand. Once the reallocation of workers and land out of agriculture slows, urban land values must adjust upward rapidly, producing the pattern documented by Knoll et al. (2017) — relatively flat housing prices until roughly the 1950s, then steep increases.

The model is a multi-city, multi-sector spatial equilibrium framework with non-homothetic CES preferences (including a subsistence requirement for the agricultural good), endogenous city fringes determined by land market clearing between agricultural and residential uses, and a monocentric commuting structure with endogenous commuting speed (workers adopt faster modes as wages rise). The model is calibrated to French historical data spanning 1840–2015, with 20 regions whose sectoral productivities are estimated to match regional urban populations and local farmland prices.

Quantitatively, the calibrated model accounts for approximately 70% of the increase in urban area since 1870, most of the decline in average urban density (the factor-of-8 fall), about half of the rise in real housing prices, and most of the reallocation of land values from agricultural to urban. Cross-sectional evidence confirms a core prediction: cities surrounded by more expensive farmland are denser, with an IV-estimated elasticity of urban density with respect to farmland prices of approximately 0.3 (a 10% increase in farmland prices raises urban density by about 3%), consistent with the model’s counterpart. Scope conditions include the focus on France as a single country case, reliance on a monocentric urban structure, and the abstraction from within-urban-sector reallocation (manufacturing to services).

Q: What is the central stylized fact motivating the paper? A: Between 1870 and 2015, the area of the 100 largest French cities increased by a factor of roughly 30, while their total population grew by a factor of about 4, so average urban density fell by a factor of roughly 8. This density decline was most rapid over 1950–1975, coinciding with France’s peak rural exodus, and has barely fallen since — tracking the slowdown of structural change. This pattern is not unique to France; Angel et al. (2010) document persistent urban density decline on a global scale.

Q: What is the paper’s key theoretical mechanism linking structural change to urban sprawl? A: The rental price of agricultural land at the urban fringe is the opportunity cost of expanding the city into surrounding farmland. When agricultural productivity is low, farmland is expensive relative to income, keeping cities small and dense. As productivity rises and workers migrate to cities, the value of agricultural land falls relative to income, reducing the cost of urban expansion at the fringe. Richer households also devote a larger share of spending to housing, reinforcing the demand for space. These two channels together cause city area to grow faster than city population, generating a sustained decline in average density — even without any improvement in commuting technology.

Q: How does the paper distinguish between the structural change channel and the commuting cost channel? A: The model contains both channels: structural change (falling agricultural land values at the fringe) and falling effective commuting costs (rising wages lead workers to adopt faster commuting modes, a wage elasticity of commuting speed calibrated from survey data). Counterfactuals show that without structural change (rural productivity growth set to 4% of baseline), the model cannot replicate the observed density decline. Without faster commutes (setting the income elasticity of commuting speed to unity), the model predicts only about 30% of the baseline density decline. Both channels are necessary; their combined effect exceeds the sum of parts because structural change raises wages, which in turn amplifies the commuting speed mechanism.

Q: How do the two channels differ in their spatial imprint within cities? A: Structural change adds new low-density settlements at the urban fringe, so suburban density falls more than average density — the center is relatively less affected. Faster commuting modes, by contrast, induce suburbanization: workers relocate from the center outward, so central density falls more than average density. For Paris, historical data show that central density fell less than average urban density, which is consistent with both mechanisms operating simultaneously — the commuting channel pushing central density down more, but the structural change channel adding fringe expansion that affects suburban density more.

Q: What is the empirical evidence on the cross-sectional farmland price prediction? A: Using data on local farmland transaction prices from the French Ministry of Agriculture at the “Petite Region Agricole” level (over 700 areas), the authors show that cities surrounded by more expensive farmland are denser. A binned scatter plot across 200 French cities shows that moving from the first to last decile of farmland prices raises density by about one third — an effect comparable in magnitude to an increase in population from roughly 25,000 (3rd decile) to 150,000 (9th decile). To address endogeneity (productive cities may inflate nearby farmland prices), the authors instrument farmland prices with soil quality characteristics; the IV elasticity of urban density with respect to farmland prices is approximately 0.3, consistent with the model’s predicted counterpart.

Q: What does the model predict about the time path of housing prices? A: The model predicts a “hockey-stick” pattern: housing prices remain relatively flat for decades while structural change is ongoing, because cities expand cheaply at the extensive margin, absorbing growing housing demand without large rent increases. Once the reallocation of workers and land out of agriculture slows, the extensive margin ceases to buffer demand, and urban land values must rise sharply. The calibrated model accounts for about half of the observed rise in real housing prices since the mid-nineteenth century; it matches the qualitative hockey-stick pattern documented by Knoll et al. (2017) and Piketty and Zucman (2014) for France and advanced economies more broadly.

Q: What happens to the relative values of agricultural versus urban land over the period? A: Agricultural land values relative to income fall dramatically: the average value of a French agricultural field per unit of land, as a share of per capita income, was divided by a factor of 15 between 1850 and 2015. Meanwhile, urban land values rise. In 1820, agricultural land accounted for more than 70% of total housing and land wealth in France; by 2010 this share had fallen to about 3%. This reallocation of land values from rural to urban is a central prediction the model accounts for, driven by structural change reducing the scarcity premium on farmland.

Q: How is the model parameterized and calibrated? A: Preferences are non-homothetic CES with housing preference parameter gamma = 0.22, subsistence consumption for the rural good calibrated to match the 1840 agricultural employment share (about 60%), and substitution elasticity between urban and rural goods sigma = 0.8. The labor share in agriculture is alpha = 0.6. Commuting cost parameters (elasticities to wages and distance) are estimated from the French Labor Force Survey (Enquete Emploi). Region-specific sectoral productivity parameters for 20 regions (40 parameters total) are estimated to match the cross-section of urban populations and local farmland values in the base year 1870. The model is then simulated forward to 2015.

Q: What share of French land has been reallocated away from agriculture, and how does this relate to urban expansion? A: About two-thirds of French land was used for agriculture in 1840; by 2015 this fell to 52%, implying roughly 15 percentage points of French territory reallocated away from agricultural use. This 15% exceeds the total land currently under artificial use in France (about 9%). Over the more precisely measured period 1982–2015, artificialized soil increased by about 2 million hectares (3.7% of French territory), representing roughly 70% of the land converted away from agriculture over the same period. Two-thirds of land surrounding French cities is agricultural, confirming that urban expansion occurs at the expense of farmland.

Q: What are the limitations and directions for future research acknowledged by the authors? A: The model relies on a monocentric urban structure where all workers commute to a single city center, which is an approximation — commuting distance increases with residential distance to the center but less than one-for-one, suggesting workers sort into nearby jobs. The model also abstracts from within-urban-sector reallocation (the manufacturing-to-services transition), which the authors conjecture matters for the cross-section of cities in recent times. Finally, the model cannot fully replicate the steep recent rise in housing prices, which the authors attribute partly to land-use regulations constraining extensive margin growth — a policy counterfactual the general equilibrium structure is well-suited to analyze.

Q: How does the paper relate to the Ricardo/Nichols view that land values should rise with economic development? A: The traditional Ricardian view predicts that a fixed factor like land must rise in value with economic development — counterfactual given the historical data showing farmland values falling sharply relative to income. The authors reconcile this with the data by emphasizing that structural change and agricultural productivity growth reduce the scarcity of farmland even as total income grows, so farmland values fall. Urban land values do rise, but the structural change channel initially dampens this increase by facilitating extensive-margin city growth. The paper thus reconciles the Ricardian fixed-factor view with the commuting technology view (Miles and Sefton, 2020) within a unified spatial structural change framework.

Endogenous land use: In this paper’s framework, land in each region is allocated either to agricultural production or to residential use, with the margin between the two determined in equilibrium by the equality of the rental price of land at the urban fringe and the marginal product of land in the rural sector. This makes the urban-rural land boundary an endogenous object that responds to structural change.

Urban fringe (phi_k): The furthest residential location of an urban worker in city k, determined endogenously as the commuting distance at which the opportunity cost of further expansion (the agricultural land rent) equals the willingness of urban workers to pay for land. All workers beyond this fringe produce rural goods without commuting.

Structural change (in the paper’s sense): The reallocation of workers and land away from agriculture driven jointly by non-homothetic preferences with a subsistence consumption requirement for the agricultural good (demand side) and rising sectoral productivity (supply side). Structural change is the primary driver of falling farmland values and urban sprawl in the model.

Non-homothetic CES preferences: Household preferences over rural and urban goods that are not homogeneous of degree one in income, specified as a CES aggregate with a subsistence floor for the rural (agricultural) good. At low income levels, households devote large budget shares to food; as income rises, spending shifts toward urban goods and housing. This demand-side non-homotheticity is the channel through which rising income generates structural change.

Food problem (Schultz, 1953): The condition in which low agricultural productivity forces households to devote a large fraction of resources to meeting subsistence food needs, leaving little for housing expenditure. In the paper’s model, the food problem makes cities initially small and very dense; as agricultural productivity rises and the food problem relaxes, cities can expand in area.

Commuting cost function tau(l_k): Spatial frictions proportional to the worker’s distance from the city center and the urban wage, of the functional form tau(l_k) = a * w_{u,k}^{xi_w} * l_k^{xi_l}, where xi_w in (0,1) captures the endogenous adoption of faster commuting modes as wages rise. Concavity in both arguments is micro-founded by an optimizing commuting mode choice model, ensuring that the share of resources devoted to commuting falls as incomes rise.

Hockey-stick housing price path: The model’s prediction that real housing prices remain relatively flat over the period of active structural change — because city expansion at the extensive margin absorbs rising housing demand without large rent increases — before rising steeply once structural change slows and the extensive margin is exhausted. This prediction matches the empirical pattern documented by Knoll et al. (2017) for France and other advanced economies.

Subjective Earnings Risk

Mon, 01 Jan 0001 00:00:00 +0000

The paper introduces a survey instrument — fielded in the Copenhagen Life Panel in January 2021 to about 10,900 employed Danes aged 20-65 — that measures how much earnings risk workers subjectively perceive over the year ahead, conditioning explicitly on whether they expect to stay in their job, quit, or be laid off. Linking each survey response to third-party-reported Danish administrative records provides multiple credibility checks: survey-reported past earnings, job-transition probabilities, and time out of work line up closely with their registry counterparts. The central finding is that subjective earnings risk is many times smaller — the authors report administratively-estimated risk being between two and six times higher — than the risk conventionally inferred from the cross-sectional dispersion of realized earnings growth. The authors attribute this gap to heterogeneity: even within narrow age-and-earnings cells, workers differ systematically in expected earnings growth, so pooling them misassigns predictable differences in means to luck (a mixture-distribution / Jensen’s-inequality argument), and the gap is largest where expected-growth heterogeneity is largest, such as among young workers. Possible job transitions are shown to be central to the level and the higher-order shape (skewness, kurtosis) of subjective risk. When a standard life-cycle search-and-matching model (Menzio, Telyukova, and Visschers, 2016) is calibrated to the administrative data in the usual way, its model-implied beliefs imply far higher individual earnings risk than workers report, whether or not they switch jobs — which the authors read as highlighting the value of survey-based measures for disciplining such models.

In depth

Q1. What gap does the paper document between subjective and administratively-estimated earnings risk?

Directly measured subjective earnings risk is many times lower than earnings risk inferred from administrative data — administratively-estimated risk is between two and six times higher than its survey-based counterpart across age-and-earnings cells. Risk is measured as the interdecile range (p90 minus p10) of the distribution of one-year-ahead earnings growth. Partitioning the Danish population into 300 cells by three age groups (20-34, 35-49, 50-65) and earnings percentiles following Guvenen et al. (2021), the average of individuals’ subjective interdecile ranges within a cell is much smaller than the interdecile range of realized earnings growth computed from the administrative data in that same cell.

Q2. Why do the two measures diverge?

The divergence arises because expected earnings growth is heterogeneous even within narrow demographic and earnings cells, so the cross-sectional dispersion of realized earnings misassigns ex-ante differences in means to luck. The pooled distribution of earnings growth is a mixture of individuals’ subjective distributions; by a variance-of-a-mixture decomposition (and Jensen’s inequality), the variance of the pooled distribution is weakly larger than the average of the individual subjective variances, with the excess reflecting differences in subjective means. Consistent with this channel, the gap between subjective and administrative risk is particularly high for groups with highly heterogeneous expected growth rates, such as younger workers, and the authors report the gap narrows as the stratification is refined — results are practically identical with an even finer 1,800-cell grid or when an individual past-growth-rate covariate is added.

Q3. How credible are the subjective survey measures?

A link to third-party-reported Danish administrative records provides multiple credibility checks, and on each the survey aligns closely with the registry. Survey-reported last-year earnings match their administrative counterpart; the average reported probability of staying with the same employer tracks the administrative share of stable job matches by age; average expected time out of work following a separation matches registry durations; and life-cycle patterns of all four moments (mean, interdecile range, skewness, kurtosis) of pooled expected earnings growth mirror those of realized administrative earnings growth. The authors note COVID-19 hit the Danish economy only lightly in 2020 (the lowest employment level was only about 40,000 below the roughly 2.77 million pre-pandemic baseline, two-thirds recovered by year-end), limiting concerns about pandemic distortion.

Q4. What did the survey reveal about expected job transitions and earnings by branch?

On average respondents assign an 82% probability to staying with their current employer, 12% to quitting, and 6% to being laid off, and they expect markedly different earnings outcomes across these branches. The average respondent expects a 3% earnings increase if staying, an 11% decrease upon reemployment after a layoff, and a 7% increase after a quit. Among those reporting a positive layoff probability, 73% expect earnings to fall if laid off; among those reporting a positive quit probability, 81% expect earnings to rise if they quit. Expected time out of work averages about 4.4-4.6 months after a layoff and about 2.7 months after a quit; the authors note that expecting positive time out of work after a quit contrasts with the standard registry-based assumption that quits correspond to direct job-to-job transfers.

Q5. What role do job transitions play in the structure of subjective risk?

Possible job transitions are shown to be central determinants of the level and the higher-order moments of subjective earnings risk. Fixing risk to the “stay” branch sharply reduces perceived uncertainty at all ages — most dramatically for the young — and largely removes both the negative skewness and the substantial excess kurtosis (about 10-20 on the holistic measure) present in the holistic distribution. The authors read this as indicating that job transitions are, in expectation, responsible for the downside and extreme-change risk that workers perceive.

Q6. Does a standard calibrated search model reproduce these subjective beliefs?

A life-cycle directed-search model (Menzio, Telyukova, and Visschers, 2016), calibrated in the standard manner to Danish administrative transition and wage data, produces far higher estimates of individual earnings risk than workers subjectively report, even conditioning on job transitions. The model matches average branch probabilities and reemployment durations well (model stay/EU/EE probabilities of 84%/6%/10% against survey 82%/6%/12%, and 4.2 vs 4.4 months out of work), but its conditional earnings-growth distributions are too dispersed and too homogeneous: on the stay branch it generates a double-peaked distribution absent from the survey, and on the quit and layoff branches the interdecile ranges are much higher and less heterogeneous than reported. The authors trace this to features common to search models — workers “starting from the bottom” of the job ladder after unemployment and match quality being initially unknown — and argue these features, which are not unique to this model, are why such models overstate risk relative to elicited beliefs.

Q7. What does the paper conclude about how earnings risk should be measured and used?

The authors conclude that survey-based measures of subjective earnings risk carry information that administrative-data inference and standard calibrated models miss, and that they are valuable for modeling labor-market transitions and other choices affected by earnings risk, such as savings and portfolio decisions. As suggestive evidence linking beliefs to behavior, they regress expected time out of work after a quit on liquid assets relative to disposable income and find that workers with less liquid wealth expect to spend less time out of work after quitting, as if pressured back to work more quickly. The paper frames its contribution as reviving and extending Dominitz and Manski’s (1997) thesis that administratively-estimated earnings risk may differ significantly from its subjective, survey-estimated counterpart.

Key concepts

Subjective earnings risk : earnings risk as perceived and reported by workers themselves about their own one-year-ahead earnings, elicited as full probability distributions conditional on possible job transitions, rather than inferred from the dispersion of realized earnings across workers.

Holistic (expected) earnings growth : an individual’s overall subjective distribution over next year’s earnings growth, formed by weighting the stay, quit, and layoff branch distributions by the subjective probabilities of each transition and the associated time out of work.

Administratively-estimated earnings risk : risk inferred from the cross-sectional distribution of realized earnings growth within demographic/earnings cells (as in Guvenen et al., 2021), which relies on the assumption that workers within a cell draw from the same underlying distribution.

Interdecile range (p90 minus p10) : the quantile-based measure of dispersion the paper uses to summarize “risk” in earnings growth, chosen for robustness relative to the variance.

Balls-in-bins elicitation : a graphical survey method (Delavande and Rohwedder, 2008) in which respondents allocate 20 balls — each interpreted as 5% probability — across earnings bins to report a subjective probability distribution.

Mixture-distribution (heterogeneity-as-risk) channel : the result that a population distribution pooling heterogeneous individual means has variance weakly larger than the average individual variance, so pooling predictable differences in means inflates measured “risk.”

Key concepts

Interdecile range (p90 minus p10) : the quantile-based measure of dispersion the paper uses to summarize “risk” in earnings growth, chosen for robustness relative to the variance.

Taxes Depress Corporate Borrowing: Evidence from Private Firms

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

Does corporate income taxation raise or lower corporate leverage? The canonical Modigliani-Miller (1963) view holds that the interest tax deduction makes debt more attractive, predicting a positive taxes-to-leverage relationship. Most prior empirical work using large public firms confirms this prediction. This paper re-examines the question using data on small private U.S. firms and finds the opposite: higher corporate taxes depress leverage, at least for small, financially constrained private firms.

Data and Identification

The primary dataset is the Federal Reserve’s Y-14Q supervisory collection (2011–2017), which covers the loan portfolios of the 33 largest U.S. banks and includes firm-level income statements and balance sheets for privately held, bank-dependent borrowers. The sample is restricted to domestic private C-corporations with prior-year assets above $100 million (to screen for pass-through entities), yielding 39,363 non-singleton firm-year observations. The median firm has $288 million in book assets and total debt-to-assets of approximately 38%. A supplementary dataset from the Shared National Credit (SNC) Program (1993–2018, 50,203 firm-year observations) provides a longer time series on syndicated loan commitments. Public firm comparisons use CRSP-Compustat (91,314 observations, 1989–2017).

The empirical strategy is a difference-in-differences event study using variation in state corporate income tax rates. A novel contribution is the manual collection of both enactment dates (when legislation was signed into law) and effective dates for each state tax change since 1975. Identification follows the narrative approach of Romer and Romer (2010) and Giroud and Rauh (2019) to exclude tax changes endogenous to local economic conditions. The specification includes firm and industry-by-year fixed effects, and the analysis uses heterogeneity-robust estimators (Borusyak et al. 2024; de Chaisemartin and D’Haultfoeuille 2020) to address staggered treatment timing.

Main Empirical Findings

For small private firms (below-median total assets, i.e., below $288 million), long-term debt-to-assets rises by approximately 4% in the year of tax cut enactment and remains elevated—at approximately 2%—four or more years later, indicating a permanent increase in leverage. This anticipation effect arises because firms respond to the law’s passage, not its effective date; results using effective dates are noisy and largely insignificant. The average tax cut during the sample period was 1.2 percentage points, representing approximately a 6% reduction in firms’ tax bills (given an average private-firm tax rate of 21%), and the implied leverage change of about 6% at year four is correspondingly large, consistent with a low-interest-rate environment in which small changes in marginal q translate into large investment and borrowing responses.

For large private firms (above-median assets), leverage shows no significant response to tax cuts in any event year. For public firms, evidence of any effect is scant, with at most transient significance and pre-trend issues that complicate interpretation.

Mechanism

The paper argues two tax-sensitive costs of debt offset the standard interest tax shield. First, a higher tax rate reduces after-tax profits, raising default probabilities and credit spreads endogenously; a tax cut thus lowers credit spreads and incentivizes more borrowing. Second, because external equity finance is either unavailable or very costly for small private firms, debt and capital are complements in financing investment: a tax cut raises the marginal product of capital, inducing firms to invest and borrow more. For small firms with low capital adjustment costs, this capital-debt complementarity dominates the direct loss of interest tax shield value. For large firms with high capital adjustment costs (estimated at nine times the small-firm value), investment responds sluggishly to tax changes, the complementarity effect is muted, and the traditional tax shield effect becomes relatively more important—producing the standard, slightly positive taxes-to-leverage relationship.

Bank-assessed default probabilities fall by 20–30 basis points (roughly a 10% decline from an average of approximately 2%) in the year of enactment or one year later for small borrowers, directly supporting the model’s credit spread mechanism.

Welfare Counterfactual

Removing the interest tax deduction from the estimated model (while retaining profit taxation and restricted equity access) causes leverage to fall from 0.36 to −0.26. Firms substitute into cash holdings, shrinking the capital stock. In equilibrium, hours worked rise, the real wage falls, and consumer welfare drops by approximately 1.8%. The interest deduction thus raises welfare in a second-best sense by offsetting other frictions that impede optimal capital accumulation.

In depth

Q1. Why do prior studies find a positive taxes-to-leverage relationship, and how does this paper differ?

Prior studies—including Titman and Wessels (1988), Heider and Ljungqvist (2015), and Faccio and Xu (2015)—predominantly use large public firms, for which the interest tax shield is the quantitatively dominant consideration. The present paper focuses on small private firms that face greater financial frictions (restricted equity access, higher default risk), in which two additional tax-sensitive costs of debt become quantitatively important. A further methodological difference from Heider and Ljungqvist (2015) is the use of firm fixed effects rather than first differences, which the authors argue is appropriate in a staggered DiD design.

Q2. Why use enactment dates rather than effective dates as the event?

Tax legislation is often signed into law one to two years before taking effect; in the sample of 125 tax packages since 1975, 33 became effective the following year and 13 became effective two or more years later. Firms that anticipate future tax changes will adjust leverage immediately upon enactment, not at the effective date. Results confirm this: event studies using enactment dates yield precise positive estimates for small firms (ranging from ~4% at year 0 to ~2% at year 4+), while results using effective dates are noisy and mostly insignificant. The paper therefore treats the enactment date as the economically relevant event and collects these dates as a novel contribution.

Q3. What is the economic magnitude of the leverage response for small private firms?

Small firms’ long-term debt-to-assets rises by almost 4% in the enactment year and remains elevated at approximately 2% four or more years after enactment, consistent with a permanent adjustment. The average tax cut during the period was 1.2 percentage points, representing roughly a 6% reduction in the average tax bill (given an average effective rate of 21% for private firms, per Zwick et al. 2016). The estimated coefficient of 0.021 in year four also implies approximately a 6% change in leverage, a large response that the paper attributes to the low interest rate environment amplifying the marginal q effect of even modest tax changes.

Q4. Do large private firms respond differently to tax cuts, and why?

Large private firms (above the median of $288 million in total assets) show no statistically significant leverage response to tax cuts in any event year, and this null is not attributable to wider confidence intervals. The model estimation explains this via capital adjustment costs: the adjustment cost parameter for large firms is estimated to be nine times larger than for small firms. With high adjustment costs, investment responds sluggishly to a tax cut, so the complementarity channel (more investment requires more debt) is suppressed. The traditional tax shield effect then becomes relatively more important, producing a slightly positive (or zero net) taxes-to-leverage relationship consistent with the large-firm data moment.

Q5. How does the model generate a negative relationship between taxes and leverage when the interest tax deduction is present?

Two mechanisms offset the tax shield. First, higher taxes reduce after-tax profits, pushing firms closer to the default threshold; this is capitalized into equilibrium credit spreads, raising the cost of debt. Specifically, for small firms, the model shows that once leverage exceeds approximately 0.47 of assets, the after-tax risky interest rate rises monotonically with the tax rate (rather than falling via the deduction effect). Second, capital and debt are complements in financing investment: because a tax cut raises the marginal product of capital, and because external equity is unavailable, firms substitute into capital by using more leverage. For small firms with low capital adjustment costs, both mechanisms outweigh the loss of interest tax shield value when taxes fall.

Q6. How are the model parameters estimated, and what are the key parameter values?

The model is estimated by simulated method of moments on the Y-14 small-firm sample, minimizing the distance between nine data moments and their model-simulated counterparts. The nine moments include the means and standard deviations of debt, investment, and operating income (all as ratios of assets), the serial correlations of investment and operating income, and the coefficient from a two-way fixed-effects regression of leverage on a tax-change dummy. The deadweight loss in default (ξ) is estimated at 0.6 for small firms and 0.32 for large firms, consistent with elevated financial frictions for small firms and in line with average recovery rates in Kermani and Ma (2023). Fixed operating costs (f) are approximately 0.15 for both samples, amounting to just under half of steady-state operating profits. The serial correlation of the tax process is estimated at 0.662, with innovation standard deviation of 0.022.

Q7. What is the model’s welfare counterfactual, and what does it imply?

The paper compares two economies both with profit taxation: one with the interest tax deduction and one without. Removing the deduction in the small-firm model causes leverage to fall from 0.36 to −0.26, as firms hold net cash rather than net debt. The capital stock shrinks, output falls, hours worked rise, and both the real wage and consumption decline. Consumer welfare drops by approximately 1.8%. Capital misallocation (measured following Hsieh and Klenow 2009) worsens from 0.89 to 0.88. The result has a second-best character: the interest deduction incentivizes debt-financed investment that partially offsets the distortion from restricted equity access.

Q8. What does the evidence on default probabilities add to the empirical case?

The Y-14 collection contains bank-assessed default probability estimates. In an event study covering Q1 2012–Q4 2018, the authors find that firms’ assessed default probabilities decline significantly by 20–30 basis points in the year of enactment or one year later for small borrowers (those with total loan commitments of $10–$100 million), representing approximately a 10% decline from the sample average default rate of around 2%. This decline peaks two years after enactment and persists for three years. No comparable decline is observed for larger loan size buckets. Separately, in SNC data, the probability of a non-pass (i.e., below-investment-grade supervisory) rating falls by 1.7–2.2 percentage points following tax cut enactments, persisting roughly three years. Together, these findings directly validate the model mechanism by which tax cuts lower default risk and credit spreads.

Q9. Are the results robust to alternative econometric methods that address heterogeneous treatment effects?

Yes. The paper applies the Borusyak et al. (2024) imputation estimator, which imputes fixed effects from untreated observations onto treated observations to remove negative weighting bias; for small firms and event years 0–3, it finds significant positive estimates comparable to the baseline. The de Chaisemartin and D’Haultfoeuille (2020, 2021) estimator, based solely on first-time switchers to treatment, yields an effect of 0.036 on leverage for small firms in the enactment year and no effect for large firms, consistent with the baseline. Results using the narrative approach (excluding Connecticut 2011 and 2015, New York 2014, and Rhode Island 2014 as potentially endogenous) produce slightly larger leverage estimates.

Q10. Are tax hike effects symmetric to tax cut effects?

Evidence on hikes is weaker because tax hikes are rare in the sample. In Y-14 data, hikes are associated with leverage declines for small firms in event year 4 and for large firms in event years 1, 2, and 4, but without sufficient pre-hike observations to identify pre-trends, these results are less credible than the cut results. In SNC data (which spans a longer period, 1992–2018), tax hikes are associated with large and significant reductions in total syndicated borrowing commitments of 6–7%, while cuts produce smaller and marginally significant increases. This asymmetry is consistent with the lower adjustment costs of reducing debt relative to increasing it.

Q11. What does the analysis of alternative model specifications reveal about the generality of the mechanism?

Three model extensions are considered. In a collateral-constrained model (no endogenous default), the cost of debt is lost financial flexibility (the future shadow cost of the borrowing constraint), which remains tax-sensitive. In a model with costly equity issuance (linear cost λ = 0.11 following Hennessy and Whited 2007), equity issuance is rare, so the model behaves nearly identically to the baseline. In a solvency-based default model (default when firm value turns negative rather than when liquidity is insufficient), the negative taxes-to-leverage result is preserved. A news-shock extension (Jaimovich-Rebelo 2009) incorporating the anticipation of future tax changes also produces lower leverage in response to higher anticipated taxes, consistent with the empirical anticipation effects, though with smaller magnitudes because the news shock variance is smaller than the total tax-change variance.

Q12. Why do contingent-claims models (Fischer-Leland-Goldstein class) always predict a positive taxes-to-leverage relationship?

In these models, shareholders have deep pockets, so negative cash flows can always be covered; this implies default is rare and the effect of taxes on the default put value is small relative to the direct interest tax deduction. Additionally, these models contain no capital stock, so there is no substitution mechanism between capital and a storage technology (i.e., cash/negative debt). Without endogenous investment, the only channel linking taxes to leverage is the tax shield, which necessarily implies a positive taxes-to-leverage relationship. This is why, as the paper notes, the result was “already hiding” in the Hennessy-Whited class of dynamic investment models but not visible in the contingent-claims literature.

Key Concepts

Interest Tax Deduction (Tax Shield) The paper uses this in the standard corporate finance sense: the after-tax cost of debt is reduced because interest payments are deductible against corporate income. In the model, debt proceeds are discounted at the after-tax interest rate, and the deduction is taken at the time of debt issuance. The paper’s contribution is to show this benefit can be outweighed by two tax-sensitive costs of debt, reversing the sign of the taxes-to-leverage relationship for small, constrained firms.

Tax-Sensitive Cost of Debt The paper defines two distinct tax-sensitive costs that offset the tax shield. First, taxes reduce after-tax profits, shifting the default threshold and raising equilibrium credit spreads; this is capitalized into the risky lending rate endogenously from the lender’s zero-profit condition. Second, taxes reduce the marginal product of capital, making debt-financed investment less attractive; because debt and capital are complements in a model without external equity, a higher tax rate lowers optimal capital and, with it, optimal debt.

Capital Adjustment Costs (ψ) Quadratic costs of changing the capital stock, parameterized as ψ(k’ − (1−δ)k)² / (2k). The paper identifies this parameter as the key determinant of whether leverage responds positively or negatively to taxes: for small firms, ψ is estimated to be near zero (insignificantly different from zero), enabling free substitution between capital and the storage technology (negative debt), so the complementarity channel dominates. For large firms, ψ is estimated to be nine times larger, suppressing this substitution.

Default Threshold In the model, default is triggered when the firm’s current after-tax profits plus recoverable capital are insufficient to repay debt: (1−τ)(y − wn − f) + (1−ξ)(1−δ)k < p. This threshold depends directly on the tax rate τ, so higher taxes move the threshold in the direction of default, raising credit spreads. The paper provides empirical support for this mechanism via the event study of bank-assessed default probabilities.

Enactment Date vs. Effective Date The paper distinguishes between the date tax legislation is signed into law (enactment date) and the date it becomes operative (effective date), which can differ by one to two years. The paper collects novel data on enactment dates from state legislative records. The empirical finding that firms respond to enactment rather than effective dates constitutes evidence of anticipation effects: firms adjust leverage upon observing future expected tax changes, not when the changes actually take hold.

Second-Best Welfare Effect of the Tax Deduction The paper uses this term to characterize the welfare result from the counterfactual: in an economy already distorted by profit taxation and restricted equity access, the interest deduction raises consumer welfare by incentivizing debt-financed capital accumulation. Removing the deduction causes firms to substitute into cash, shrinking the capital stock and lowering wages and consumption. This is a second-best result because the deduction is welfare-improving only because it partially offsets the distortions created by other frictions; in a frictionless world, no such second-best rationale would apply.

Y-14Q Supervisory Data The Federal Reserve’s supervisory collection from the 33 largest U.S. banks, covering loan portfolios and associated borrower financial statements for firms with commercial and industrial loans exceeding $1 million in commitment. The paper uses this dataset because it covers private, bank-dependent firms—a population not previously studied in the tax-leverage literature—and contains firm-level balance sheets, credit ratings, and default probability estimates.

Technology Transfer and Early Industrial Development: Evidence from the Sino-Soviet Alliance

Mon, 01 Jan 0001 00:00:00 +0000

This paper estimates the causal effect of technology and knowledge transfers on early industrial development using the Sino-Soviet Alliance of the 1950s as a natural experiment. Between 1950 and 1957, the Soviet Union supported the “156 Projects” — 139 approved civil projects for constructing technologically advanced, large-scale, capital-intensive industrial facilities in China. The intended program comprised two components: a “basic” transfer of Soviet state-of-the-art machinery and equipment (including blueprints, site surveys, and plant construction assistance), and an “advanced” know-how transfer involving Soviet experts residing in Chinese plants for roughly three years to train engineers and production supervisors in organizational, technological, and planning methods. Total investment amounted to approximately $80 billion in 2020 figures (45.7% of Chinese GDP in 1949).

Identification exploits idiosyncratic delays in project completion caused by Soviet production capacity constraints, insufficient experts, translator shortages, and miscommunication — factors documented in historical records as unrelated to project-specific characteristics. When the Sino-Soviet Split in 1960 abruptly ended the program, all 139 plants had been built but differed in what transfers they had received: 46 received both machinery and know-how (advanced), 46 received only machinery (basic), and 47 received neither (comparison). The paper verifies, via ANOVA tests, multinomial logit models, balancing regressions on 26 plant characteristics, pre-trend tests, and Oster (2019) selection-on-unobservables bounds, that the three groups were statistically equivalent prior to receiving the Soviet transfers.

The primary data source is plant-level annual reports from the Steel Association covering 94 steel firms (1,410 plants) from 1949 to 2000, matched to 304 steel plants across the 156 Projects. Supplementary sources include the declassified 1985 Second Industrial Survey (7,592 largest Chinese firms) and the China Industrial Enterprises database (1998–2013, over 1 million firms).

Three main results emerge. First, receiving only the basic (machinery) transfer had positive but short-lived effects: output of basic plants peaked at 14.7 percent above comparison plants six years after receiving Soviet machinery, then declined monotonically and became statistically insignificant after 20 years — consistent with the estimated 15–20 year life cycle of Soviet capital. Second, the advanced transfer had large and persistent effects: advanced plants’ output rose 8.4 percent relative to basic plants within two years, 19.7 percent within 20 years, and 49.5 percent cumulatively after 40 years. TFPQ of advanced plants reached 47.9 percent above basic plants after 40 years. These magnitudes held across industries in 1985 and 1998–2013 data, where value added of advanced firms was 41.4–52.0 percent higher and TFPR 39.5–49.3 percent higher than basic firms. Third, the program generated horizontal spillovers (12.9 percent higher output, 12.4 percent higher productivity for steel plants in counties hosting advanced plants) and vertical spillovers (16.4 percent productivity gain for supply-chain firms in counties of advanced nonsteel plants), with spillover effects conditional on post-1990s market liberalization to materialize in private firms.

The mechanism driving persistence is the accumulation of organizational and human capital during the advanced transfer, which enabled advanced plants — uniquely — to develop new production processes endogenously, home-fabricate continuous casting furnaces to replace obsolete Soviet open-hearth equipment, and produce export-quality steel. Advanced plants employed more engineers and high-skilled technicians, established professional schools, and their counties had 10.4 percent higher STEM university degree rates and 16.8 percent more technical schools.

Scope conditions: results apply to large-scale, capital-intensive state-planned industrial facilities in a country at an early stage of industrialization, under conditions of near-complete trade isolation (1960–1978) that prevented basic plants from compensating via imported foreign capital. The estimated aggregate contribution of the program is that, without both transfer types, Chinese real GDP per capita growth between 1953 and 1978 would have been 7 to 19 percent lower.

Q: What distinguishes the “basic” from the “advanced” Soviet transfer? A: The basic transfer involved duplication of whole Soviet plants through provision of state-of-the-art Soviet machinery, equipment, blueprints, geological surveys, and construction assistance. The advanced transfer added visits of Soviet experts — expected to stay approximately three years — to teach Chinese technicians how to operate the machinery and to provide within-firm training in engineering (math, physics, chemistry, organizational and planning methods) and supervisory management based on “scientific management” principles including quality-control methods.

Q: What caused plants to receive different levels of transfer, and why is this variation credible for identification? A: Delays arose from Soviet production capacity constraints (by 1955, one-third of annual Soviet steel-rolling output was destined for China), insufficient experts, translator shortages, and bilateral miscommunication — all documented in historical records as unrelated to project characteristics. When the 1960 Split ended the program, plants’ treatment status was determined by where they happened to be in the delivery queue. ANOVA tests find no significant differences in approval year, investment, workforce, equipment value, project length, or capacity across the three groups, and a multinomial logit on province and industry fixed effects shows no group had higher ex-ante probability of receiving either transfer type.

Q: What were the output effects of the basic transfer, and why did they fade? A: Output of basic plants was not significantly above comparison plants for the first two years, peaked at 14.7 percent higher six years after receiving Soviet machinery, then declined monotonically and became statistically insignificant after 20 years. This timing corresponds to the estimated 15-year life cycle of Soviet capital goods. TFPQ of basic plants followed the same pattern, peaking at 14.5 percent above comparison plants. Without the know-how component, basic plants could not develop new processes or home-fabricate replacement capital, so productivity advantages disappeared as Soviet equipment became obsolete.

Q: What were the output and productivity effects of the advanced transfer? A: Advanced plants’ output rose 8.4 percent relative to basic plants within two years of the Soviet transfer and 19.7 percent within 20 years, reaching a cumulative effect of 49.5 percent after 40 years. TFPQ of advanced plants increased from 8.3 percent above basic plants two years after the transfer to 47.9 percent after 40 years. These effects were driven by output growth rather than differential input use — the number of workers, coke, and iron were statistically indistinguishable across the three plant types — ruling out government input reallocation as an explanation.

Q: Did the advanced transfer affect steel quality? A: Advanced plants produced substantially more crude steel (higher quality, lower carbon content) and less pig iron than basic and comparison plants, and this quality advantage persisted well beyond the 20-year life cycle of Soviet capital. Basic plants also shifted toward crude steel initially but the quality advantage dissipated once Soviet machinery became obsolete, whereas advanced plants maintained the shift through adoption of the basic oxygen process and later continuous casting furnaces.

Q: What is the main mechanism through which the advanced transfer generated persistent effects? A: The advanced transfer equipped engineers and supervisors with organizational, technological, and planning knowledge, enabling advanced plants to develop and adopt the basic oxygen steelmaking process independently during China’s 1960–1978 period of trade isolation. Advanced plants had a 15.2 percent higher probability of using the basic oxygen process five years after the transfer and a 65.1 percent higher probability twenty years after, relative to basic plants. They also home-fabricated continuous casting furnaces, making them 26.7 to 78.4 percent more likely to use such furnaces 10 to 20 years after the transfer; basic plants showed no differential advantage over comparison plants on this measure.

Q: What role did trade openness play in the divergence between basic and advanced plants? A: Once China opened to international trade from 1978, advanced plants relied dramatically less on imported foreign capital than basic plants — likely because they had developed domestic production capabilities. At the same time, advanced plants exported 45.5 percent more steel and produced 51.1 percent more steel above international quality standards than basic plants. Basic plants showed no differential imports of foreign capital or differential exports relative to comparison plants, suggesting that once both types could access foreign machinery, basic plants lost any remaining productivity edge.

Q: What were the human capital effects of the advanced transfer? A: Over time, advanced plants opened training schools for high-skilled technicians and offered within-firm training programs for engineers. As a result, advanced plants employed more engineers and high-skilled technicians and fewer low-skilled workers than basic plants, while the human capital composition did not differentially change between basic and comparison plants. At the county level, universities hosting advanced plants were 10.4 percent more likely to offer STEM degrees, had 16.8 percent more technical schools, 14.3 percent more STEM college graduates, and 17.6 percent more high-skilled workers than counties hosting basic plants.

Q: Did the government differentially favor basic or advanced plants after the Split? A: The paper finds no evidence of special government favor. Government transfers and loans were not differentially allocated to basic or advanced plants in either the short or long run. Distance from railroads and roads did not change differentially across plant types. Measures of political connection and politician quality at the prefecture level showed no significant differences across the three groups in the 40 years after the Soviet transfer. County-level total investment and investments in related and unrelated industries were also statistically indistinguishable.

Q: What were the intra-firm spillover effects? A: Steel plants in the same firm as advanced plants increased their steel production by 24.9 percent and were 22.1 percent more productive relative to plants in the same firm as basic plants, after the Soviet transfer. Plants in the same firm as basic plants showed no differential performance relative to plants in the same firm as comparison plants. The within-firm spillovers appear driven by the transmission of new technologies and production methods through formal within-firm training programs, as supported by historical records.

Q: What were the horizontal spillover effects across firms? A: Steel plants in the same counties as advanced plants produced 12.9 percent higher output and were 12.4 percent more productive than those in counties hosting basic plants, after the transfer. They were more likely to adopt basic oxygen converters and continuous casting furnaces, and from 1978 they exported significantly more and produced more steel above international quality standards, mirroring the patterns of the advanced plants themselves.

Q: What were the vertical spillover effects? A: Steel plants in counties hosting nonsteel basic plants produced 14.2 percent more steel than those in counties hosting nonsteel comparison plants, suggesting some output spillover from basic machinery. However, only plants in counties of advanced nonsteel plants experienced a productivity increase — estimated at 16.4 percent — relative to plants in counties of basic nonsteel plants. These supply-chain firms were also the only ones to show increased adoption of basic oxygen and continuous casting furnace technology and differential engagement in trade.

Q: How did market liberalization reforms interact with the spillover effects? A: Starting in the late 1990s, privatized firms economically related to advanced plants outperformed their counterparts in terms of value added, TFPR, and exports, while state-owned firms in the same counties no longer showed a competitive advantage. New private firms locating in counties that had hosted advanced plants received an additional performance gain. At the county level, counties hosting advanced plants had on average 16.6 percent more private firms and 25.2 percent more privately-produced industrial output than counties hosting basic plants. The mechanism appears to be the stock of industry-specific human capital concentrated in those counties, which private firms could draw on once allowed to compete for workers.

Q: What is the estimated aggregate contribution of the Soviet transfer to Chinese growth? A: Province-level regressions show that each additional basic project increased province-level output by 1.1 percent per year on average, and each additional advanced project by 6.2 percent per year. A back-of-the-envelope calculation implies that without both transfer types, Chinese real GDP per capita growth between 1953 and 1978 would have been 7 to 19 percent lower.

Q: How does the paper rule out selection on unobservable characteristics? A: Using the Oster (2019) methodology, the paper finds that for the treatment effects to become statistically insignificant, selection on unobserved variables would need to be 8 to 19 times larger than selection on observed variables — a range the authors characterize as implausible given the strong balancing on observables and the historical documentation of delay causes.

Q: How does this paper differ from Heblich et al. (2020), which also studies Sino-Soviet technology transfer? A: Heblich et al. (2020) study long-run negative spillovers of the 156 Projects on counties that hosted them relative to counties that were geographically suitable but ultimately not selected, focusing on an outside-the-program comparison. This paper instead exploits within-program variation — differences across the three plant types — using plant-level data to assess short-, medium-, and long-run direct effects and spillover effects of different transfer intensities.

Basic Transfer: The provision of Soviet state-of-the-art machinery, equipment, blueprints, geological surveys, and plant construction assistance — duplicating a whole Soviet plant — without accompanying human capital or organizational training.

Advanced Transfer: The full Soviet technology and know-how package: basic machinery provision plus multi-year visits of Soviet experts who taught Chinese engineers and production supervisors organizational, technological, and planning methods based on “scientific management” principles.

Comparison Plants: Plants approved under the 156 Projects that received neither Soviet machinery nor technical assistance due to delays compounded by the Split, and which continued operating with traditional domestic technology.

156 Projects: An array of 139 approved, technologically advanced, large-scale, capital-intensive industrial facilities whose construction the Soviet Union agreed to support between 1950 and 1957 as part of the Sino-Soviet Alliance, representing 45.7% of Chinese GDP in 1949.

Tacit Knowledge: Industry- and firm-specific knowledge embodied in workers and organizations — including operational methods, quality-control procedures, and process innovation capabilities — that cannot be transferred through capital goods alone and requires extensive on-the-job training from foreign experts.

Basic Oxygen Process: A steelmaking process innovation that became predominant in the 1960s by blowing oxygen through molten pig iron to reduce carbon content; adopted by advanced plants through endogenous process development, while basic plants showed no differential adoption relative to comparison plants.

Source Text Origin: The paper’s classification scheme for the grounding of evidence — in this case, full working paper text obtained from NBER WP 29455, enabling comprehensive summary of quantitative results, mechanisms, and robustness tests.

Testing Mechanisms

Mon, 01 Jan 0001 00:00:00 +0000

Kwon and Roth develop econometric tests for the “sharp null of full mediation”: the hypothesis that a treatment D affects an outcome Y only through a specified mechanism (or set of mechanisms) M, with no direct pathway. Rather than attempting the more demanding task of identifying average direct and indirect effects — which typically requires strong assumptions about how M is assigned — the paper asks whether full mediation is consistent with the data at all, and if not, how large the alternative mechanisms are.

The key theoretical observation is that under the sharp null of full mediation, together with independence of D and monotonicity of M in D, the treatment D satisfies the conditions for a valid instrumental variable for the local average treatment effect (LATE) of M on Y. This equivalence means that existing tools for testing IV validity with binary endogenous treatment can be applied off-the-shelf when both D and M are binary. The paper then extends this framework to the general case where M is a p-dimensional vector with finite support, and where the researcher can impose arbitrary restrictions on the distribution of compliance types θ_{lk} = P(M(0)=m_l, M(1)=m_k) — including monotonicity, relaxations allowing a bounded share of defiers, elementwise monotonicity for multidimensional M, or no restrictions.

The testable implications of the sharp null require that there exists type shares θ̃ in the identified set Θ_I such that sup_A Δ_k(A) ≤ Σ_{l≠k} θ̃_{lk} for all k, where Δ_k(A) is the treatment-control difference in the probability of the compound outcome {Y∈A, M=m_k}. The intuition is that any positive treatment effect on this compound outcome can only be driven by compliers, not by always-takers who under the sharp null have both fixed M and fixed Y. Because Θ_I is characterized by linear constraints when R is, verifying the testable implications reduces to a linear program. The paper proves these implications are sharp: if satisfied, there exists a joint distribution of potential outcomes consistent with the data and the sharp null. The paper also derives sharp lower bounds on ν_k = P(Y(1,m_k) ≠ Y(0,m_k) | M(1)=M(0)=m_k), the fraction of k-always-takers whose outcome is affected despite having the same mediator value under both arms.

For inference, the testable implications are reformulated as moment inequalities and the Cox-Shi (2022) test is recommended based on Monte Carlo simulations calibrated to the empirical applications, which find close-to-nominal size across nearly all designs (null rejection probability no larger than 9% for a 5% test), with the exception of settings with only 40 clusters where CS is over-sized at 0.15 but recovers with 80 clusters.

The methodology is illustrated in two RCT applications. In Bursztyn, González, and Yanagizawa-Drott (2020), where an information treatment about other men’s beliefs is randomized in Saudi Arabia and the outcome is wives’ job applications, the sharp null that effects operate only through job-search service sign-up is rejected (p=0.02, CS test); the lower bound on the fraction of never-takers affected despite no change in sign-up is at least 11%, compared to an overall ATE of 0.12, with the lower bound remaining positive for defier shares up to 7%. In Baranov et al. (2020), where cognitive behavioral therapy for new mothers is randomized and the outcome is financial empowerment at seven-year follow-up, the sharp null is rejected for grandmother presence alone (p=0.02, lower bound ≥19% of never-takers affected) and for relationship quality alone (p=0.03, lower bound ≥10% of always-takers affected); however, when both mechanisms are considered jointly, the sharp null cannot be rejected at conventional levels (p=0.65), indicating the data are statistically consistent with the combination of these two mechanisms fully explaining the treatment effect.

Scope conditions: the main results assume D is randomly assigned (extended in Section 5 to IV, conditional unconfoundedness, and distributional difference-in-differences settings) and M has finite support. An R package, TestMechs, accompanies the paper.

In depth

Q1. What is the sharp null of full mediation and how does it differ from standard mediation analysis objectives?

The sharp null posits that Y(d,m) depends only on m and not on d — that is, Y(0,m) = Y(1,m) almost surely for all m — meaning the treatment affects the outcome exclusively through its effect on M. Standard mediation analysis seeks to decompose the average treatment effect into average direct and indirect components, which requires identifying the causal effect of M on Y and thus typically imposes sequential unconfoundedness or an instrument for M. The sharp null test asks only whether any direct effect exists for any individual, which is answerable without identifying the causal effect of M on Y and therefore under substantially weaker assumptions.

Q2. What is the core identification insight connecting mediation testing to IV validity testing?

Under the sharp null of full mediation, combined with independence of D and monotonicity of M(d) in d, the treatment D satisfies exactly the LATE assumptions as an instrument for the effect of M on Y. Consequently, testable implications of the LATE assumptions — developed in Kitagawa (2015), Huber and Mellace (2015), and Mourifié and Wan (2017) — translate directly into testable implications of the sharp null when both D and M are binary. This equivalence allows researchers to apply off-the-shelf IV validity tests for mechanism testing with no additional methodological development in the binary-binary case.

Q3. What are the sharp testable implications of the sharp null in the general multi-valued, multi-dimensional M case?

The sharp testable implications require that there exists a vector of type shares θ̃ in the identified set Θ_I (consistent with observed marginal distributions of M|D and the researcher’s restrictions R) such that sup_A Δ_k(A) ≤ Σ_{l≠k} θ̃_{lk} for all k, where Δ_k(A) = P(Y∈A, M=m_k|D=1) − P(Y∈A, M=m_k|D=0). The intuition is that any positive treatment effect on the compound outcome 1{Y∈A, M=m_k} can only be driven by compliers transitioning into state k; always-takers have fixed M=m_k and under the sharp null also have fixed Y, so they contribute zero. The testable implications are proved to be sharp: if they hold, there exists a joint distribution of potential outcomes consistent with the data and the sharp null.

Q4. How does the paper quantify the magnitude of violation when the sharp null is rejected?

The paper derives sharp lower bounds on ν_k = P(Y(1,m_k) ≠ Y(0,m_k) | M(1)=M(0)=m_k), the fraction of k-always-takers whose outcome is affected by the treatment despite having the same mediator value under both arms. The lower bound is θ_{kk}·ν_k ≥ (sup_A Δ_k(A) − Σ_{l≠k} θ_{lk})₊, which is sharp in the sense that there exists a distribution of potential outcomes achieving equality. Appendix B.1 additionally derives bounds on ADE_k = E[Y(1,m_k)−Y(0,m_k)|M(1)=M(0)=m_k], the average direct effect for k-always-takers.

Q5. How is inference conducted and which test is recommended?

Because the test statistic involves the solution to a linear program whose constraints depend on the data, and sup_A Δ_k(A) can be non-differentiable in the data-generating process — making standard bootstrap methods invalid — the paper reformulates the testable implications as moment inequalities of the form H₀: ∃ω s.t. C₁ω − C₂p ≥ 0, where C₁ and C₂ are known matrices and p collects observable conditional probabilities. Methods from the moment inequality literature (Andrews, Roth, and Pakes, 2023; Cox and Shi, 2022; Fang, Santos, Shaikh, and Torgovitsky, 2023) are then directly applicable. Cox and Shi (2022) is recommended as a default based on Monte Carlo evidence.

Q6. What do the Monte Carlo simulations reveal about size and power?

Across nearly all simulation designs calibrated to the two empirical applications, the ARP, CS, and K tests achieve close-to-nominal size, with null rejection probabilities no larger than 9% for a nominal 5% test. The notable exception is settings with only 40 independent clusters, where CS is over-sized with a null rejection probability of 0.15; doubling to 80 clusters restores approximate size control. For power, CS performs similarly to or better than ARP across all designs, with the advantage being substantial in some cases, particularly with multi-valued M. The FSST test can be substantially over-sized in settings with small or moderate numbers of clusters.

Q7. What does the Bursztyn et al. (2020) application find?

The treatment is random assignment of information about other men’s beliefs about women working outside the home in Saudi Arabia; the mediator is job-search service sign-up (binary); the outcome is whether the wife applies for jobs three to five months later. The sharp null is rejected with p=0.02 (CS test), establishing that the information treatment affects long-run labor market outcomes through pathways other than mechanical service sign-up. The lower bound on the fraction of never-takers affected despite no change in sign-up is at least 11%; the estimated average direct effect for these never-takers ranges from 0.11 to 0.18, compared to an overall ATE of 0.12. The lower bound remains positive for defier shares up to 7% of the population (0.33 defiers per complier), providing robustness to violations of monotonicity.

Q8. What does the Baranov et al. (2020) application find?

The treatment is cognitive behavioral therapy for pregnant women and new mothers (randomized RCT); the outcome is an index of financial empowerment at seven-year follow-up. For the binary mechanism of grandmother presence in the household, the sharp null is rejected (CS p=0.02) with a lower bound of at least 19% of never-takers affected. For relationship quality with husband (1-5 scale, under monotonicity that CBT improves the relationship), the sharp null is rejected (CS p=0.03) with a pooled lower bound of at least 10% of always-takers affected. When both mechanisms are considered jointly as a vector M, the sharp null cannot be rejected (CS p=0.65) and the lower bound on the fraction of always-takers affected is 7%, indicating the data are statistically consistent with the combination of these two mechanisms fully explaining the CBT effect on financial empowerment.

Q9. How does the framework accommodate relaxations of monotonicity?

The paper allows the researcher to specify arbitrary closed non-empty subsets R of the simplex as restrictions on type shares θ. Monotonicity in the binary case corresponds to R = {θ∈Δ: θ_{10}=0}, ruling out defiers. A relaxation allows up to d̄ fraction of the population to be defiers (θ_{10} ≤ d̄). In the Bursztyn et al. (2020) application, the estimated lower bound on ν_k remains positive for d̄ up to 0.07. One can also completely remove monotonicity by setting R = Δ, though this yields less informative bounds. For multidimensional M, elementwise monotonicity imposes that each dimension of M(d) is increasing in d.

Q10. How does the paper extend to non-experimental settings?

Section 5 shows that results extend whenever the distributions of (Y^tot(d), M(d)) are identified through strategies other than direct randomization of D. Under a standard IV setup with binary instrument Z for D, the LATE of D on Y and D on M are identified for instrument-compliers, and the same testable implications apply within this subpopulation. Under conditional unconfoundedness D ⊥ (Y(·,·), M(·)) | X with overlap, distributions are identified via propensity-score reweighting. Under distributional difference-in-differences (Athey and Imbens, 2006; Callaway and Li, 2019; Roth and Sant’Anna, 2023), counterfactual distributions of Y and M for treated units are identified, enabling the same testing approach.

Q11. What is the paper’s relationship to the principal stratification literature?

The k-always-takers — those with M(1)=M(0)=m_k — correspond directly to principal strata (Frangakis and Rubin, 2002). The bounds on ADE_k derived in Appendix B.1 match those of Lee (2009), Flores and Flores-Lagunes (2010), and Zhang and Rubin (2003) in the special case of binary M under monotonicity, and extend them to non-binary M and relaxations of monotonicity. The primary focus of the present paper is the sharp (Fisherian) null that ν_k = 0 for all k — that is, no always-taker is affected — which is strictly stronger than the weak null of zero average direct effect studied in the principal stratification literature.

Q12. What are the limitations and directions for future work identified by the authors?

The analysis is restricted to discrete M; while M can be discretized under assumptions described in Remark 3, testing the sharp null directly for continuous M remains an open question for future work. The framework does not impose restrictions on the magnitude of M’s effect on Y or on the degree of endogeneity of M, and incorporating such restrictions could yield sharper testable implications. Extension to non-binary treatments D is also identified as a direction for future research.

Sharp null of full mediation: The hypothesis that Y(0,m) = Y(1,m) almost surely for all m in the support of M — i.e., the treatment D affects the outcome Y exclusively through its effect on M, with no direct effect on any individual’s outcome. This is a Fisherian sharp null, strictly stronger than a zero average direct effect.

k-always-takers: Individuals for whom M(1)=M(0)=m_k — those whose mediator value equals m_k regardless of treatment assignment. Under the sharp null, these individuals’ outcomes must be unaffected by the treatment. They constitute the principal stratum with fixed mediator value m_k and generalize the always-taker and never-taker concepts from the binary LATE framework.

ν_k (fraction of always-takers affected): ν_k = P(Y(1,m_k) ≠ Y(0,m_k) | M(1)=M(0)=m_k), the fraction of k-always-takers whose outcome is affected by the treatment despite having the same mediator value under both arms. Under the sharp null ν_k = 0 for all k; a large ν_k indicates strong alternative mechanisms operating outside of M for always-takers with mediator value m_k.

Type shares θ_{lk}: The fractions of the population of each compliance type, θ_{lk} = P(M(0)=m_l, M(1)=m_k). These generalize the LATE compliance categories (always-takers, never-takers, compliers, defiers) to the multi-valued mediator setting. The vector θ may be only partially identified when M is non-binary, with the identified set Θ_I characterized by linear constraints matching observed marginal distributions of M|D.

Δ_k(A): The treatment-control difference in the probability of the compound outcome {Y∈A, M=m_k}: Δ_k(A) = P(Y∈A, M=m_k|D=1) − P(Y∈A, M=m_k|D=0). The supremum of Δ_k(A) over all sets A is the key estimable quantity that appears in both the testable implications and the lower bounds on ν_k.

Identified set Θ_I: The set of type-share vectors θ̃ consistent with the observed marginal distributions of M|D=0 and M|D=1, and with the researcher’s restrictions on compliance types R. When R is characterized by linear constraints (as in all main examples), Θ_I is a polytope and optimization over it — required for implementing the testable implications — is a linear program.

TestMechs R package: The accompanying software implementation of the inference methods and lower bound estimators developed in the paper, designed to facilitate empirical application of the tests.

The Architecture of Social Networks and the Diffusion of Innovations

Mon, 01 Jan 0001 00:00:00 +0000

This paper examines how the architecture of social networks shapes the success or failure of technology diffusion when adoption decisions exhibit strategic complementarities. The research question is: which structural feature of a network determines whether a new technology spreads or fails, and in which direction does that feature work?

The paper builds on the canonical threshold diffusion model of Morris (2000) and Granovetter (1978), in which an agent adopts a new technology if the share of his neighbors who have adopted exceeds a threshold Q in [0,1]. The key innovation is the addition of a second structural object — a set of decision-making units C — that captures the empirically common phenomenon that subsets of agents (friends, family, neighbors, colleagues) can coordinate and make joint adoption decisions. The model is purely theoretical; the paper derives characterizations and comparison theorems rather than estimating parameters from data.

The central structural concept introduced is insularity: the extent to which agents concentrate their connections to a narrow set of other agents, rather than distributing connections broadly. A formal partial order over networks is defined: network {w̃} is less insular than network {w} if there is no local increase in insularity in {w̃} relative to {w}, where a local increase in insularity occurs when one agent’s proportionate connections to a narrow set S are strictly higher and another agent’s proportionate connections to a superset R are strictly lower (with the first agent’s share of S weakly exceeding the second agent’s share of R). Moving from a network toward a convex combination with the complete network strictly reduces insularity under this definition (Lemma 3).

The paper’s main characterization result (Proposition 1) establishes that the set of non-adopters of technology Q is precisely SQ — the maximal (1−Q)-subgroup-cohesive set — defined as the largest set in which every decision-making unit C contained in SQ has at least one agent with at least fraction (1−Q) of his connections inside SQ. This extends Morris’s (2000) cohesion characterization to the joint-decision setting.

The main theorem (Theorem 1) establishes that for any two societies sharing the same decision-making structure C but differing in network insularity, there exists a cutoff threshold mu in [0,1] such that: (i) for technologies with Q < mu, adoption is weakly higher in the less insular network; and (ii) for technologies with Q >= mu, adoption is weakly lower in the less insular network. The direction reversal at mu reflects two competing mechanisms. Insular connections hinder singleton diffusion: an agent over-connected to a narrow set will not adopt individually until others in that set adopt, blocking entry of the technology from outside. But insular connections facilitate joint adoption: the same over-connectedness makes it profitable for the group to adopt together if they can coordinate, because each member already has a high share of neighbors within the group. High-threshold technologies depend crucially on joint adoption cascades and so benefit from insularity; low-threshold technologies spread person-to-person and are impeded by insularity when agents cannot coordinate.

Proposition 2 establishes a complementary monotonicity result: expanding the set of decision-making units (C subset of C’) weakly increases adoption for any technology and any network, because joint decision-making resolves local coordination failures.

The main result is extended to heterogeneous thresholds (Section 7). Proposition 3 shows that Theorem 1 continues to hold when agent-specific idiosyncratic components theta_i are bounded within an interval [−gamma/2, gamma/2] for some gamma > 0. Proposition 4 characterizes the necessary conditions for the main result to break: the specification fails only if there exist two agents i and j with theta_i > theta_j + Q2 − Q1, meaning the idiosyncratic gap between them exceeds the difference between the two technology thresholds being compared.

Q: What is the paper’s central research question? A: The paper asks how the architecture of a social network — specifically the structure of agents’ connections — determines whether a new technology spreads widely or fails to diffuse. It focuses on technologies with strategic complementarities, where an agent’s benefit from adopting depends on neighbors adopting and those neighbors’ benefit depends on their neighbors, creating potential for both snowballing and coordination failure.

Q: What is the key modeling innovation relative to the standard threshold model? A: The paper adds a set of decision-making units C, a collection of subsets of agents each of which can make a joint adoption decision. In the standard Morris (2000) model, only individual agents decide; here, groups such as friends, family, or neighbors can collectively agree to adopt, resolving their local coordination problem. The set C is subject only to closure under subsets and inclusion of all singletons, making the framework highly flexible.

Q: How does the diffusion process work formally? A: At each period t >= 1, agent i adopts if either: (1) more than fraction Q of his neighbors adopted in period t−1 (singleton adoption), or (2) i belongs to a decision-making unit C not yet adopted, and for every j in C the fraction of j’s neighbors in A_{t−1} union C exceeds Q (joint adoption). Actions are irreversible, and Appendix C proves this irreversibility assumption is without loss of generality for the final adoption set under myopic best-response dynamics.

Q: What is the characterization of non-adopters (Proposition 1)? A: The set of agents who do not adopt technology Q equals SQ, the unique maximal (1−Q)-subgroup-cohesive set — the largest set S such that every decision-making unit C contained in S has at least one member i with Pi(S minus C) >= (1−Q), meaning at least fraction (1−Q) of i’s connections remain inside S outside of C. This extends Morris (2000)’s p-cohesion concept: when C contains only singletons, (1−Q)-subgroup cohesion collapses to (1−Q)-cohesion in Morris’s sense.

Q: What does the simple eight-agent example illustrate? A: With two four-clique subgraphs (agents 1-4 and 5-8), Network A has agents 1, 3, 5, 7 each holding 3/4 of their connections within their four-agent group; Network B reduces those within-group shares to 5/8 by weakening two within-group links from weight 1 to weight 1/2 and adding cross-group links of weight 1/2. For Q = 3/10: in Network B all eight agents adopt (group {1,2,3,4} adopts jointly at t=1, then agents 5 and 7 adopt as singletons at t=2, agents 6 and 8 at t=3), while in Network A only {1,2,3,4} adopt (agents 5-8 each have only 1/4 of neighbors adopted, below Q = 3/10). For Q = 7/10: in Network A group {1,2,3,4} adopts jointly (each has 3/4 > 7/10 of neighbors adopting), while in Network B there is zero adoption (agent 3 has only 5/8 < 7/10 of neighbors in the joint group). This is the concrete illustration of the threshold-dependent reversal in Theorem 1.

Q: What is insularity and how is it formally defined? A: Insularity is the extent to which agents concentrate their connections to a narrow set of others. A local increase in insularity in {w} relative to {w̃} occurs when, for some agents i and j and sets S subset of R: (1) Pi(S) is strictly higher in {w} and Pj(R) is strictly lower in {w}, and (2) Pi(S) >= Pj(R) in {w}. Network {w̃} is less insular than {w} if no local increase in insularity exists in {w̃} relative to {w}. Lemma 3 establishes that the lambda-convex combination of any non-complete network with the complete network is strictly less insular.

Q: What is the main theorem (Theorem 1) and its precise statement? A: For two societies sharing the same decision-making structure C but differing in network insularity — with {w̃} strictly less insular than {w} — there exists a cutoff mu in [0,1] such that: for Q < mu, adoption is weakly higher in the less insular network; and for Q >= mu, adoption is weakly lower in the less insular network. The cutoff mu depends on the specific networks and decision-making structure. The result is a clean reversal: less insular is better for low-threshold technologies and worse for high-threshold technologies.

Q: What are the two competing mechanisms driving Theorem 1? A: First, insular connections hinder individual diffusion: an agent with a high share of connections concentrated inside a set will not adopt as a singleton until others in that set adopt, blocking entry of the technology from outside via individual contagion. Second, insular connections facilitate joint adoption: precisely because an agent has a high share of connections to a narrow group, jointly adopting with that group is profitable — each member has enough neighbors already within the group to exceed the threshold when the group adopts together. For high-threshold technologies, joint adoption is the only viable mechanism, so the second effect dominates; for low-threshold technologies, singleton diffusion suffices and the first effect dominates.

Q: How does joint decision-making affect adoption (Proposition 2)? A: Expanding the set of decision-making units from C to any C’ containing C weakly increases adoption of technology Q for any network and any Q. The proof shows that the non-adopter set SQ under C’ is also (1−Q)-subgroup cohesive under C, making it a subset of non-adopters under C. The economic logic is that any group able to make a joint decision can solve its local coordination problem: agents who individually would not adopt because too few neighbors have adopted may collectively adopt if each would benefit from group adoption.

Q: How robust is Theorem 1 to heterogeneous thresholds? A: Proposition 3 shows that Theorem 1 extends with the same cutoff structure when each agent i has an idiosyncratic threshold component theta_i in [−gamma/2, gamma/2] for sufficiently small gamma > 0. Proposition 4 establishes the necessary condition for the result to break with unbounded heterogeneity: there must exist agents i and j with theta_i > theta_j + Q2 − Q1, meaning the idiosyncratic gap must strictly exceed the technology threshold gap being compared. The underlying intuition of Theorem 1 persists even when the precise specification fails.

Q: What are the policy and managerial implications? A: A firm with a low-threshold technology should target less insular societies to maximize uptake, while a firm with a high-threshold technology should target more insular societies; the paper cites Facebook’s initial launch within closed university networks as consistent with the high-threshold logic. Policymakers and firms can increase adoption by encouraging joint decision-making — sanitation campaigns that organize neighborhood workshops, family mobile-plan discounts, or online coordination platforms all work through this channel. Conversely, governments trying to suppress collective action such as protest can prohibit in-person gatherings or online communication to prevent joint decision-making. The paper notes results abstract from seeding, leaving optimal seeding under joint decision-making as a future research direction.

Insularity: The extent to which agents concentrate their connections to a narrow set of other agents rather than distributing connections broadly; formally defined via a partial order based on local increases in agents’ proportionate connections to nested sets S subset of R.

Decision-making unit: A set C of agents who can make a joint decision to adopt together; the collection C of all decision-making units is closed under subsets and contains all singletons, capturing informal group coordination among friends, family, or neighbors.

p-Subgroup cohesion: A set S is p-subgroup cohesive if every decision-making unit C contained in S (of any size, including singletons) is p-connected in S — meaning at least one agent in C has at least fraction p of his connections to S minus C; the paper’s generalization of Morris (2000)’s p-cohesion to settings with joint decision-making.

Threshold of adoption (Q): A parameter Q in [0,1] summarizing a technology’s strategic complementarities, such that an agent is better off adopting if and only if more than fraction Q of his neighbors adopt; low Q means the technology is valuable even with few adopters, high Q means it requires near-universal neighborhood adoption.

Local increase in insularity: A pairwise comparison between two networks: {w} exhibits a local increase in insularity relative to {w̃} when one agent’s proportionate connections to narrow set S are strictly higher and another agent’s proportionate connections to superset R are strictly lower in {w}, with the first agent’s share of S weakly exceeding the second agent’s share of R in {w}.

SQ (maximal non-adopter set): The unique maximal (1−Q)-subgroup-cohesive set in a society, constituting exactly the agents who do not adopt technology Q in the final outcome; it is the union of all (1−Q)-subgroup-cohesive sets and is itself (1−Q)-subgroup-cohesive (Lemma 2, Proposition 1).

The Confederate Diaspora

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates how white migration out of the postbellum South diffused Confederate culture and entrenched racial norms across the United States during a critical juncture of westward expansion and post-Civil War reconciliation. The central question is whether the “Confederate diaspora” — Southern white migrants who left the former Confederacy from 1870 to 1900 — causally shaped the geography of Confederate memorialization, white supremacist organizations, racial violence, and long-run racial inequity outside the South.

Using complete-count U.S. Census records from 1870–1900 and linked Census records from the Census Linking Project, the authors track nearly one million white migrants from former Confederate states, including more than 61,000 former enslavers and 127,000 of their household kin, who settled outside the South by 1900. By 1900, migrants from the former Confederacy comprised on average 2.2% of the population in destination counties. Four outcomes measuring Confederate culture at the county level are constructed: Confederate memorialization (monuments, place names, schools), United Daughters of the Confederacy (UDC) chapters, Ku Klux Klan (KKK) chapters, and lynchings of Black people.

The primary identification strategy is a shift-share instrumental variable (SSIV) that combines the cross-sectional distribution of Southern white migrants across non-Southern counties in 1870 (shares) with predicted migration flows out of each Southern state between 1870 and 1900 (shifts). The predicted shifts are constructed from origin-county economic and ideological push factors estimated via LASSO, insulating the IV from endogenous location sorting. Conditional on the 1870 Southern white population share, the SSIV identifies the distinct causal influence of the postbellum Confederate diaspora.

Main findings are large relative to the diaspora’s modest population share. Moving from zero to the mean Confederate diaspora share implies an 8 percentage point (p.p.) increase in the likelihood of KKK activity relative to a mean prevalence of 35% in non-Southern counties. Effects on post-1900 lynching events are even larger proportionally: a 4 p.p. increase in likelihood relative to a mean of only 5%. IV estimates for Confederate memorialization show that a 1 p.p. increase in the Southern white share in 1900 raised the likelihood of memorialization by 3.4 p.p. (after controlling for the 1870 share), relative to a baseline prevalence of 25% outside the South. Effects on UDC chapters are similarly large given the organization’s limited non-Southern footprint (present in only 10% of counties). IV estimates consistently exceed OLS estimates, consistent with economic sorting biasing OLS downward.

Beyond Confederate symbolism, the diaspora also contributed to a novel form of racial exclusion: the “sundown town.” A 1 p.p. increase in the Confederate diaspora share in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation (defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900).

Former slaveholders, though only about 6% of Confederate migrants, played an outsized role. They disproportionately sorted into frontier counties and into positions of public authority — more than twice as likely to work as lawyers or judges and nearly three times as likely to work in public administration as the average non-slaveholding Southern white migrant. Their cultural influence was especially pronounced in frontier communities where institutions were weak and norms malleable. In Denver, first-generation Southern white migrants were 11% more likely to join the KKK than men with no Southern heritage, with a similar differential observed for second-generation migrants.

The diaspora’s effects persist into the 21st century: counties with larger Confederate diasporas in 1900 exhibit larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, higher rates of police-induced Black mortality, and more conservative racial attitudes among whites, as measured in modern survey data. These long-run findings are identified using the same county-level SSIV strategy. Scope conditions: effects are larger in frontier counties (weaker institutions, more malleable norms), in counties with fewer Union Army enlistees, and in newly incorporated areas with fewer than 2 residents per square mile in 1860.

Q: What is the central research question and why does it matter? A: The paper asks whether postbellum Southern white migration causally diffused Confederate culture — memorialization, organized white supremacy, and racial violence — beyond the South, and whether this early cultural transplantation has persistent effects on racial inequity today. It matters because Confederate monuments and persistent Black disadvantage in labor, housing, and policing are often attributed to the legacies of slavery within the South; this paper shows the mechanism by which those norms spread nationally through internal migration at a critical juncture of westward expansion and post-war reconciliation.

Q: How large was the Confederate diaspora, and who comprised it? A: Estimates from linked Census records suggest that nearly one million whites left the former Confederacy for the rest of the U.S. in the three decades after the war, including more than 61,000 former enslavers and 127,000 of their household kin. By 1900, migrants from the former Confederacy averaged 2.2% of the population in non-Southern destination counties. The diaspora hailed primarily from the upper South — Virginia, Tennessee, and North Carolina — and later from Texas, Arkansas, and Oklahoma.

Q: How do the authors construct the shift-share instrumental variable, and what identifying assumption does it require? A: The SSIV multiplies each Southern origin state’s 1870 settlement shares across non-Southern counties (the shares) by predicted total Southern white outflows from 1870 to 1900 (the shifts), where the predicted shifts are constructed by summing LASSO-selected origin-county push factors — economic conditions, cotton and tobacco potential, Civil War battle locations, Black population share — rather than actual flows. The exclusion restriction requires that these predicted push-factor-driven outflows affect destination county outcomes only through the Confederate diaspora they deliver, not through direct economic linkages with origin counties. Conditioning on the 1870 Southern white share absorbs time-invariant destination heterogeneity correlated with antebellum settlement.

Q: What are the IV estimates for Confederate memorialization and UDC chapters? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of Confederate memorialization by 3.4 p.p. after controlling for the 1870 share (relative to a baseline prevalence of 25% outside the South). For UDC chapters, which were present in only 10% of non-Southern counties, IV estimates show similar or larger proportional effect sizes. IV estimates are consistently more than twice the size of OLS estimates, consistent with downward bias from economic sorting of Southern whites toward productive, culturally-diverse destinations.

Q: What are the IV estimates for KKK activity and Black lynchings, and how are they interpreted? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of KKK chapter presence by 3.5 p.p. (controlling for 1870 shares), relative to a mean KKK prevalence of 37% in non-Southern counties, implying that moving from zero to the mean diaspora share is associated with an 8 p.p. increase in the probability of KKK activity. For Black lynchings, the corresponding IV estimate is 1.5 p.p. (column 5), with the effect rising when earlier migration is controlled, against a mean prevalence of only 5% — implying moving from zero to the mean raises lynching likelihood by 4 p.p. Critically, the authors find no diaspora effect on white lynchings, which distinguishes racially-targeted violence from a generalized Southern culture of violence.

Q: What is a “sundown town” and what does the paper find about the diaspora’s role in producing them? A: Sundown towns, described in historical research by Loewen (2005), are all-white towns where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960 and representing a novel form of racial exclusion distinct from de jure Jim Crow institutions. The authors find that a 1 p.p. increase in the size of the Confederate diaspora in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation — defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 — changing the geography of Black settlement throughout the 20th century.

Q: What role did former slaveholders specifically play, and how are their effects separately identified? A: Former slaveholders comprised just over 6% of the Confederate migrant sample but played an outsized role: they were about 50% more likely than the average Southern white migrant to work in any public-facing authority occupation, more than twice as likely to work as lawyers or judges, and nearly three times as likely to work in public administration. Their effects are identified using an analogous SSIV that, conditional on the instrumented overall diaspora, draws on distinct identifying variation in slaveholder-specific push factors. Former slaveholders gravitated toward Western, lower-density, cotton-suitable counties with higher Breckinridge vote shares and fewer Union Army soldiers, consistent with seeking to reconstruct antebellum hierarchies in malleable frontier spaces.

Q: Why were effects stronger in frontier counties? A: The paper finds that diaspora impacts on Confederate culture diffusion were significantly larger in counties along the frontier, where state institutions were weak and cultural norms not yet deeply ingrained. Restricting the sample to counties with fewer than 2 residents per square mile in the 1860 Census yields somewhat larger estimates than baseline, and the differential sorting of Southern whites (especially former slaveholders) into these nascent communities suggests that institutional malleability amplified the cultural entrepreneurs’ influence. Fewer Union Army enlistees in destination counties also amplified effects, as those families might otherwise have opposed resurgent Confederate ideology.

Q: How did the diaspora transmit its norms to subsequent generations and non-Southern neighbors? A: In the Denver metropolitan area, using newly digitized KKK membership records, first-generation Southern migrants were 11% more likely to join the KKK than men with no Southern heritage, and a similar differential holds for second-generation migrants (born in the diaspora), with patterns holding within Census enumeration blocks. White men without Southern heritage living next door to first- or second-generation Southern whites were significantly more likely to join the KKK, consistent with horizontal cultural spillovers. For naming patterns, non-Southern white parents who moved to counties with a larger Confederate diaspora gave their later-born children names more evocative of Confederate heroes than those given to earlier-born children — providing direct evidence of cultural spillovers beyond the diaspora.

Q: What long-run effects of the diaspora are documented through the 21st century? A: Using the county-level SSIV strategy, the paper finds that a larger Confederate diaspora in 1900 is associated with larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, and higher rates of police-induced Black mortality through the 21st century. These disparities are mirrored in more conservative racial attitudes among whites in these counties as measured in modern survey data. These persistent effects suggest that, despite racially progressive national policy reform since the 1960s, locally institutionalized mechanisms reinforced by a culture of racial animus continue to generate inequity.

Q: How robust are the main estimates to alternative specifications? A: The authors show robustness across: (i) alternative spatial standard errors using Conley (1999) distance-based clustering and Adao et al. (2019) shift-share inference corrections; (ii) Belloni et al. (2014) double LASSO control selection; (iii) replacing predicted shifts with actual shifts; (iv) a random-shifts placebo where fewer than 5% of coefficients are significant; (v) dropping individual origin or destination states one-by-one (all estimates remain significant with 97% positive Rotemberg weights); (vi) excluding border states with antebellum slavery (Delaware, Kentucky, Maryland, Missouri, West Virginia), which actually increases estimates; and (vii) restricting to newly incorporated counties with near-zero 1860 populations, which yields somewhat larger effects.

Q: What is the paper’s contribution to the culture-institutions literature? A: The paper uses granular data on migration, occupational choices, and local governance to shed light on the historical process by which Confederate “cultural entrepreneurs” captured early institutions across America, illustrating how culture and institutions reinforce each other during critical junctures of nation-building. The findings suggest that laws to reduce racial discrimination may have limited impact where a culture of racial animus is ingrained in local institutions — an institutionalized persistence mechanism that helps explain the gap between formal legal reforms and observed racial outcomes. The paper also identifies a prestige-biased cultural transmission channel, consistent with Henrich and Gil-White (2001), wherein non-elite masses emulate former slaveowners in positions of power.

Confederate diaspora: The approximately one million white migrants, including more than 61,000 former enslavers and 127,000 of their household kin, who left former Confederate states for the rest of the U.S. in the three decades after the Civil War, comprising on average 2.2% of destination county populations by 1900 and retaining strong cultural attachments to the Confederacy.

Confederate culture: A cluster of symbolic and material expressions that coalesced in the postbellum South, encompassing Lost Cause narratives (glorifying Confederate figures and reframing secession as a defense of states’ rights rather than slavery), public memorialization (monuments, place names, school names), United Daughters of the Confederacy chapters, Ku Klux Klan activity, and lynchings of Black people — together functioning as technologies to transmit white supremacist norms and maintain racial hierarchies.

Lost Cause: A revisionist narrative emerging after the Civil War that sought to redeem the image of the South by offering noble rationalizations for secession — emphasizing Northern aggression and states’ rights while downplaying slavery — and portraying enslaved people as content and slaveowners as generously paternalistic; central to the ideology propagated by the UDC and to Confederate memorialization.

Shift-share instrumental variable (SSIV): An identification strategy that combines the 1870 distribution of Southern white migrants across non-Southern counties (shares, reflecting historical migration networks) with predicted total Southern white outflows from 1870 to 1900 constructed from origin-county push factors via LASSO (shifts), to isolate exogenous county-level variation in Confederate diaspora exposure that is insulated from endogenous location sorting.

Sundown town: An all-white municipality where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960, operationalized in this paper as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 (Black depopulation), representing a novel form of racial exclusion distinct from de jure Jim Crow institutions associated with the Confederacy.

Prestige-biased cultural transmission: An evolutionary transmission mechanism, formalized in Henrich and Gil-White (2001), in which non-elite populations emulate culturally salient leaders; invoked in this paper to explain how former slaveholders in positions of authority could diffuse Confederate norms to non-Southern whites who had no direct connection to the Confederacy.

Cultural entrepreneur: A migrant (especially a former slaveholder) who, by sorting into positions of public-facing authority — judges, lawyers, law enforcement, clergy, public administrators — at early stages of community formation when institutions are most malleable, actively embeds cultural norms into nascent local institutions, amplifying influence beyond their small population share.

The Dynamics of Internal Migration: A New Fact and its Implications

Mon, 01 Jan 0001 00:00:00 +0000

Howard and Shao document a new empirical regularity in U.S. internal migration: the t-year interstate migration rate — defined as the share of people living in a different state than they did t years ago — is approximately proportional to the square root of t. The fact is established using the Gies Consumer and Small Business Credit Panel (GCCP), a 15-year panel (2004–2018) covering approximately 1 percent of all Americans with a credit report, and is corroborated in the Panel Survey of Income Dynamics (PSID, 1969–1997), where the square root pattern holds out to a 25-year horizon. The fact is not an artifact of averaging across origins, destinations, cohorts, or age groups: most of the distribution across these cuts is concentrated close to the square root line. It holds for both people under 45 and over 45, and is robust to the choice of time period and inter-state distance.

The standard moving cost model — in which location choice is a Markov process with i.i.d. extreme-value utility shocks and large bilateral moving costs — is shown (Proposition 1) to imply that the t-year migration rate is approximately proportional to t, not sqrt(t), as moving costs tend to infinity. Simulations confirm the linear pattern persists in calibrated versions of the moving cost model even when adding state variables for prior location, home state, or age.

The paper’s main theoretical contribution is the SPACE model (Spatially and Persistently Autocorrelated Epsilons). Rather than imposing moving costs, the SPACE model assumes that person-location match-specific utility is (i) persistent over time, governed by an autocorrelation parameter rho, and (ii) spatially correlated across locations via a generalized extreme-value (cross-nested logit) structure. The model has no moving costs by default. Proposition 3 proves that as rho approaches 1, the ratio of t-year migration to 1-year migration is bounded below by sqrt(t) and above by sqrt(pi/3) * sqrt(t) — a tight bound, since sqrt(pi/3) is approximately 1.023. The calibrated rho-tilde is 0.892, implying a period-to-period autocorrelation of 1 − (1 − rho-tilde)^2 = 0.988.

The SPACE model replicates bilateral one-year migration flows, matches the decreasing hazard rate of migration conditional on duration of stay, reproduces the distribution of lifetime move counts (including the large fraction who never move and the few percent who move four or more times in 14 years), and outperforms the moving cost model at out-of-sample individual location forecasting: by 2018, the moving cost model’s mean Kullback-Leibler divergence reaches approximately 0.12 log-points per observation above the maximum-possible benchmark, versus only 0.014 log-points for the SPACE model.

Key divergences from the moving cost model arise in four areas. First, moving costs need not be large: the SPACE model rationalizes observed low migration without any moving costs, in contrast to Kennan and Walker’s (2011) estimate of average moving costs of $312,146 (2010 dollars), more than six times median household income; when moving costs are added to the SPACE model, they are roughly two orders of magnitude smaller. Second, long-run population elasticities differ sharply: in the SPACE model they remain proportional to bilateral gross migration rates, while in the moving cost model they converge to a static logit proportional to population shares — and population shares and gross migration rates have little empirical correlation, so the long-run elasticities of the two models are essentially uncorrelated across state pairs. Third, adjustment dynamics differ: in the SPACE model a permanent utility shock to Louisiana produces immediate, full population adjustment; in the moving cost model adjustment takes roughly 200 years, with Mississippi overshooting its new steady-state and New York adjusting implausibly slowly. Fourth, welfare inferences are almost reversed: the correlation between log utility changes implied by the two models using U.S. population data is −0.497, with the SPACE model attributing relative utility gains to the South and West and the moving cost model attributing gains to New York and New England.

Q: What is the square root fact, and which datasets confirm it? A: The t-year interstate migration rate scales approximately as sqrt(t). It is documented in the GCCP (2004–2018, ~1% of Americans with credit reports) and verified in the PSID (1969–1997), where the pattern holds out to a 25-year horizon. It is not driven by averaging across subgroups: the distribution of the fact across origin-destination pairs, age groups, cohorts, and starting years is concentrated close to the square root line.

Q: Why does the standard moving cost model fail to match the square root fact? A: In the moving cost model, location choice is a Markov process with i.i.d. extreme-value shocks. Proposition 1 proves that as the common component of moving costs tends to infinity, the t-year migration rate is proportional to t (linear). Because the model requires large moving costs to rationalize low migration rates, the linear prediction is unavoidable. Simulations of calibrated versions — including variants with home bias, prior-location state variables, or age — confirm the relationship remains approximately linear.

Q: What is the SPACE model, and why does it generate a square root? A: The SPACE model replaces moving costs with persistent and spatially correlated person-location match-specific utility. Utility shocks are drawn from a generalized extreme-value (cross-nested logit) distribution that allows spatial correlation, and they are autocorrelated over time with persistence parameter rho. Proposition 3 shows that as rho → 1, the ratio of t-year to 1-year migration is bounded in [sqrt(t), sqrt(pi/3)*sqrt(t)], a tight interval since sqrt(pi/3) ≈ 1.023. The intuition is that when rho is close to 1, the idiosyncratic utility process resembles a random walk, whose standard deviation grows as sqrt(t), causing migration thresholds to be crossed at a sqrt(t) rate.

Q: What is the calibrated persistence parameter, and what does it imply? A: The calibrated rho-tilde is 0.892, close enough to 1 to generate the square root fact in simulations. The implied period-to-period autocorrelation of match-specific utility is 1 − (1 − 0.892)^2 = 0.988. This calibration is achieved by solving for the largest eigenvalue of an I×I matrix of conditional migration rates.

Q: How do the two models compare on individual-level forecasting accuracy? A: Performance is evaluated using mean Kullback-Leibler divergence from the maximum-achievable log likelihood. Both models perform similarly in 2005, but by 2018 the moving cost model’s KL divergence reaches approximately 0.12 log-points per observation, while the SPACE model’s reaches only 0.014 log-points — roughly an order of magnitude better — leaving little room for improvement.

Q: How large are implied moving costs under each model? A: Kennan and Walker (2011) estimate average moving costs of $312,146 in 2010 dollars, exceeding six times the median household income. The baseline SPACE model requires zero moving costs to match observed migration levels. When an augmented SPACE model with both persistence and moving costs is calibrated to match the one-year and ten-year migration rates, the estimated moving costs are approximately two orders of magnitude smaller than those from a moving-cost-only model.

Q: How do short-run population elasticities compare across models? A: In both models, the short-run cross-elasticity of population in state i with respect to utility in state j is approximately proportional to the gross migration rate between them. Corollary 1 formalizes this for the SPACE model: dp_i/du_j = −(1/(1−rho)) * m_{i→j} for i ≠ j. This means that in the short run, both models deliver similar predictions for how populations respond to local shocks.

Q: How do long-run population elasticities differ? A: In the SPACE model, long-run elasticities remain proportional to bilateral gross migration rates — the same relationship as in the short run. In the moving cost model, Proposition 4 shows that the long-run elasticity converges to the static logit: d(log p_i)/d(v_j) = −2*p_j for i ≠ j, depending only on population shares. Since population shares and gross migration rates are empirically uncorrelated, the long-run elasticities of the two models are essentially uncorrelated across state pairs.

Q: What do the models predict about the speed of regional adjustment? A: In the SPACE model, a permanent utility shock to Louisiana causes full, immediate population adjustment in the first period with no further dynamics. In the moving cost model, the same shock generates adjustment lasting roughly 200 years. Mississippi overshoots its long-run steady state in the moving cost model due to high bilateral migration with Louisiana, while New York adjusts especially slowly due to low bilateral migration — a pattern the authors describe as potentially counterintuitive.

Q: How do the models handle events involving rapid population change, such as Hurricane Katrina? A: The SPACE model accommodates fast adjustments by assuming rapid utility changes, consistent with the observed sharp decline in Louisiana’s population share followed by a small rebound. The moving cost model requires implausible utility assumptions to match these dynamics: it implies that Louisiana utility two years after Katrina was higher than before the hurricane.

Q: What do the two models infer about which U.S. states have gained or lost relative utility over time? A: Using exact-hat algebra applied to observed U.S. population changes, the SPACE model infers that the South and West have the largest relative utility gains, while New England and the Rust Belt have the largest relative declines. The moving cost model produces nearly the opposite inference: New York and New England show relative utility gains, while the South and West show declines. The correlation between the log utility changes implied by the two models is −0.497.

Q: Why do the authors argue that spatially and temporally correlated utility is realistic, not merely a mathematical convenience? A: Surveys (Jia et al., 2023) show that people primarily cite family and employment considerations as reasons for interstate moves — both are persistent and geographically concentrated. Proximity to family is spatially correlated: if state i is close to one’s family, nearby states are also relatively close. Job opportunities in specific industries or skills are geographically clustered. Natural amenities and regional cultures are spatially correlated as well. The authors argue it is harder to defend the i.i.d. assumption of the moving cost model than the SPACE model’s correlated structure.

Q: What is the distinction between moving costs and persistent match-specific utility? A: A moving cost is a one-time irreversible cost paid upon leaving a location. Persistent match-specific utility implies that the utility change from moving is ongoing, partially reversible upon return, and decays with time away from the original location. The authors argue that many factors labeled “moving costs” in the literature — such as distance from friends or amenities — are more accurately characterized as persistent and partially reversible utility losses, a distinction previous models could not draw.

Q: Does the SPACE model replicate the gravity equation for bilateral migration? A: Yes. Proposition 2 shows that migration from i to j in the SPACE model is given by m_{i→j} = (1 − rho) * p_i * p_j * (1 + tau_ij), where tau_ij captures spatial correlation. This resembles a gravity equation: more spatially correlated location pairs have higher bilateral migration, and higher persistence (higher rho) implies lower overall migration levels.

Q: Can the SPACE model be embedded in broader quantitative spatial models? A: Yes. The SPACE model admits closed-form solutions for state populations and bilateral migration flows, is compatible with exact-hat algebra for dynamic counterfactuals, and supports computationally feasible individual-level simulations. Appendix E embeds the SPACE model in a housing model with durable local housing production and shows that slow population adjustment can emerge from housing durability rather than slow migration per se, providing an alternative explanation for regional divergence persistence.

SPACE model: A model of internal migration featuring Spatially and Persistently Autocorrelated Epsilons — person-location match-specific utility that is both autocorrelated over time (with persistence parameter rho) and spatially correlated across locations via a generalized extreme-value (cross-nested logit) distribution. The model contains no moving costs by default.

Square root fact: The empirical regularity that the t-year interstate migration rate (share of people living in a different state than t years ago) is approximately proportional to sqrt(t). Documented in GCCP data (2004–2018) and PSID (1969–1997) up to a 25-year horizon.

Moving cost model: The standard dynamic discrete-choice model of migration in which an agent living in state i chooses location j to maximize u_j − delta_ij + epsilon_j + beta*E[V’], where delta_ij is a bilateral one-time irreversible moving cost and epsilon_j is i.i.d. extreme-value. Low migration rates are rationalized by large moving costs (e.g., $312,146 average in Kennan and Walker 2011).

Persistence parameter (rho): In the SPACE model, rho governs the autocorrelation of match-specific utility over time. The calibrated value is rho-tilde = 0.892, implying period-to-period autocorrelation of 0.988. As rho → 1, the model generates a square root relationship between the t-year migration rate and t.

Population cross-elasticity: The elasticity of population in state i with respect to utility in state j. In both models it is proportional to gross bilateral migration in the short run. In the long run, the SPACE model retains this proportionality to migration rates, while the moving cost model converges to a static logit proportional to population shares.

Exact-hat algebra: A solution method for computing counterfactual equilibria in terms of ratios of new to old values (hats), without requiring knowledge of levels. The SPACE model admits simple exact-hat formulas for population changes; the moving cost model’s exact-hat algebra additionally requires tracking past population changes.

Kullback-Leibler divergence (in this context): The mean divergence between a model’s predicted distribution over future locations and the empirical distribution, used as a measure of forecasting accuracy. By 2018, the SPACE model achieves KL divergence of 0.014 log-points per observation versus approximately 0.12 for the moving cost model.

The Dynamics of Verification when Searching for Quality

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops a dynamic principal-agent model in which a principal seeks to select exactly one project from a stream of possibilities emerging over time, while a biased agent (who wants any project selected, regardless of quality) reports project quality each period. The principal cannot observe quality directly but can pay a cost c to verify it. Monetary transfers are unavailable. The central question is how verification and selection rules should optimally evolve over time as new options arrive.

The model is set in discrete time with an infinite horizon (extended to finite horizons in Section 6.1). Each period, a project of quality h with probability q = λΔ or quality l with probability 1 − q arrives i.i.d. The principal selects at most once; the agent receives utility 1 from any selection and 0 otherwise; the principal’s payoff equals project quality net of verification costs. Both parties share discount factor δ = e^{−ρΔ}.

When verification costs are low (c ≤ h) and the horizon is effectively infinite, the optimal mechanism exhibits decreasing skepticism: verification of high-quality reports occurs with a probability that is strictly declining over time, hitting zero at an endogenous deadline T* = ⌈(1−q)(δr − l) / (qc(1−δ))⌉. At that deadline, the principal selects any project irrespective of quality. Before the deadline, the agent reports truthfully — proposing only high-quality projects — and is incentivized by the threat of verification catching a lie, which triggers permanent exclusion. As the deadline approaches, the agent’s continuation value rises (guaranteed allocation arrives sooner), so the loss from a detected lie grows, and less verification is needed to deter misreporting. The deadline length is weakly increasing in h and r and decreasing in l and c; as c → 0, T* → ∞ and the principal’s payoff converges to the first-best of qh/(1−δ(1−q)).

When verification costs are high (h < c < c̄, where c̄ is an explicitly computed threshold), deterministic selection is suboptimal. The optimal mechanism has two sequential phases: a randomization phase (periods 1 through T_R = ⌊log(h/c)/log(1−q)⌋ + 1) in which the principal randomizes between selecting and never selecting after a high-quality report without any verification, and a subsequent verification phase matching the low-cost structure. Verification is strictly backloaded: the principal never uses both tools simultaneously in the same period, and randomization always precedes verification. The intuition is that verification acts as a reward to the agent (guaranteeing allocation when h is realized), so delaying it allows earlier periods to exploit the prospect of future verification to relax incentive constraints across more periods, accumulating gains that justify the high verification cost.

When the horizon is short (T ≤ T̄ := ⌊−(1−q)l/(qc)⌋) and l < 0 (static bias), increasing skepticism emerges: verification probability rises toward 1 in the final period. This occurs because a shrinking horizon reduces the agent’s continuation value, weakening the punishment for a detected lie, so more verification is required to maintain incentive compatibility. The paper also establishes that under renegotiation-proofness (Ray 1994), the optimal mechanism takes the same qualitative form as the full-commitment case but with permanent exclusion replaced by a mechanism restart. The leading application is board oversight of CEO-proposed acquisitions, motivated by the Smith v. Van Gorkom Delaware Supreme Court ruling; Graham et al. (2020) is cited as broad empirical support for decreasing oversight of CEOs over time.

Q: What is the core agency conflict in the model? A: The agent receives utility 1 from any selection regardless of quality, while the principal’s payoff equals quality minus verification costs. The agent always prefers immediate selection, while the principal prefers waiting for high quality, formalized by the condition qh + (1−q)l < qh/(1−δ(1−q)). This is “dynamic bias.” “Static bias” additionally arises when l < 0, meaning the principal prefers not allocating to allocating a low-quality project; this second source of conflict is more common in static settings.

Q: What is the endogenous deadline T* and what determines its length? A: T* = ⌈(1−q)(δr − l)/(qc(1−δ))⌉. It is weakly increasing in h and r (higher upside makes waiting worthwhile), weakly decreasing in l (a less costly low type shortens the horizon), and decreasing in c (cheaper verification makes longer search feasible). The term δr − l reflects the value of an additional quality draw relative to selecting low quality. As c → 0, T* → ∞ and the principal’s payoff converges to the first-best.

Q: Why does the verification probability decline over time under decreasing skepticism? A: As the deadline T* approaches, the agent’s continuation value from truthful play rises because guaranteed allocation is nearer. The loss from having a lie detected — permanent exclusion — therefore grows in absolute expected terms. Since more severe punishment requires less verification to deter misreporting, the minimum verification probability that satisfies the low type’s incentive compatibility constraint falls strictly over time, reaching zero exactly at T*.

Q: When is randomization of the selection rule optimal, and when is verification strictly better? A: Randomization is optimal if and only if c > h — when verification would guarantee a negative ex-post payoff for the principal. When c ≤ h, replacing randomization probability (1 − p̂_h) with verification probability x_h = 1 − δu_{t+1} maintains incentive compatibility while yielding a net gain to the principal proportional to h − c > 0 per period. The condition c > h is both necessary and sufficient for the randomization-augmented mechanism to dominate.

Q: Why is verification backloaded when c > h? A: Verification guarantees allocation whenever h is realized, which is a valuable reward for the agent. Deploying this reward later allows earlier randomization-phase periods to exploit the prospect of future verification to relax incentive constraints across multiple periods, accumulating gains. Moving verification earlier yields the same static cost but foregoes these accumulated gains; thus backloading verification is optimal. The principal never simultaneously randomizes and verifies in the same period.

Q: What are the two phases in Theorem 2 and how long does each last? A: The randomization phase runs from period 1 through T_R = ⌊log(h/c)/log(1−q)⌋ + 1; during this phase the principal randomizes allocation after a high-quality report (with the outside-option probability declining toward 0) but never verifies. The verification phase runs from T_R + 1 through a deadline at T* or T* + 1, with verification probability declining over time exactly as in Theorem 1. The total deadline is T* = T_R + ⌊(h − c − (l − δr)/(1−δ))(1−q)/(qc)⌋.

Q: Under what conditions does increasing skepticism emerge? A: Increasing skepticism arises when the horizon is finite and short — specifically when T ≤ T̄ = ⌊−(1−q)l/(qc)⌋, which requires l < 0 (static bias present). In this regime, verification probability rises to 1 in the final period T. Before T, the agent’s continuation value shrinks as fewer drawing opportunities remain, weakening the punishment for detected lies, so verification must increase to maintain incentive compatibility. Decreasing skepticism necessarily emerges only given a horizon long enough to overcome static bias.

Q: How does the renegotiation-proofness extension modify the optimal mechanism? A: Under renegotiation-proofness following Ray (1994), the mechanism cannot indefinitely withhold allocation following a detected lie, because both parties would prefer to restart rather than receive zero forever. The optimal renegotiation-proof mechanism takes the same qualitative form as Theorems 1 and 2, but permanent exclusion is replaced by a restart to the first period whenever a lie is verified during the verification phase or allocation is withheld during the randomization phase after a high-quality report. Deadlines, verification dynamics, and the phase structure are otherwise unchanged.

Q: What is the three-region form of the value function? A: Lemma 4 identifies thresholds u_low < u_high such that: for promised utility u ∈ [0, u_low], x_h(u) = 0 (no verification; only randomization); for u ∈ [u_low, u_high], dV/du = h − c (verification is interior, slope equals net benefit of verification); and for u > u_high, x_h(u) + y(u) = 1 (verification is at maximum). The slope h − c is constant on the middle region because increasing verification by ε raises promised utility by qε and the objective by q(h−c)ε, yielding a constant marginal rate.

Q: What revelation-principle simplifications reduce the problem? A: Lemmas 1–3 establish: (i) only high-type reports are ever verified (x_l = 0), since verification of the low type cannot improve principal payoffs; (ii) following verified truthfulness, allocation occurs with probability 1 (p*_{hh} = 1); (iii) the high type’s incentive constraint never binds in the optimal solution; and (iv) only the low type’s incentive compatibility constraint binds. These reduce the optimization to four free variables — x_h, p̂_h, p̂_l, û_l — subject to two binding constraints.

Q: How does the paper relate to Kovac et al. (2013)? A: The model builds most directly on Kovac et al. (2013)’s principal-agent stopping problem, which lacks costly verification. The key addition is the verification technology; the paper shows that when c ≤ h, verification eliminates the need for randomized selection rules that arise in Kovac et al. (2013). Kovac et al.’s randomization logic resurfaces in the randomization phase when c > h, and the analysis applies and extends Kovac et al.’s innovations.

Q: What empirical and institutional evidence motivates the model? A: The Smith v. Van Gorkom Delaware Supreme Court ruling (1985) established that boards must make meaningful efforts to become informed — exercising verification — as part of their duty of care in acquisition approvals; the TransUnion board was found negligent after approving an acquisition following a twenty-minute presentation with no written materials. Graham et al. (2020) provides broad empirical support for decreasing board oversight of CEOs over time, consistent with the paper’s decreasing skepticism prediction. Gompers et al. (2020) on VC analysts’ project evaluation processes also illustrates the general applicability.

Decreasing skepticism: The property of the optimal mechanism whereby the principal verifies high-quality reports with a probability that strictly declines over time, reaching zero at the endogenous deadline. Reflects diminishing concern about misrepresentation as the agent’s continuation value — and thus the cost of a detected lie — rises as the deadline approaches.

Endogenous deadline (T*): The period at which the principal allocates any project irrespective of quality, ending the mechanism. Determined by T* = ⌈(1−q)(δr − l)/(qc(1−δ))⌉, balancing the value of waiting for additional quality draws against verification costs; weakly increasing in h and r, decreasing in l and c.

Static bias vs. dynamic bias: Dynamic bias denotes the conflict that the principal prefers waiting for high quality while the agent prefers immediate selection. Static bias is the additional conflict (arising when l < 0) that the principal prefers withholding allocation to selecting a low-quality project, mirroring the agent-prefers-higher-action conflict in standard static models. Decreasing skepticism necessarily obtains absent static bias; static bias may flip dynamics to increasing skepticism if the horizon is short.

Backloaded verification: The property that when c > h, verification is deployed only after a complete randomization phase, never simultaneously with randomization. Arises because verification acts as a reward to the agent by guaranteeing allocation when high quality is realized, and delaying this reward allows its incentive-relaxation benefits to compound across more randomization-phase periods.

Randomization phase: The initial phase (periods 1 to T_R) in the high-cost regime, in which the principal randomizes the allocation decision after a high-quality report (outside option selected with declining probability) without using the verification technology. The randomization probability is set to keep the low type indifferent between truthful reporting and misreporting.

Increasing skepticism: The opposite verification dynamic from decreasing skepticism, arising when the horizon is short (T ≤ T̄) and l < 0 (static bias). Verification probability rises over time toward 1 in the final period, because the agent’s continuation value shrinks as drawing opportunities dwindle, weakening the deterrent effect of detection and requiring more frequent verification to maintain incentive compatibility.

Incentive compatibility via verification: The mechanism through which the principal deters low-type misreporting: by verifying a reported high-quality project with probability x_h, and punishing detected lies with permanent exclusion (or restart under renegotiation-proofness). This strictly dominates selection randomization when c ≤ h because the net per-period gain equals h − c > 0 while maintaining the same incentive compatibility condition for the low type.

The Economics of Equilibrium with Indivisible Goods

Mon, 01 Jan 0001 00:00:00 +0000

This paper develops an economic theory of competitive equilibrium with indivisible goods that accommodates both complementarities and substitutabilities. The central research question is: what conditions on demand are sufficient, and essentially necessary, for the existence of competitive equilibrium prices when goods are indivisible?

The classical answer — gross substitutes (Kelso and Crawford, 1982) — entirely rules out complementarities. Complementarities matter in practice, yet prior work showed that equilibrium does not generally exist when all goods are complements (Bikhchandani and Mamer, 1997), while certain patterns of complementarities are compatible with equilibrium (Greenberg and Weber, 1986; Danilov, Koshevoy, and Lang, 2013). The economic content of which patterns permit equilibrium has remained opaque, previously accessible only through combinatorial or tropical geometry.

Jagadeesan and Teytelboym’s key conceptual move is to analyze complementarity and substitutability between bundles of goods, rather than between individual goods. They introduce a bundle consistency condition: each pair of relevant bundles — defined via the compensated price effects of agents — must be either consistently substitutable or consistently complementary across all agents. A bundle is relevant if it arises as a price effect (revealing either direct complementarity or hidden complementarity between a good and an opportunity to sell another good) or consists of a single good. Bundle consistency is formulated as: for each bundling composed only of relevant bundles, each pair of bundles within it must be consistent.

The paper establishes three core results. First (Theorem 1), for economies in which each agent demands at most one unit of each good, bundle consistency is sufficient for competitive equilibrium existence. Second (Theorem 2), bundle consistency is essentially necessary: if competitive equilibria exist for all economies in which agents have valuations in an invariant domain, then those valuations are bundle-consistent. “Invariant” requires closure under addition of nonneg linear functions and inclusion of the zero valuation — a condition satisfied by all major prior domains including gross substitutes, consecutive games, substitutes-and-complements, and all classes of discrete convexity. Third, for the multiunit demand setting (Theorems 3 and 4), unit consistency is additionally required: units of the same good must be substitutes for each other. This rules out increasing returns to scale at the unit level, analogous to the absence of increasing returns in standard divisible-good theory.

The sufficiency proof works by showing that unit- and bundle-consistent preferences lie within a class of discrete convexity (Danilov, Koshevoy, and Murota, 2001), with bundle consistency shown equivalent (Proposition 3) to total unimodularity of the matrix of all agents’ price effects in {-1, 0, 1}^I. Equilibrium existence then follows from existing results for discrete convex economies.

A testable characterization is provided: preferences are bundle-consistent if and only if the set of all agents’ price effects in {-1, 0, 1}^I is totally unimodular (Proposition 3, under unit consistency). This gives a finite, computable test.

The scope conditions are explicit: the full theorem applies to agents with continuous utility functions strictly increasing in money; income effects are permitted. The necessity results apply to invariant domains. The multiunit extension requires the additional unit consistency condition. The paper does not impose quasilinearity for the main theorems, though geometric appendices restrict to the quasilinear case for the connection to tropical geometry.

The results unify all previously known sufficient conditions for equilibrium existence with indivisible goods — substitutes, consecutive games, substitutes-and-complements, and the geometric domains — as special cases of bundle consistency. Crucially, Example 3 (four goods, six agent types with additive and pairwise-complement valuations) demonstrates a case where equilibrium exists under bundle consistency even though no bundling makes all agents view bundles as substitutes, so the result cannot be derived from Kelso-Crawford by rebundling.

Q: What is the fundamental obstruction to equilibrium existence with indivisible goods, according to this paper?

A: The only essential obstruction is an inconsistency between substitutability and complementarity across a pair of relevant bundles — that is, one agent seeing two bundles as substitutes while another sees them as complements. With only two goods (or only two units), consistency between goods themselves suffices. With more goods, apparent consistency at the good level can mask bundle-level inconsistency, as shown in Example 1 (three goods, each pair complements, yet no equilibrium exists). Bundle consistency — requiring pairwise consistency for all relevant bundlings — captures the full obstruction.

Q: What makes a bundle “relevant” for the purpose of bundle consistency?

A: A bundle b in {-1, 0, 1}^I is relevant if it either arises as a compensated price effect for some agent (revealing which goods move together following a price decrease, including negative entries that reveal hidden complementarities between a good and the opportunity to sell another) or consists of a single good e_i. Bundles with negative components (sale opportunities) are included because sale opportunities can themselves be complementary to goods — the “hidden complementarity” concept from Ostrovsky (2008) and Hatfield et al. (2013, 2019).

Q: Why does the three-cycle-of-complements example (Example 1) fail to have an equilibrium, and how does bundle consistency detect this?

A: Three agents hold V^1 = 3 min{x_a, x_b}, V^2 = 3 min{x_b, x_c}, V^3 = 3 min{x_a, x_c}, with one unit of each good available. Every pair of goods is complementary for some agent, so no inconsistency appears at the goods level. However, under the bundling B = {(1,0,0), (1,1,0), (0,0,1)} (apples-and-bananas bundled, coconuts separate), a fall in the coconut price induces agent 2 to buy the apple-banana bundle and sell apple, making apple and coconut substitutes for agent 2 while they remain complements for agent 3 — a bundle inconsistency. Bundle consistency detects this whereas good-level consistency does not.

Q: What distinguishes the consecutive-games pattern (Example 2) from the three-cycle pattern (Example 1), and why does equilibrium exist in the former?

A: In Example 2, agent 3’s valuation is replaced by V^3 = 3 min{x_a, x_b, x_c}: coconuts are complementary to apples only in conjunction with bananas, not directly. Under the same bundling B, a fall in the coconut price again makes apple and coconut substitutes for agents 2 and 3, but now this substitutability is consistent — neither agent sees apple and coconut as direct complements independently of bananas. Bundle consistency holds, and Greenberg and Weber (1986) confirm equilibrium existence for all endowments. The difference between the two examples hinges entirely on whether coconuts are directly complementary to apples or only complementary to apples in combination with bananas.

Q: How does bundle consistency relate to the prior geometric approaches (discrete convexity, tropical geometry)?

A: Proposition 4 establishes that a family of utility functions belongs to a single class of discrete convexity (Danilov, Koshevoy, and Murota, 2001) if and only if the family is unit- and bundle-consistent. Proposition 3 establishes that (under unit consistency) preferences are bundle-consistent if and only if the set of all agents’ price effects in {-1, 0, 1}^I is totally unimodular — the same mathematical condition underlying Baldwin and Klemperer’s (2019) totally unimodular demand types. The paper thus provides economic interpretations for the entire class of geometric domains, not just substitutes or specific named cases.

Q: What does unit consistency require, and why is it needed in the multiunit setting?

A: Unit consistency requires that for any good i and any two serial-number indices m < m’, the m-th and m’-th units of good i are substitutes for each other (Definition 6). This rules out increasing returns to scale in units of the same good: with one indivisible good, increasing returns arise if and only if units of that good are complements. Since units of the same good are mechanically substitutes in the divisible-good limit, complementarity between units creates an inconsistency between substitutability and complementarity at the unit level. Unit consistency is automatically satisfied when each agent demands at most one unit of each good.

Q: What is the “essentially necessary” sense of the necessity results (Theorems 2 and 4)?

A: The results require that the domain be “invariant” — closed under addition of nonneg linear price functions and containing the zero valuation. This is satisfied by all major prior domains: substitutes, consecutive games, substitutes-and-complements, sign-consistent tree valuations, all classes of discrete convexity, and all totally unimodular demand types. For any such domain in which competitive equilibria are guaranteed to exist for all economies, the domain’s valuations must be bundle-consistent (Theorem 2) or unit- and bundle-consistent (Theorem 4). This is stronger than previous necessity results because it covers any invariant domain, not just specific named ones.

Q: How can bundle consistency be tested computationally?

A: Under unit consistency, Proposition 3 gives a finite test: collect all agents’ compensated price effects that lie in {-1, 0, 1}^I and form a matrix with these vectors as columns. Preferences are bundle-consistent if and only if this matrix is totally unimodular. Total unimodularity of an integer matrix can be verified in polynomial time using standard results from combinatorial optimization (Schrijver, 1998). Example 3 demonstrates this explicitly: for four goods and six agent types (additive plus four pairwise-complement pairs plus one all-complement agent), the 4x9 price-effect matrix is verified to be totally unimodular, confirming bundle consistency and equilibrium existence.

Q: Does bundle consistency imply that some rebundling of goods makes all agents treat bundles as substitutes?

A: No — this is a key finding. Example 3 shows a case where bundle consistency holds and equilibrium exists, yet Danilov, Koshevoy, and Lang (2013) confirm that no bundling exists for which all agents view the bundles as substitutes. Thus, the paper’s equilibrium existence result is strictly stronger than what could be obtained by applying Kelso and Crawford (1982) after rebundling goods. Bundle consistency is a weaker condition than the existence of a substitute-making rebundling.

Q: What are the implications of the results for auction design?

A: The paper suggests that bidding languages for sealed-bid multi-item auctions can be extended beyond the quasilinear-substitutes case (where Milgrom’s (2009) assignment messages apply) by using the economic concepts of bundling and consumer theory. Since bundle consistency characterizes when market-clearing prices exist even with complementarities and income effects, auction formats that guarantee equilibrium existence could in principle be designed for the full bundle-consistent domain, accommodating richer preference structures including complementarities and income effects.

Q: How do “hidden complementarities” enter the analysis and why must bundles with negative components be considered?

A: When a good’s price falls and demand for another good decreases, this reveals a hidden complementarity between the first good and the opportunity to sell the second. Ostrovsky (2008) and Hatfield et al. (2013, 2019) identified this structure in trading networks. Ignoring these hidden complementarities would miss obstructions to equilibrium existence: Online Appendix E provides an example where the full set of obstructions is only revealed by including bundles with negative components (sale opportunities) among the relevant bundles. This is why relevant bundles are defined to include price effects with negative entries, and bundles in a bundling are allowed to have negative components.

Bundle consistency: The condition that for each bundling composed solely of relevant bundles, each pair of bundles within it is either consistently substitutable or consistently complementary across all agents — meaning no two agents disagree on whether the bundles are substitutes or complements. This is the paper’s central sufficient and essentially necessary condition for equilibrium existence.

Relevant bundle: A bundle b in {-1, 0, 1}^I that is either a compensated price effect for some agent (a vector describing how demand changes following a price decrease, including negative entries for goods whose demand falls) or the unit vector e_i for a single good i. Only relevant bundles determine the obstructions to equilibrium existence.

Compensated price effect: A nonzero vector delta_x for which there exist a utility level u, a price vector p, and a lower price p’_i at which demand shifts from x to x + delta_x, with unique demand at both prices. Price effects identify which pairs of goods are strict complements (same-sign entries) and which involve hidden complementarities (opposite-sign entries).

Hidden complementarity: A complementarity between a good and the opportunity to sell another good, revealed when a price effect has a negative entry — meaning demand for some good decreases following the price decrease of another. The concept unifies settings with substitutes and with complements by treating sale opportunities as analogous to goods.

Unit consistency: The condition that for any good i and any two units m < m’ of that good, the m-th and m’-th units are substitutes. This rules out increasing returns to scale at the unit level and is needed for equilibrium existence in the multiunit demand setting; it is automatically satisfied in the single-unit case.

Total unimodularity (of price effects): The property, for the matrix formed by stacking all agents’ price effects in {-1, 0, 1}^I as columns, that every square submatrix has determinant in {-1, 0, 1}. Proposition 3 establishes this is equivalent to bundle consistency under unit consistency, providing a computable test and linking the economic conditions to the geometric literature.

Invariant domain: A domain V of valuations closed under addition of nonneg linear price functions (V(x) + p*x remains in V for all p >= 0) and containing the zero valuation. Invariance is the scope condition under which the necessity theorems apply; it is satisfied by all major prior equilibrium existence domains.

The Effect of Provider Diversity on Racial Health Disparities: Evidence from the Military

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether racial concordance between patients and medical providers — specifically, whether Black patients are treated by Black physicians — improves use of preventive care and reduces mortality among patients with chronic, manageable diseases. The authors argue that trust and communication deficits along racial lines cause Black patients to underuse low-cost, life-saving preventive care, and that increasing the share of Black providers addresses this deficit.

The authors use data from the Military Health System (MHS) Data Repository covering fiscal years 2003–2013, encompassing roughly 9.6 million beneficiaries. A distinctive feature of the MHS is that active-duty providers are themselves MHS beneficiaries, so their race is observed in the same eligibility files used for patients — overcoming the typical absence of provider-race data in claims databases. The study focuses on four chronic, deadly but manageable conditions: diabetes, hypertension, hypercholesterolemia, and clinical atherosclerotic cardiovascular disease. Preventive care is measured by medication fill-days for condition-appropriate generic drugs, HEDIS-recommended Comprehensive Diabetes Care compliance, and (for a subset) blood pressure control. Mortality is tracked across the full sample period.

The identification strategy exploits quasi-random variation in provider racial composition induced by across-base moves. The MHS setting generates abundant moves driven by DoD personnel management needs — not by patient health or preferences. Using a movers-only differences specification (analogous to Finkelstein et al. 2016), the authors compare differential changes in outcomes for Black versus non-Black patients who move to bases with larger versus smaller increases in the share of Black providers. This design includes fixed effects for both sending and receiving bases, controlling flexibly for regional quality differences. The estimand is an intent-to-treat effect among patients living within 10 miles of a base (who use on-base care 66% of the time).

The findings are consistent across all four disease samples. For diabetes, a move-induced one-standard-deviation increase in the share of Black diabetes providers is associated with a roughly 6 additional metformin fill-days per year (approximately 16% relative to the mean) and a 3 percentage-point increase (roughly 8% relative to the mean) in Comprehensive Diabetes Care compliance for Black relative to non-Black patients. Mortality falls by 0.4 percentage points — a 33% relative decline — for Black relative to non-Black diabetes patients following such a move.

Pooling across all four chronic-disease samples, a one-standard-deviation move-induced increase in the Black provider share is associated with approximately 3 additional fill-days of relevant preventive medication and a roughly 0.2 percentage-point reduction in mortality — approximately 15% relative to the mean mortality rate — for Black relative to non-Black patients.

A decomposition analysis combining the paper’s estimates with medical-literature parameters on the mortality effects of preventive medications finds that between 55% and 69% of the concordance mortality effect across the four disease samples can be attributed to improved medication adherence alone, with the remainder attributed to other aspects of the provider-patient relationship (e.g., lifestyle effects, other preventive care).

Scope conditions: results are local to MHS movers, who are on average slightly younger and healthier than non-movers, potentially understating concordance benefits for the full population. The MHS covers over 3% of all Black U.S. residents, but beneficiaries may differ from the general population. The paper measures Black patient / Black provider concordance specifically; it does not establish a symmetric concordance effect for non-Black patients. The concordance effect estimated is relative — it captures how much Black patients benefit more than non-Black patients from moving to a higher Black-provider-share base. A system-wide spillover mechanism (non-Black providers improving care for Black patients when working alongside more Black providers) cannot be ruled out and would also be consistent with the core concordance motivation.

Q: What is the central research question and why is the MHS an advantageous setting? A: The paper asks whether racial concordance between providers and patients causes Black patients to use more preventive care and achieve better health outcomes, focusing on the trust and communication channel. The MHS is advantageous because active-duty providers are themselves MHS beneficiaries, making their race observable — a feature absent in most claims databases. Across-base moves are driven by DoD staffing needs rather than patient health or preferences, providing quasi-random variation in provider racial composition. The system offers complete claims data covering both on- and off-base care, allowing full mortality tracking.

Q: How does the empirical strategy address selection concerns that plague prior concordance studies? A: Prior studies face selection problems from Black patients choosing different doctors than white patients and from residential segregation concentrating Black patients and Black physicians in regions with distinct care quality. The movers-based differences specification directly addresses both problems: it uses only patients who move across bases, comparing how the same individual’s outcomes change relative to non-Black patients experiencing the same move, as a function of the move-induced change in the Black provider share. Inclusion of fixed effects for both sending and receiving bases accounts flexibly for regional quality differences. Balance tests on observable patient characteristics show no differential sorting of Black versus non-Black patients toward high-Black-provider-share bases.

Q: What specific preventive care and outcome measures are used for each disease? A: For diabetes, the primary measures are annual metformin fill-days and Comprehensive Diabetes Care (CDC) compliance — defined as receiving HbA1c testing, a retinal eye exam, and medical attention for nephropathy in the focal year — plus blood pressure control (available only from 2009 onward for on-base patients). For hypertension, the measures are annual fill-days of WHO-recommended antihypertensives (thiazides, ACEs/ARBs, or long-acting dihydropyridine CCBs) and blood pressure control. For hypercholesterolemia, the measure is fill-days of antilipemic agents, bile acid sequestrants, and statins. For atherosclerotic cardiovascular disease, the HEDIS statin therapy receipt indicator is used. Mortality is tracked across all four samples.

Q: What are the main quantitative results for the diabetes sample? A: A move-induced one-standard-deviation increase in the share of Black diabetes providers is associated with approximately 6 additional metformin fill-days annually for Black relative to non-Black patients (roughly 16% relative to the mean). Compliance with Comprehensive Diabetes Care increases by 3 percentage points for Black relative to non-Black patients (roughly 8% relative to the mean). Mortality falls by 0.4 percentage points for Black relative to non-Black patients — a 33% relative decline — in connection with the same one-standard-deviation increase in Black provider share.

Q: What are the pooled results across all four chronic-disease samples? A: Pooling across diabetes, hypertension, hypercholesterolemia, and atherosclerotic cardiovascular disease, a one-standard-deviation move-induced increase in the Black provider share is associated with approximately 3 additional preventive medication fill-days per year for Black relative to non-Black patients. The pooled mortality effect is a 0.2 percentage-point reduction — roughly 15% relative to the mean mortality rate — for Black relative to non-Black patients.

Q: How much of the concordance mortality effect operates through medication adherence? A: The decomposition combines the paper’s estimated concordance effects on medication fill-days with medical-literature estimates of the mortality impact of each additional fill-day. For the diabetes sample, increased metformin adherence (4.2 additional fill-days) explains approximately 58.8% of the 0.4 percentage-point concordance mortality effect, with the residual 41.2% attributed to other channels such as lifestyle changes or other preventive care. Across all four disease samples, the medication fill-day channel explains between 55% and 69% of the respective concordance mortality effects.

Q: What specification checks do the authors conduct to validate causal identification? A: The authors conduct five main checks. First, balance regressions show that move-induced changes in Black provider share are not differentially related to baseline patient characteristics for Black versus non-Black patients. Second, regressions of the probability of moving on initial Black provider share and its interaction with patient race yield a near-zero concordance coefficient (0.008, SE 0.023), indicating no differential sorting. Third, regressions of post-move on-base care share on the concordance interaction term yield a near-zero coefficient (0.002, SE 0.003), indicating no differential race-specific selection into on-base care. Fourth, a distance falsification test shows that concordance coefficients are near zero and statistically insignificant for patients living more than 10 miles from the base. Fifth, event-study dynamics show no pre-move divergence in preventive care adherence between Black and non-Black patients, with a positive divergence emerging only after the move to a higher Black-provider-share base.

Q: How does the paper separate a concordance effect from a pure Black-physician-quality effect? A: The paper estimates a “first stage” specification on the subsample receiving on-base care (where provider race is observed), regressing the change in the probability of visiting a Black provider on the move-induced change in Black provider density. The results show an approximately one-to-one relationship between higher Black provider availability and increased visits to Black providers for all patients, with only a modest differential by patient race. This confirms that non-Black patients also see more Black providers when Black provider density rises, allowing the interaction specification to isolate concordance from a pure physician-quality effect.

Q: How do the authors assess the potential role of spillover effects? A: The authors acknowledge they cannot rule out that some of the estimated concordance effect arises through system-wide spillovers — for instance, non-Black providers on bases with more Black colleagues may improve their care for Black patients through peer learning or information transmission. They note that even if such a spillover mechanism operates, it is still consistent with the paper’s core concordance motivation, because provider-knowledge deficiencies about treating Black patients are among the theorized channels of racial discordance.

Q: What do the results imply for the overall racial mortality gap? A: Among MHS beneficiaries aged 20–65, Black beneficiaries are roughly 38% more likely to have diabetes and die over the sample period than non-Black beneficiaries; this gap appears driven primarily by higher diabetes prevalence rather than a within-diabetes mortality gap. Applying the diabetes concordance mortality estimate (a 0.4 percentage-point reduction), the authors calculate that a one-standard-deviation increase in the Black provider share would reduce the overall diabetes mortality gap from 38% to approximately 21% — a substantial narrowing driven by the concordance effect operating through conditional-on-prevalence outcomes.

Q: What are the policy implications of the findings? A: The results imply that investments in increasing physician workforce diversity could meaningfully reduce racial mortality disparities in the United States, particularly for chronic diseases manageable through preventive medication. The paper notes the results are relevant to affirmative action policies in medical school admissions, specifically the pending Supreme Court cases Students for Fair Admissions v. University of North Carolina and Students for Fair Admissions v. Harvard at the time of writing. The MHS population covered in the study includes over 3% of all Black U.S. residents, so the policy stakes extend substantially beyond the military context.

Q: What are the limitations of the study regarding generalizability? A: Movers in the chronic-disease samples are on average about four years younger and 0.2 percentage points less likely to die than non-movers, suggesting the local average treatment effect for movers may understate concordance benefits for the full population. The MHS population may be healthier overall than the general population, though conditioning on chronic-disease patients mitigates this concern. The paper covers only Black-patient/Black-provider concordance; concordance effects for other racial and ethnic groups are not estimated. The estimate of the concordance coefficient technically captures how much the Black patient / Black provider concordance effect exceeds the non-Black patient / non-Black provider concordance effect, meaning the absolute magnitude of Black concordance benefits is understated if non-Black concordance effects are also positive.

Racial concordance: In this paper’s usage, the match between the race of a patient and their treating physician — specifically Black patient / Black provider pairing — theorized to improve care through trust, communication, and reduced provider knowledge deficiencies about Black patients.

Provider Black share: The fraction of outpatient office visits for a given chronic condition at a given military base that are attended by Black active-duty providers, used as the base-level treatment variable; varies across bases from zero to approximately 20 percentage points in the pooled sample.

Movers-based differences specification: An identification strategy that restricts to patients who relocate across military bases exactly once during the sample period and estimates the differential change in outcomes for Black versus non-Black patients as a function of the move-induced change in the base’s Black provider share, including fixed effects for both the sending and receiving base.

Intent-to-treat (ITT) effect: The concordance estimate as applied to all patients living within 10 miles of a base — regardless of whether they actually received on-base care — to avoid selection bias from differential race-specific decisions to seek care on versus off base.

Comprehensive Diabetes Care (CDC): A HEDIS composite measure requiring receipt of all three of the following in the focal year: HbA1c testing, a retinal eye exam, and medical attention for nephropathy (via microalbumin exam, ACE/ARB therapy, or nephropathy treatment).

Medication fill-days: Annual days of supply dispensed for condition-appropriate generic medications (metformin for diabetes; thiazides/ACEs/ARBs/CCBs for hypertension; antilipemic agents, bile acid sequestrants, and statins for hypercholesterolemia; statins for atherosclerotic cardiovascular disease), used as the primary preventive care adherence measure.

Decomposition of concordance mortality effect: A calculation that uses the paper’s estimated concordance effect on medication fill-days, combined with medical-literature estimates of the mortality impact per fill-day, to determine what share of the total concordance mortality effect passes through medication adherence versus other channels (lifestyle, other preventive care).

The Illiquidity of Water Markets

Mon, 01 Jan 0001 00:00:00 +0000

Donna and Espín-Sánchez investigate whether a market (sequential English auction) or a non-market institution (fixed quota) more efficiently allocates an intermediate good — irrigation water — when some buyers are liquidity constrained. The setting is Mula, a city in southeastern Spain, where farmers used an unregulated water auction continuously from 1244 until August 1, 1966, when the institution was replaced by a fixed quota system. This 700-year natural experiment, combined with the fact that water demand for a given crop is pinned down by the crop’s production function rather than by farmer wealth, allows the authors to separately identify liquidity constraints from unobserved heterogeneity in productivity.

The empirical context has four features the authors exploit. First, the pre-1966 auction was entirely unregulated, so price differences directly reflect valuations without the confounds of regulatory changes. Second, water is an intermediate good for apricot production; conditional on plot area, tree count, and crop type, demand is determined by the apricot tree’s biological water requirements — not by the farmer’s wealth — so wealthy and poor farmers growing the same bulida apricot variety share the same underlying demand up to an idiosyncratic productivity shock. Third, farmers are classified as wealthy if they held positive urban real estate (non-agricultural wealth) in 1955 tax records; wealthy farmers’ average annual urban rental income (5,702 pesetas) far exceeded their average annual water expenditure (500 pesetas, rising to 1,619 in the highest-expenditure year, 1963), supporting the assumption that wealthy farmers were never liquidity constrained. Fourth, the 1966 institutional shift to quotas — under which each farmer received a fixed water allotment (tanda) every three weeks proportional to plot size, paying only a small annual maintenance fee after the critical season — provides the counterfactual.

The authors build a structural dynamic demand model with three key features: storability (irrigation raises soil moisture, creating intertemporal substitution between periods because water evaporates partially), liquidity constraints (poor farmers cannot always afford water during the critical season when prices peak), and weather seasonality (the critical season, corresponding to apricot fruit growth stages II–III and the Early Post-Harvest period, spans roughly weeks 18–32 and is when trees most need water). Farmers are forward-looking and form expectations about future prices and rainfall. The model’s production function, drawn from the agricultural engineering literature (Torrecillas et al., 2000; Allen et al., 2006), transforms soil moisture into apricot output via a transformation rate parameter gamma, a hydric stress coefficient, and a seasonal dummy.

Demand parameters are estimated using a two-step conditional choice probability (CCP) estimator (Hotz et al., 1994) on wealthy farmers only, then projected onto poor farmers’ welfare calculations. The sample consists of 24 single-crop apricot farmers observed in weekly auction records from January 1955 to July 1966, embedded in a market with over 500 total participants.

The main finding is that the institutional change from auction to quota increased total efficiency. Welfare increased by 23.4 real pesetas per farmer per tree, a 6 percent increase in total apricot production relative to the market. This gain arises because: (1) farmers were relatively homogeneous in productivity (small idiosyncratic shocks), so the primary source of misallocation was not productivity heterogeneity but wealth heterogeneity; (2) liquidity constraints prevented poor farmers from purchasing water during the critical season when their valuation was high, causing them instead to buy earlier (at lower prices but with partial evaporation loss) or later (when their trees had already experienced hydric stress); and (3) the apricot production function is concave in water, so uniform quota allocation is more efficient than market allocation when farmers are approximately homogeneous. The paper provides the first empirical demonstration that liquidity constraints can reverse the standard efficiency ranking of markets over quotas.

Q: What is the core research question? A: The paper asks whether a free market (water auction) or a non-market institution (fixed quota) more efficiently allocates an intermediate good when some buyers are liquidity constrained. The theoretical ranking is ambiguous when agents are heterogeneous in both productivity and wealth, making this an empirical question. The authors find that quotas dominated the auction in the specific Mula setting.

Q: What was the historical water market in Mula and when did it end? A: From 1244 to 1966 — over 700 years — Mula farmers used a sequential ascending-price (English) auction to allocate river water. The auctioneer sold water in discrete units called cuartas (each representing 3 hours of canal flow, or approximately 432,000 liters), holding 40 units per weekly Friday session. Farmers paid in cash on auction day. On August 1, 1966, the farmers’ union (Sindicato de Regantes) replaced the auction with a fixed quota system, having secured a credit line to purchase water property rights share by share.

Q: How did the quota system work, and how did it eliminate liquidity constraints? A: Under the quota, each plot of land received a fixed water allotment (tanda) every three weeks, proportional to plot size. Farmers paid only a small annual maintenance fee to the Sindicato at year-end, after the critical season harvest. Because payment occurred after farmers collected harvest revenue, no farmer was liquidity constrained under the quota. The fee was substantially lower than the per-unit average price under the market.

Q: How do the authors identify liquidity constraints separately from unobserved heterogeneity in productivity? A: The key insight is that water is an intermediate good whose demand is determined by the apricot tree’s biological production function, not by farmer wealth. Two farmers growing the same bulida apricot variety with the same number of trees should have the same water demand up to an idiosyncratic shock. The authors use wealthy farmers (those with positive urban real estate in 1955 tax records) to estimate preferences, under the assumption that wealthy farmers are never liquidity constrained. They then verify that outside the critical season, wealthy and poor farmers purchase similar amounts of water; the purchasing divergence appears only during the high-price critical season, consistent with a cash constraint rather than a preference difference.

Q: What empirical evidence shows poor farmers were liquidity constrained rather than simply less interested in water? A: Poor farmers display a bimodal purchasing pattern inconsistent with the apricot tree’s biological water needs: they buy water before the critical season (when prices are low) in anticipation of not being able to afford it during the critical season, and again after the critical season (when prices fall) to prevent their trees from withering from dehydration. Wealthy farmers, by contrast, delay purchases strategically to the critical season when trees most need water (weeks 18–32). Regression analysis confirms that wealthy farmers purchase significantly more water per tree during the critical season than poor farmers growing identical bulida apricots, while the difference outside the critical season is not statistically significant.

Q: How were wealthy farmers defined and why does their wealth validate the non-constrained assumption? A: A farmer is defined as wealthy if the value of their urban real estate (from 1955 urban tax records) is positive, and as poor if it is zero. Urban real estate constitutes non-agricultural wealth uncorrelated with the apricot production function. Wealthy farmers’ average annual urban rental income was 5,702 pesetas, while their average annual water expenditure was only 500 pesetas (rising to 1,619 pesetas in 1963, the highest-expenditure sample year). This large gap supports the assumption that wealthy farmers could always afford water purchases.

Q: What is the model’s treatment of soil moisture dynamics and why does it matter? A: Soil moisture (M_it) evolves according to an agricultural engineering formula: it increases with rainfall and irrigation purchases (each unit adding 432,000 liters divided by plot area) and decreases via evapotranspiration (ET), subject to a full-capacity ceiling (FC) and a permanent wilting point (PW) lower bound. This storage structure creates intertemporal substitution — water purchased early partially substitutes for future purchases, but at a cost (evaporative loss). The dynamics mean poor farmers who pre-buy water before the critical season lose some of that investment to evaporation, generating a real efficiency loss relative to the quota that delivers water closer to when it is biologically needed.

Q: What are the two sources of potential inefficiency the authors identify? A: The first is inefficiency due to heterogeneity: if farmers differ in ex-post productivity (captured by idiosyncratic shocks epsilon_it), allocating water to a less productive farmer at a given moment is wasteful. Markets correct this inefficiency (they direct water to highest-valuation buyers) while quotas do not. The second is inefficiency due to decreasing marginal returns (DMR): because the production function is concave in water, giving water to a farmer with already-high soil moisture is less productive than giving it to a farmer with low moisture. Quotas naturally avoid DMR inefficiency by allocating uniformly; markets with liquidity constraints exacerbate DMR inefficiency by directing scarce critical-season water to wealthy farmers who may have already accumulated moisture from prior purchases.

Q: What is the main quantitative result of the welfare analysis? A: Switching from the market auction to the fixed quota system increased welfare by 23.4 real pesetas per farmer per tree, representing a 6 percent increase in total apricot production relative to the market counterfactual. This is computed as the difference in yearly mean welfare per tree per farmer (net of irrigation costs, excluding water expenditures which are transfers) between the quota and market allocations using the estimated structural model.

Q: Under what conditions is a quota more efficient than a market with liquidity constraints? A: Quotas dominate markets when three conditions hold simultaneously: (1) farmers are relatively homogeneous in productivity (so the market’s advantage of directing water to high-valuation buyers is small), (2) liquidity constraints are significant (so the market misallocates water away from constrained high-valuation farmers), and (3) the production function is concave in water (so uniform allocation is efficient when farmers are homogeneous). The authors find all three conditions hold in Mula. Conversely, markets dominate quotas when heterogeneity in productivity is large relative to heterogeneity in wealth.

Q: How is the transformation rate parameter gamma estimated and interpreted? A: The transformation rate gamma measures how soil moisture above the permanent wilting point converts into apricot output (in pesetas) during the critical season, via the production function h() = gamma * (M_it - PW) * KS(M_it) * Z(w_t). It is identified from variation in purchasing patterns across seasons and variation in moisture across farmers within the same season. The preferred specification (column 3 of Table 3) yields gamma_L = 0.05. With average moisture per tree (accounting for the hydric stress coefficient) of 873.93 during the critical season, a farmer earns on average 29.09 pesetas per tree per week during the critical season, or 407.25 pesetas per tree per year.

Q: How does ignoring liquidity constraints bias demand estimates? A: If one estimates demand using the full sample (poor and wealthy farmers pooled), a decrease in demand during the critical season when prices rise conflates two effects: (1) the standard price effect (fewer farmers have valuations above the price) and (2) the liquidity constraint effect (some farmers with valuations above the price still cannot buy because they lack cash). Attributing the second effect to price sensitivity overstates the demand elasticity, biasing its absolute value upward.

Q: What robustness checks do the authors provide against unobserved heterogeneity? A: The authors provide four pieces of evidence that wealthy and poor farmers do not have systematically different underlying preferences: (1) wealthy and poor farmers are not geographically sorted into different locations (both groups appear in subareas 1, 2, 4, and 7); (2) wealthy and poor farmers grow the same bulida apricot variety; (3) outside the critical season, wealthy and poor farmers purchase statistically similar amounts of water; and (4) the purchasing divergence is significant only during the critical season when prices are high, precisely the pattern predicted by the liquidity constraint mechanism.

Q: What are the policy implications for water allocation in developing countries? A: The paper implies that before introducing water markets in regions where farmers may be liquidity constrained, policymakers should assess the magnitude of those constraints. If liquidity constraints are significant and farmers are relatively homogeneous in productivity, a quota system or a market supplemented with credit provision may deliver higher efficiency than a pure market. The standard presumption that markets outperform quotas can reverse when poor farmers cannot access credit to purchase water at the times they most need it.

Q: How does this paper relate to Che et al. (2013)? A: Che, Gale, and Kim (2013) assume agents consume at most one unit with linear utility and find that markets always dominate quotas, though some non-market mechanisms with resale outperform markets. Donna and Espín-Sánchez extend this framework by allowing multiple discrete units, a concave utility function, and intertemporal dynamics. Under these extensions, the efficiency ranking between markets and quotas is theoretically indeterminate, and the authors show empirically that quotas can dominate markets. Both papers agree that non-market mechanisms with resale outperform both markets and simple quotas.

Liquidity constraint (paper’s sense): A farmer is liquidity constrained when they lack sufficient cash to purchase water at the prevailing auction price, even if their valuation (marginal productivity of water) exceeds that price. In Mula, poor farmers without urban real estate income faced this constraint during the critical season when prices peaked, because they had already spent their harvest proceeds from the prior year and lacked access to credit markets.

Soil moisture (M_it): The state variable measuring water accumulated in a farmer’s plot, computed using the agricultural engineering evapotranspiration formula. Moisture increases with rainfall and irrigation purchases (each auction unit contributing 432,000 liters divided by plot area) and decreases via evapotranspiration. It is bounded below by the permanent wilting point (PW) — below which trees die — and above by field capacity (FC). Moisture creates intertemporal substitution in demand.

Critical season: The period corresponding to apricot fruit growth stages II and III and the Early Post-Harvest (EPH) period, spanning approximately weeks 18–32 (early May to early August). This is when the bulida apricot tree transforms water into fruit at the most rapid rate, when water demand peaks biologically, and when auction prices rise to their highest levels. It is the season during which liquidity constraints are binding.

Transformation rate (gamma): The parameter in the apricot production function that measures the rate at which excess soil moisture (above the permanent wilting point) converts into apricot output (measured in real pesetas) during the critical season. Estimated at gamma_L = 0.05 in the preferred specification (column 3). It is identified from cross-seasonal variation in purchasing patterns and cross-farmer variation in moisture levels.

Inefficiency due to decreasing marginal returns (DMR): One of two sources of allocation inefficiency identified in the paper. It arises when a farmer with already-high soil moisture receives water, yielding less additional output than if that water had gone to a farmer with lower moisture, given the concavity of the production function. Quotas avoid this inefficiency by allocating uniformly; markets with liquidity constraints exacerbate it by directing critical-season water to wealthy farmers who may have accumulated moisture from earlier purchases.

Cuarta (quarter): The unit of water sold at Mula auctions, representing the right to use water flowing through the main channel for three hours. At approximately 40 liters per second of flow, each cuarta carried approximately 432,000 liters of water. Water rights and land rights were held independently; farmers who participated in auctions owned only land, while waterlords separately owned canal usage rights.

Conditional choice probability (CCP) estimator: The two-step estimation procedure used to recover demand parameters from wealthy farmers’ purchasing choices. In Step 1, transition probability matrices for observable state variables (moisture, week, price, rainfall) are computed and CCP is estimated via multinomial logit. In Step 2, the value function is forward-simulated using these transition matrices and parameters are estimated by GMM, following Hotz et al. (1994).

The Impact of EITC on Education, Labour Market Trajectories, and Inequalities

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies the effect of the Earned Income Tax Credit (EITC) on educational attainment and labor market trajectories through two complementary approaches. Using policy discontinuities at U.S. state borders—exploiting variation in state EITC generosity set as a percentage of the federal EITC—the paper finds that an increase in the state EITC leads to a statistically significant increase in the high school dropout rate. The mechanism is that a tax credit targeted at low-wage (low-skilled) workers increases the value of low-skilled employment and reduces the relative return to schooling, generating a powerful disincentive to pursue long-term studies. A structural life-cycle matching model with directed search and endogenous educational choices, search intensities, hirings, hours worked, and separations is developed to quantify the long-run general equilibrium effects: in the long run, EITC reduces the proportion of high-skilled workers, with ambiguous effects on income inequality that depend on the competing channels through which EITC affects both the supply and demand sides of the labor market.

In depth

Q1. What is the empirical strategy for identifying the effect of EITC on education?

The paper identifies the causal effect of state EITC on education by exploiting policy discontinuities at U.S. state borders, comparing contiguous PUMA pairs on opposite sides of state borders that differ in state EITC generosity. State EITC rates are set as a percentage of the federal EITC and have varied considerably since the mid-1980s. Borrowing from the minimum wage literature (Dube et al., 2010; Hagedorn et al., 2015), the border-discontinuity design controls for local labor market conditions that vary continuously across state borders while isolating the effect of the discrete EITC policy difference.

Q2. What is the labor market mechanism linking EITC to education?

EITC raises the value of low-skilled employment by directly increasing the earnings of low-wage workers, which in turn reduces the relative return to investing in education, generating a powerful disincentive to pursue long-term studies. When directed search is present—as supported by recent empirical studies—educational decisions affect both job-finding probabilities and labor incomes over the life cycle. EITC’s subsidization of low-skilled work contracts the education premium in this framework, making the forgone earnings cost of staying in school larger relative to the low-skilled employment option supported by the EITC.

Q3. What does the life-cycle matching model contribute?

The structural life-cycle matching model with directed search and endogenous educational choices, search intensities, hirings, hours worked, and separations quantifies the general equilibrium and long-run effects of EITC that purely reduced-form studies cannot capture—including the feedback of an expanded low-skilled labor force on equilibrium wages and job creation. The model endogenizes labor demand, capturing both household responses (education, hours, search intensity) and firms’ responses (job creation and destruction). It is solved and estimated to replicate the life-cycle profile of labor market variables.

Q4. What are the long-run implications for inequality?

In the long run, EITC reduces the proportion of high-skilled workers in the economy, with ambiguous effects on income inequality because of offsetting channels: EITC directly increases earnings of low-skilled workers, but by expanding the supply of low-skilled labor it may also depress low-skilled wages; additional channels through unemployed workers’ search effort and employed workers’ hours further complicate the net effect. The model is used to determine the optimal design of the EITC that balances the income-support objective against these unintended long-run effects.

Key concepts

state EITC : a supplement to the federal Earned Income Tax Credit set as a fixed percentage of the federal credit; varies across states; used in this paper as the identification source for the effect of EITC generosity on education via border discontinuities. directed search : a labor market framework in which workers and firms direct their search to specific submarkets with posted wages; in this setting, educational choice affects both job-finding probabilities and wages over the life cycle, amplifying the disincentive effects of EITC on education relative to random-search models. education-EITC disincentive : the mechanism by which EITC targeted at low-wage workers raises the relative value of low-skilled employment and reduces the return to schooling, generating an increase in high school dropout rates as a side effect of the anti-poverty policy.

The Macroeconomics of Irreversibility

Mon, 01 Jan 0001 00:00:00 +0000

Overview

Research question. How does partial capital irreversibility — arising from a wedge between the purchase price and the resale (discounted) price of capital — shape the persistence and amplitude of aggregate capital fluctuations? And what is the quantitative magnitude of the capital price wedge that is needed to simultaneously reconcile micro-level investment behavior with macroeconomic propagation?

Methodology. Baley and Blanco build a continuous-time investment model for a continuum of firms facing (i) idiosyncratic productivity shocks (geometric Brownian motion), (ii) fixed capital adjustment costs proportional to productivity, and (iii) a capital price wedge ω, under which firms buy capital at price p and sell at p(1−ω). The key state variable is the log capital-productivity ratio k̂. The optimal policy takes the form of an inaction region with two distinct reset points — one for upsizing (k̂*₋) and one for downsizing (k̂*₊) — instead of the single reset point that arises without the wedge.

Their central innovation is the Cumulative Impulse Response (CIR): the cumulative deviation of average capital-productivity ratios following a small, permanent, unanticipated aggregate productivity shock. They show the CIR can be expressed analytically through three sufficient statistics derived entirely from the steady-state cross-sectional distribution of k̂ and capital age a: (i) Var[k̂], (ii) Cov[k̂, a], and (iii) an “irreversibility term” reflecting how idiosyncratic shocks change the anticipated direction of the next adjustment. Because idiosyncratic and aggregate shocks enter the law of motion symmetrically, steady-state moments encode the aggregate propagation.

To handle the path dependence introduced by the dual reset points, they condition all behavior on the previous reset (upsizing or downsizing) and characterize transitions across reset points via a Markov chain. They then derive explicit mappings from observable microdata — size and direction of investment adjustments, duration of inaction spells, and cross-spell transition probabilities — back to the unobservable capital-productivity distributions and sufficient statistics. These mappings require no revenue or productivity data; investment actions alone suffice.

They extend the baseline model to a generalized hazard framework (stochastic, asymmetric fixed costs), enabling the model to match the full empirical investment-rate distribution, and apply everything to annual establishment-level manufacturing data from Chile (Encuesta Nacional Industrial Anual, 1980–2011), restricting to plants observed for at least ten years with more than ten workers.

Main findings.

Price wedge estimate. A capital price wedge of ω = 0.12 (12%) is selected as the preferred value because it maximizes joint consistency between the model’s predicted CIR decomposition and the data, while also matching the distribution of investment rates. At ω = 0 the model generates a CIR of 0.92 and a negative covariance term, inconsistent with the data. At ω = 0.18 the aggregate CIR level (2.39) is close to data (2.33) but the decomposition diverges. At ω = 0.12, the CIR is 1.93 and the decomposition into sufficient statistics closely mirrors the data structure.
Irreversibility doubles persistence. In the analytically tractable case of zero drift and only a price wedge (no fixed costs), the CIR equals exactly twice the ratio Var[k̂]/σ², compared to the single fixed-cost case. This means irreversibility doubles the persistence of aggregate capital fluctuations for a given cross-sectional dispersion. More generally, under the calibrated model, a 1% decrease in aggregate productivity generates a nearly 2% cumulative deviation of average capital-productivity ratios from steady state. Without irreversibility, the CIR collapses to approximately 1.
Decomposition of the CIR. At ω = 0.12, the variance term Var[k̂]/σ² accounts for 72% of the CIR; the covariance term ν·Cov[k̂,a]/σ² accounts for 10%; and the irreversibility term accounts for 18%. The positive covariance (Cov[k̂,a] = 0.152 > 0) reflects that firms subject to downward rigidity accumulate older capital stocks above the economy’s average, amplifying persistence. This positive covariance arises because the price wedge’s downward-rigidity force dominates the drift’s negative effect.
Micro-level evidence. In the Chilean data, the inaction rate is 40%. More than 96% of adjustments are positive (upsizing), fewer than 4% are negative. The probability of upsizing after a previous upsize is P⁻⁻ = 0.958; the probability of downsizing after a downsize is P⁺⁺ = 0.124. A logistic regression yields an odds ratio of 3.3, meaning a firm is more than three times as likely to purchase capital following a prior purchase than following a prior sale. The average duration of inaction conditional on a prior purchase is E⁻[τ] = 1.72 years; conditional on a prior sale it is E⁺[τ] = 1.98 years. These patterns are qualitatively consistent with the serial correlation in adjustment sign predicted by the model.
Comparison with existing wedge estimates. The calibrated ω = 0.12 lies between micro-level studies based on liquidating firms (Ramey and Shapiro, 2001: ω ≈ 0.72; Kermani and Ma, 2023: ω ≈ 0.65) and structural models calibrated to static moments of investment distributions (Cooper and Haltiwanger, 2006; Khan and Thomas, 2013: ω = 0.025–0.07). The lower value relative to liquidation studies is attributed to selection effects (liquidating firms face fire-sale dynamics) and firm-internal capital reallocation that mitigates irreversibility for continuing firms.

Scope conditions. The analysis is a partial equilibrium characterization of transitional dynamics, maintaining constant interest rates and steady-state investment policies throughout the transition (a general equilibrium extension delivering constant prices as an equilibrium outcome is provided in Appendix D). Results apply to small, permanent, unanticipated aggregate productivity shocks; nonlinearities for shocks below 5% are found to be tiny. The empirical application is specific to Chilean manufacturing establishments, 1980–2011.

In depth

Q1. What is the economic mechanism by which capital irreversibility generates persistence in aggregate capital fluctuations?

Irreversibility creates two distinct reset points rather than one. When a negative aggregate productivity shock hits, it shifts more firms into the downsizing region. Downsizing firms, because they have been selling capital sequentially, maintain capital-productivity ratios persistently above the economy’s average and continue to do so for multiple periods. This increases the share of firms in a persistent “downsizing phase,” which prolongs the aggregate deviation from steady state. Two channels compound: first, the population tilts toward more downsizing firms; second, their mean deviations become larger and converge more slowly. Both channels increase the CIR. Crucially, without irreversibility, firms become identical after their first adjustment and there is no additional persistence beyond what fixed costs alone generate.

Q2. How are the three sufficient statistics derived, and what does each capture?

The CIR is characterized as a steady-state cross-sectional average of a recursive function m(k̂). Integrating over firms first and then time, and splitting each firm’s horizon at its first adjustment, yields three steady-state terms (Proposition 4). The first statistic, Var[k̂]/σ², measures how far firms allow their capital-productivity ratio to drift from the frictionless optimum — the “insensitivity of incomplete spells” to idiosyncratic productivity shocks. The second statistic, ν·Cov[k̂,a]/σ², is a bias-correction term that removes drift effects from the variance, ensuring only Brownian-shock sensitivity is captured. The third statistic, unique to the irreversibility case, measures how much idiosyncratic shocks alter the anticipated direction of the next adjustment — the “insensitivity of complete spells” — and equals the difference in expected cumulative deviations between departing and ending points of an inaction spell, scaled by duration.

Q3. Why is the CIR exactly twice as large under pure irreversibility (no fixed costs) as under pure fixed costs, for a given level of dispersion?

Proposition 5, case (ii) shows that with zero drift and only a price wedge, the CIR = 2 × Var[k̂]/σ², because the first and third sufficient statistics are identical and the covariance term is zero. In contrast, with only fixed costs (case (i)), the CIR = Var[k̂]/σ². The doubling arises because the price wedge generates history-dependence through the dual reset: after a firm adjusts, whether it upsized or downsized predicts its future adjustment direction. This “anticipated terminal condition” effect (captured by the third statistic) adds an equal contribution to the CIR as the pure inaction effect (the first statistic), doubling total persistence for the same cross-sectional dispersion.

Q4. How does the empirical strategy recover the capital price wedge?

The price wedge cannot be identified from the investment rate distribution alone: for any price wedge ω, the generalized hazard framework can find an adjustment hazard function Λ(k̂) such that the product Λ(k̂)·g(k̂) matches the observed investment density h(Δk̂). Instead, the authors use the CIR’s sufficient statistics — specifically the covariance term and the irreversibility term — as additional discriminating moments. At ω = 0, the model produces a negative covariance (inconsistent with the positive Cov[k̂,a] = 0.152 in the data) and no irreversibility term. At ω = 0.12, all three sufficient statistics simultaneously align with their data counterparts in relative importance (72%, 10%, 18%), selecting this wedge as preferred. The CIR level at ω = 0.12 is 1.93, somewhat below the data value of approximately 2.54–2.60, but the preferred criterion is mechanistic consistency, not just level matching.

Q5. What is the role of the Markov chain across reset points in handling path dependence?

Because optimal investment features serial correlation in the sign of adjustment (P⁻⁻ = 0.958 and P⁺⁺ = 0.124 in the data), firms’ future behavior depends on their most recent reset point. To maintain tractability, the authors condition all densities, durations, and expectations on the previous reset (upsizing g⁻(k̂) or downsizing g⁺(k̂)). The transition matrix P encoding probabilities P⁻⁻, P⁻⁺, P⁺⁻, P⁺⁺ determines the steady-state shares of upsizing and downsizing firms (as the eigenvector of P) and the renewal weights r⁻ and r⁺ that rescale conditional densities to account for observational bias (firms with longer inaction spells contribute more to the cross-section). This Markov structure is sufficient because one adjustment erases all heterogeneity except the direction of adjustment.

Q6. What do the microdata mappings recover, and how are the reset points identified?

Stage I mappings (Propositions 6–9) recover: drift ν = E[Δk̂]/E[τ]; volatility σ² from cross-spell moment E[(k̂τ’ + ντ’)² − (k̂*)²]/E[τ]; conditional means E±[k̂] as midpoints of inaction spells weighted by relative adjustment size; Var[k̂] from differences in cubed stopped values; Cov[k̂,a] from variance, average age, and the dynamic covariance E[(k̂τ’ − E[k̂])²τ’]/E[τ]; and the irreversibility term from differences in expected deviations at departing vs. ending reset points. Stage II (Proposition 10) recovers the two reset points k̂*₋ and k̂*₊ from optimality conditions that equalize the investment price to the expected discounted marginal product of capital during inaction plus the expected value of undepreciated capital, conditioning on the prior reset. The inner inaction region width k̂*₊ − k̂*₋ = 0.813 in the Chilean data, of which 45% is attributed to the exogenous price wedge and 55% to the endogenous response to the wedge.

Q7. How does the sign of Cov[k̂,a] depend on the price wedge vs. the drift?

With zero price wedge and negative drift ν < 0 (depreciation exceeding productivity growth), firms with older capital have capital-productivity ratios below average, yielding Cov[k̂,a] < 0. The drift makes old capital-productivity ratios negative. Introducing a price wedge creates downward rigidity: unproductive firms delay selling, so old firms accumulate capital-productivity ratios above average, pushing Cov[k̂,a] toward positive values. The covariance turns positive once ω > 0.08 (in the illustrative parametrization in Figure V). In the Chilean calibration at ω = 0.12, Cov[k̂,a] = 0.152 > 0, confirming that the price wedge’s effect dominates the drift’s negative effect. A positive covariance amplifies the CIR (through the second sufficient statistic with ν > 0).

Q8. What is the generalized hazard extension and why is it needed?

The baseline model with a single fixed cost θ generates an investment distribution concentrated at two mass points (purchases and sales of fixed size), which does not match the empirical distribution’s coexistence of large and small investment rates and its convex shape. The generalized hazard model replaces the deterministic fixed cost with a stochastic, state-dependent adjustment cost, parameterized by a hazard function Λ(k̂) giving the probability of adjusting per unit time at any capital-productivity ratio in the outer inaction region. This function is recovered non-parametrically from the data by fitting a Gamma distribution to the investment density and inverting the Kolmogorov Forward Equation. The generalized hazard model nests the baseline model, random fixed cost models (Thomas 2002, Khan and Thomas 2008), and asymmetric adjustment models, while preserving the sufficient statistics characterization.

Q9. How does the model handle the “problem with reinjection” that arises from path dependence after the first adjustment?

Without irreversibility, a firm’s initial state k̂₀ does not affect behavior after the first adjustment, because there is a unique reset point; subsequent behavior is independent of the aggregate shock magnitude. With irreversibility, firms only partially absorb the aggregate shock at the first adjustment, since the initial state affects the probability of subsequently upsizing or downsizing. In principle, one must track firms through infinitely many adjustments. The paper’s resolution (Proposition 2) is to note that the first adjustment erases all heterogeneity except the direction (upsizing vs. downsizing), allowing subsequent behavior to be summarized by just two numbers m(k̂*₋) and m(k̂*₊), combined with the transition probabilities P⁻(k̂₀) and P⁺(k̂₀). This yields a recursive formulation for m(k̂) governed by an HJB equation with two boundary conditions at the reset points, making the problem tractable.

Q10. What is the role of the stationarity condition in pinning down the CIR?

The HJB for m(k̂) has infinitely many solutions (m(k̂) + a for any constant a). The stationarity condition, requiring that the cross-sectional average of m(k̂) in steady state is zero (no fluctuations without shocks), pins down the unique solution. Economically, it says that average cumulative deviations from complete upsizing spells and complete downsizing spells must exactly balance the deviations from incomplete inaction spells. For upsizing firms, deviations are negative (they hold too little capital relative to average); for downsizing firms, deviations are positive (they hold too much capital). The stationarity condition imposes a linear relationship between m(k̂*₋) and m(k̂*₊) that together with the HJB uniquely determines the solution.

Q11. How are the results extended to assess nonlinearities and robustness?

Appendix G studies nonlinearities numerically in the generalized hazard model for different signs and magnitudes of the aggregate productivity shock. The authors find tiny nonlinearities and asymmetries for productivity shocks below ε = 5%, validating the first-order approximation used throughout. Appendix E.7 provides comparative statics on the output-capital elasticity α. The model is estimated with an inaction threshold of ι = 0.01 (investment rates below 1% in absolute value are treated as inaction), consistent with Cooper and Haltiwanger (2006). The investment distribution is truncated at the 2nd and 98th percentiles to remove outliers.

Q12. What broader applicability do the authors claim for the CIR sufficient statistics framework?

The authors argue the framework applies wherever path-dependent lumpy adjustments occur, including: inventory management (with two types of ordering decisions), durable goods consumption, and labor markets with sticky wages. The key requirement is the existence of a finite number of reset points and sufficient microdata to discipline the transition probabilities across them. Future extensions noted in the paper include: analysis of other aggregate shocks (profitability, capital prices, interest rates); corporate tax reform; monetary policy interacting with investment frictions; time-varying and endogenous price wedges in secondary markets; and higher-order cross-sectional moment responses (variance, skewness of capital-productivity ratios) by choosing different functions f(k̂) for the generalized CIR.

Key Concepts

Capital price wedge (ω). The fractional discount between the purchase price of capital p and its resale price p(1−ω). In the model this creates two distinct reset points for investment (one for buying at price p, one for selling at the discounted price) and represents the core source of irreversibility. It reflects asset specificity, adverse selection, intermediary fees, and obsolescence. The preferred calibrated value for Chilean manufacturing is ω = 0.12.

Cumulative Impulse Response (CIR). The integral over all future dates of the impulse response function of the average capital-productivity ratio following a small, permanent, unanticipated aggregate productivity shock. It summarizes both the impact and persistence of aggregate capital fluctuations in a single scalar. Without investment frictions, the CIR is zero (firms adjust instantaneously); the calibrated CIR at ω = 0.12 is 1.93, meaning a 1% aggregate shock generates a 1.93% cumulative deviation.

Dual reset points (k̂₋ and k̂₊).** The two levels to which firms reset their capital-productivity ratio upon adjustment: k̂*₋ after a capital purchase (upsizing) and k̂*₊ after a capital sale (downsizing). With a price wedge, k̂*₊ > k̂*₋, creating an “inner inaction region” [k̂*₋, k̂*₊] with path-dependent behavior. The inner inaction region width is 0.813 in the Chilean data.

Sufficient statistics for the CIR. Three steady-state cross-sectional moments that together fully characterize the CIR up to first order: (i) Var[k̂]/σ², the scaled cross-sectional variance of capital-productivity ratios (captures insensitivity of incomplete spells to idiosyncratic shocks); (ii) ν·Cov[k̂,a]/σ², the scaled covariance of capital-productivity ratios with capital age (a drift-bias correction); (iii) the “irreversibility term” measuring how idiosyncratic shocks change the anticipated direction of the next adjustment (unique to the irreversibility case, zero without a price wedge).

Serial correlation in adjustment sign. The property, implied by the dual-reset structure, that a firm is more likely to purchase capital following a prior purchase and more likely to sell following a prior sale. In the Chilean data, P⁻⁻ = 0.958 (probability of upsizing after a prior upsize) vs. P⁺⁺ = 0.124 (probability of downsizing after a prior downside), and a logistic regression yields an odds ratio of 3.3.

Generalized hazard function Λ(k̂). A state-dependent adjustment probability per unit time, allowing for stochastic and asymmetric fixed costs, that generates the full empirical investment rate distribution. It replaces the single deterministic fixed cost of the baseline model. The hazard function is recovered non-parametrically from microdata by fitting a Gamma distribution to the investment density and inverting the Kolmogorov Forward Equation, conditional on the price wedge.

Renewal weights (r⁻, r⁺). Weights used to construct the unconditional density of capital-productivity ratios from the two conditional densities (conditional on prior purchase g⁻(k̂) and prior sale g⁺(k̂)). They rescale adjustment shares by relative average duration, correcting for the observational bias that firms with longer inaction spells are over-represented in the cross-section: r± = (N±/N) × (E±[τ]/E[τ]).

Endogenous irreversibility. The component of the inner inaction region width (k̂*₊ − k̂*₋) that arises not from the exogenous price wedge directly but from firms’ endogenous responses to the wedge — specifically, the differences in expected marginal products and user costs across the two types of inaction spells. At ω = 0.12, 45% of the inner inaction region is attributed to the exogenous wedge and 55% to endogenous amplification.

The Micro and Macro Dynamics of Capital Flows

Mon, 01 Jan 0001 00:00:00 +0000

Using the 2001 Hungarian capital account liberalization as a quasi-natural experiment and census-level firm data covering the entire economy (1992–2008), the paper identifies two channels through which capital inflows affect resource allocation: an input-cost channel (lower cost of capital benefits capital-intensive sectors) and a consumption channel (higher household incomes benefit high-expenditure-elasticity sectors, chiefly services). The paper finds the consumption channel dominates: one standard deviation increase in expenditure elasticity is associated with 8.4% greater real value-added growth, versus 4.2% for one standard deviation in capital elasticity. Along the extensive margin, high-expenditure-elasticity sectors experience 15% higher net entry and 19% higher gross entry. A calibrated multi-sector heterogeneous-firm model with non-homothetic preferences (à la Comin–Lashkari–Mestieri 2021) replicates 12 non-targeted moments and reproduces 70% of the reallocation toward services observed in Hungary. Counterfactual exercises show that a neoclassical homothetic model underpredicts reallocation by a factor of ten and generates counterfactual real exchange rate depreciation. Despite reallocation toward less productive service firms (a negative composition effect), aggregate TFP increased 11.4% in Hungary — driven by a love-of-variety effect from entry (mass-of-firms effect of +3.5% versus composition effect of −1.9%). Non-homothetic preferences amplify this mechanism: capital-scarce economies experience 21.9% larger TFP gains than homothetic models predict.

In depth

Q1. Why is Hungary’s 2001 capital account liberalization a clean quasi-natural experiment?

Hungary deregulated only cross-border financial flows, without simultaneous trade or FDI liberalization, and the reform was predetermined by the Copenhagen Criteria of 1993 as a condition for EU accession. The content and timing of the reform were not driven by Hungarian firm-level fundamentals: by March 2001, financial liberalization was the sole remaining EU accession requirement, and neither trade nor FDI changed around the reform (Figures C.4–C.5). Exports to the EU already accounted for 80% of total exports before 2001. The nine other EU accession candidates at the time did not experience comparable patterns of capital inflows, consumption booms, or sectoral reallocation (Tables C.2–C.3), ruling out EU accession itself as the driver.

Q2. How does the paper identify the input-cost and consumption channels separately?

The identification strategy exploits three sources of variation: pre- versus post-reform timing, heterogeneous capital elasticities across four-digit industries (input-cost channel), and heterogeneous expenditure elasticities across two-digit industries (consumption channel), derived from model-implied structural relationships. Using equation (4), the DiD regression estimates γ₁ (capital elasticity × reform dummy) and γ₂ (expenditure elasticity × reform dummy). These two structural parameters are nearly orthogonal (correlation 2.1% between USDA capital and expenditure elasticities), allowing separate identification. The capital elasticities are estimated using the Petrin–Levinsohn–Wooldridge method on pre-reform data; expenditure elasticities come from USDA Seale–Regmi–Bernstein (2003) estimated for Hungary in 1996. Parallel trends hold: firms across elasticity levels shared similar pre-reform growth trajectories (Table C.9).

Q3. What do the baseline regression results show about which channel dominates?

In the preferred specification with both channels and all controls (column 4, Panel A of Table 1), capital elasticity raises value added by 4.2% per standard deviation (0.045 SD), while expenditure elasticity raises it by 8.4% per standard deviation (0.223 SD USDA); standardized beta coefficients confirm the consumption channel is larger. For capital accumulation (Panel B), only the capital elasticity coefficient is significant: a one standard deviation increase in capital elasticity is associated with 4.4% more firm-level capital, while expenditure elasticity has no significant effect — firms in high-expenditure-elasticity sectors do not accumulate more capital, they hire more workers. Employment (Panel C) shows 9.3% higher employment per standard deviation in expenditure elasticity (5.9% using Bils–Klenow–Malin elasticities). These patterns survive controls for non-tradability, financial frictions (Rajan–Zingales, Raddatz inventories-to-sales, cash conversion cycle), and firm-level debt obligations.

Q4. How does the model fit the non-targeted moments for Hungary?

Calibrated to 13 internally targeted moments (including the 3.5 percentage point decline in the domestic real interest rate and sectoral firm-size distributions), the model matches 12 non-targeted moments spanning consumption, capital accumulation, cross-sector reallocation, and within-sector selection (Table 6). Key matches: household consumption +5.8% (data), +7.2% (model); within-firm capital accumulation +22.5% vs +24.9%; value-added share of services +3.9pp vs +2.7pp (70% match); relative operational cutoff of services vs manufacturing −2.3% vs −1.7% (74% match); relative export cutoff +4.6% vs +4.5% (98% match). The model accounts for roughly 60% of the 2.9% relative price appreciation (real exchange rate). The model also reproduces the differential increase in entry rates: services +10.8pp (data) vs +18.4pp (model), manufacturing +5.7pp vs +8.6pp.

Q5. What do counterfactual exercises reveal about the role of non-homothetic preferences?

A neoclassical representative-firm model with homothetic preferences generates only 0.4 percentage points of reallocation toward services — ten times less than the 3.9pp observed in Hungary — and produces a counterfactual real exchange rate depreciation. In Table 7, four counterfactuals are compared: (1) baseline model (εS ≠ εM, αS ≠ αM): consumption ratio CS/CM +6.9pp, service value-added share +2.7pp, relative price appreciation +1.7%; (2) consumption channel only (εS ≠ εM, αS = αM): similar service reallocation but no RER appreciation; (3) input-cost channel only (εS = εM, αS ≠ αM): modest reallocation (~1.1pp) but correct RER appreciation; (4) homothetic heterogeneous-firm model (εS = εM, αS = αM): ~0.7pp reallocation, wrong RER; (5) neoclassical model: ~0.4pp, wrong RER. Non-homothetic preferences account for about two-thirds of the service reallocation; differential capital elasticities are necessary to replicate exchange rate dynamics.

Q6. How can aggregate TFP increase when resources move toward less productive services?

Financial liberalization induces firm entry — especially in high-expenditure-elasticity services — generating a love-of-variety effect that increases aggregate output more than proportionally with the number of varieties (since σ > 1), overwhelming the negative composition effect from reallocation to lower-productivity service firms. The TFP decomposition (Table 9) shows: composition effect −1.9%, mass-of-firms effect +3.5%, interaction +0.7%, sum +2.3% model (data: +11.4%). The composition effect is consistently negative across all capital-scarcity levels because service firms are less productive. But the mass-of-firms effect is consistently larger and positive. Non-homothetic preferences amplify entry in services (the high-expenditure-elasticity sector), strengthening the love-of-variety channel.

Q7. How do non-homothetic preferences affect TFP gains in capital-scarce economies, and what are the policy implications?

Capital-scarce economies experience larger consumption booms upon financial liberalization (given lower initial capital levels and higher intertemporal borrowing gains), inducing stronger entry in high-expenditure-elasticity services and larger mass-of-firms TFP effects; non-homothetic preferences amplify this gradient by 21.9% relative to homothetic preferences (Table 10). Specifically, an economy liberalizing at 25% of its open-economy steady-state capital stock gains 5.5× more TFP than one liberalizing at 70%; under homothetic preferences the ratio is 4.5×, yielding a 21.9% amplification from non-homotheticity. This helps explain the empirical puzzle documented by Bekaert–Harvey–Lundblad (2011) and Bonfiglioli (2008) that financial liberalization episodes associate with productivity gains in capital-scarce economies, which neoclassical models predict incorrectly as productivity declines. The policy implication is that the gains from financial openness are largest — and most driven by consumption-driven entry — when economies are capital-scarce, but these gains also carry macro-financial risks (as in Gyongyosi–Rariga–Verner 2023 on the 2008 Hungarian forint depreciation).

Key concepts

input-cost channel : the mechanism through which capital inflows reduce firms’ cost of capital (borrowing rate), benefiting sectors with higher capital elasticity; identified in Hungary through the differential expansion of firms in high-capital-elasticity industries after the 2001 deregulation.

consumption channel : the mechanism through which capital inflows increase household consumption, benefiting sectors with higher expenditure elasticity; found to dominate the input-cost channel in Hungary, explaining the reallocation toward services.

non-homothetic preferences : demand preferences (modeled following Comin–Lashkari–Mestieri 2021) in which sectoral expenditure shares change with income levels — goods with expenditure elasticity above one gain share as income rises; these preferences are quantitatively necessary to explain the 3.9pp reallocation toward services in Hungary (versus 0.4pp under homothetic preferences).

mass-of-firms effect : the aggregate productivity gain from an increase in the number of active firm varieties under CES demand (σ > 1), whereby output grows more than proportionally with the number of varieties; this love-of-variety mechanism explains why aggregate TFP increases in Hungary despite resource reallocation toward less productive service firms.

expenditure elasticity : the sector-level responsiveness of consumption to a proportional increase in aggregate income; used in the paper’s DiD identification to separate the consumption channel from the input-cost channel, measured using USDA (Seale–Regmi–Bernstein 2003) estimates for Hungary, with services having higher elasticity (1.18 in model calibration) than manufacturing (0.75).

The Origins and Control of Forest Fires in the Tropics

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies the economics of illegal tropical forest fires in Indonesia, framed as a modern counterpart to Pigou’s canonical externality example of sparks from railway engines. The central research question is whether private firms adjust their fire-setting behavior depending on the degree to which the costs of fire spread fall on themselves versus others, and what enforcement architecture shapes that adjustment.

The empirical setting is Indonesia’s national forest estate, where palm oil and wood fiber concession holders use fire as a cheap land-clearance method — burning primary forest costs 44–70% less than mechanical clearance — despite the practice being illegal. The paper assembles a novel dataset of 107,334 fires across Indonesia’s major forested islands from October 2000 to January 2016, constructed from NASA MODIS daily satellite hotspot data (1 km resolution, four flyovers per day). Fire ignitions and spread paths are traced by linking contiguous pixels burning on adjacent days. This fire data is merged with geocoded concession boundaries (logging, palm oil, wood fiber), land-use classifications (protected forest, unleased productive forest, areas outside the forest estate), annual deforestation data from Hansen et al. (2013) at 30 m resolution, daily wind speed data from NOAA NCEP-DOE Reanalysis 2 interpolated to each 1 km pixel, and data on firms investigated by the Indonesian government following the 2015 fires. The main analytical sample focuses on the 39,077 fires started inside wood fiber and palm oil concessions.

The paper’s identification strategy exploits two intersecting sources of variation: (1) temporal and spatial variation in monthly wind speed, which predicts the probability and extent of fire spread — a one-standard-deviation increase in wind speed (approximately 5 km/hr) increases fire spread area by 287%; and (2) cross-sectional variation in the land-type composition of the area surrounding each ignition pixel, which determines whether spread costs would fall on the fire-setter or on others. The interaction of these two factors identifies whether firms are more cautious about igniting fires on windy days when surrounding land is their own versus when it belongs to others.

Three main findings emerge. First, fires are systematically human-caused and linked to industrial land clearance. Fires are eight times more likely per hectare in oil palm and wood fiber concessions than in logging concessions. Completely deforesting a 1 km pixel increases the probability of fire ignition in that pixel in the subsequent year by 279%, and this effect reverses in the year after (two years post-deforestation), ruling out natural flammability as the explanation and confirming a deliberate slash-and-burn cycle. Fire use following deforestation falls by approximately 38% in oil palm concessions during district election years, consistent with tighter enforcement when political incentives favor suppression.

Second, firms partially internalize the externalities from fire-setting. They are significantly less likely to set fires on windy days when surrounding pixels belong to their own concession rather than to others. A buffer zone entirely owned by the same concession holder reduces ignitions by 8–25% at mean wind speed, and by 22–61% at the 95th-percentile wind speed. However, firms treat neighboring concession land and unleased productive forest similarly — suggesting Coasian bargaining between concession holders is not occurring.

Third, the government’s enforcement pattern shapes firm behavior. Using data on firms investigated after the 2015 fires, the paper shows the government disproportionately investigates firms whose fires burned protected areas or high-population-density land, but not those whose fires damaged other private concessions. The relative weights firms place on different land types when deciding whether to ignite fires align closely with this government punishment function, consistent with firms responding to implicit Pigouvian incentives.

Counterfactual simulations show that broadening enforcement to treat all land types as the government currently treats populated areas would reduce fires by 80%; treating all land like protected forest would reduce fires by 67%. By contrast, fully Coasian property-rights solutions yield only 14% reductions, and tort reform allowing concession holders to recover damages from neighbors yields only 6%.

Q: What is the core externality problem studied in this paper? A: Firms use fire as a cheap land-clearance method, but once set, fires risk spreading beyond the igniter’s own concession onto land owned by others, creating an uncompensated externality. The decision to use fire rather than mechanical clearance is de facto a decision to impose this spread risk on third parties. The paper asks whether firms adjust this decision depending on the extent to which spread costs fall on themselves versus others, and whether government enforcement shapes that adjustment.

Q: Why is Indonesia the empirical setting? A: Indonesia holds a large share of the world’s tropical forests and is among the countries most affected by illegal land-clearing fires. The 2015 Indonesian fires alone released approximately 400 megatons of CO2 equivalent, at their peak emitting more daily greenhouse gases than all US economic activity, and caused an estimated 100,000 excess deaths across Indonesia, Malaysia, and Singapore. The palm oil industry in Indonesia and Malaysia, where fire is used extensively, accounted for 4.7% of global CO2 emissions from 1986 to 2016.

Q: How are fire ignitions and spread identified in the data? A: The paper starts from NASA MODIS daily hotspot data at 1 km resolution from October 2000 to January 2016. An iterative procedure assigns contiguous pixels burning on adjacent days to the same fire event, with a 1-pixel buffer allowing for spread detection. This yields 176,855 total fires across Indonesia, of which 107,334 remain after restricting to the major forested islands and the forest estate. The procedure may understate single-day spread since pixels burning on the same day are classified as part of the ignition area rather than spread.

Q: What fraction of fires spread beyond their ignition area, and how much of the spread falls on outsiders? A: 87% of fires burn for only one day and 89% do not spread beyond their initial ignition area. However, the largest fire in the data spread to cover 466 times its initial area, and the largest single fire burned 764 km2. Across all multi-day fires started inside concessions, 32% of the total land burned outside the initial ignition area is outside the concession where the fire began, quantifying the scale of the local externality.

Q: How is wind speed used as an identification strategy? A: Wind speed provides temporal and spatial variation in the probability that a fire will spread. A one-standard-deviation increase in wind speed (approximately 5 km/hr) increases the extent of fire spread by 287%. Because wind varies month to month and across space, while the composition of surrounding land types is fixed in the cross-section, the interaction of wind speed with surrounding land type identifies whether firms are more cautious about igniting fires when spread risk is high and spread costs would fall on their own land versus others’ land.

Q: What is the main result on firms’ internalization of fire spread externalities? A: Firms are significantly less likely to start fires on windy days when a larger share of the surrounding buffer zone belongs to their own concession. One additional buffer pixel in one’s own land decreases ignitions by 0.2–0.7%. A buffer zone entirely owned by the same concession holder reduces ignitions by 8–25% at mean wind speed, and by 22–61% at the 95th-percentile wind speed. This demonstrates that firms take fire spread risk into account when it threatens their own assets, but discount it when spread would damage others’ land.

Q: Do firms treat different types of neighboring land differently? A: Yes. The benchmark category is unleased productive forest, which has the weakest property rights and receives the least de facto government protection. Relative to this benchmark, firms are more cautious about fire spread toward protected forest (national parks and watershed areas) and toward land outside the forest estate (typically villages and smallholders). One additional buffer pixel in protected forest versus unleased productive forest decreases ignitions by 0.9% at mean wind speed and 2.7% at the 95th-percentile wind speed; the deterrent for land outside the forest estate is even stronger at 1.6% and 4.6%, respectively. Firms treat other firms’ concession land similarly to unleased productive forest, suggesting no effective private enforcement between concession holders.

Q: What evidence shows fires are tied to intentional land clearance rather than natural ignition? A: Fires are eight times more likely per hectare in oil palm and wood fiber concessions than in logging concessions, consistent with clear-cutting versus selective logging. Completely deforesting a 1 km pixel increases fire probability in that pixel in the subsequent year by 279%. Crucially, the effect reverses in the second year after deforestation — the pixel becomes less likely to burn than before — which rules out natural flammability as the mechanism and confirms deliberate slash-and-burn timing.

Q: What does the electoral cycle evidence show about government enforcement? A: Fires following deforestation fall by approximately 38% in oil palm concessions during district election years relative to the year prior to an election, and bounce back to pre-election levels in the year after. The decline is confined to productive forest zones where conversion is occurring; no electoral cycle appears in protected areas where conversion is already prohibited. This indicates that enforcement is tightened when political incentives are strong, and confirms that these fires are set intentionally and are responsive to government pressure.

Q: How is the government’s de facto punishment function estimated? A: The paper uses data on firms investigated by the Indonesian Ministry of Forestry following the 2015 fires, matching investigated firms (identified only by initials in the published list) to concession-holder names. A logistic regression of investigation probability on the land-type outcomes of a firm’s fires — conditional on total area burned — shows the government is substantially more likely to investigate firms whose fires burned protected areas or high-population-density land, but does not differentially investigate cases where fire damage is largely confined to other private concessions.

Q: How closely do firm behavior and government enforcement weights align? A: The relative weights across land types that the government applies in its investigation decisions correspond closely to the relative weights firms apply when deciding whether to ignite fires on windy days. Firms are most deterred by spread risk toward protected forest and populated areas outside the forest estate — the same categories the government prioritizes. Firms are least deterred by spread toward unleased productive forest and other private concessions — the categories the government largely ignores. This alignment is consistent with firms responding to Pigouvian-style implicit incentives generated by the government’s enforcement pattern.

Q: What do the counterfactuals reveal about policy effectiveness? A: Fully Coasian property-rights reform — where firms treat all surrounding land as their own — would reduce fires by only 14%. Tort reform enabling concession holders to recover damages from neighbors (treating neighboring concessions as own land) would reduce fires by only 6%. By contrast, uniform enforcement raising deterrence to the level currently applied to populated areas would reduce fires by 80%; applying the level currently applied to protected forest would reduce fires by 67%. An enforcement regime that perfectly prevented all fire spread outside the igniting concession would reduce area burned by only 23%; preventing spread into protected and populated areas alone would yield only a 2% reduction.

Q: What do the benefit-cost ratios for fires look like? A: The estimated external damages from the 1997/1998 Indonesian fires range from 1,286 to 6,074 USD per hectare burned (2020 USD). The average private benefit from using fire rather than mechanical clearance — accounting for fertilizers and other costs — averages approximately 52 USD per hectare (2020 USD). Benefit-cost ratios of 0.008 to 0.04 lie well below 1, indicating that the social damages from fires vastly exceed the private benefits, even though the government currently deters only the most costly categories of fire.

Q: Why do Coasian private solutions perform poorly in this setting? A: Coasian bargaining between concession holders would require them to reach agreements to bring fire use to a locally efficient level without government intervention. The evidence shows firms treat other concession holders’ land essentially the same as unprotected unleased productive forest, implying that no such bargains are being struck. The counterfactual analysis confirms this: even a fully-Coasian outcome where every surrounding pixel is treated as own land would reduce fires by only 14%, because the bulk of fires occur when ignition costs to the firm’s own land are low regardless of wind speed.

Q: What is the primary policy implication? A: The most effective lever for reducing fires is not preventing spread after the fact, but rather deterring ignition in the first place by extending the enforcement regime uniformly across all land types. If firms were induced to treat all surrounding land with the same caution they currently apply toward populated areas — through broader and stronger penalties — fires would fall by 80%. This is substantially more effective than property-rights reforms, tort reforms, or targeted spread-prevention measures focused only on protected and populated areas.

Externality (fire spread): In this paper’s usage, the cost imposed on third parties when a fire ignited inside one concession spreads to land owned by others. The externality is quantified as the share of area burned outside the igniting concession (32% of multi-day fire spread in the data) and the ratio of external damages (1,286–6,074 USD/ha) to private benefits (52 USD/ha) from using fire rather than mechanical clearance.

Slash-and-burn (industrial scale): The two-stage land-clearance practice where valuable timber is first harvested (deforestation) and the remaining vegetation is then burned to prepare land for plantation crops. The paper establishes this cycle empirically: complete deforestation of a 1 km pixel increases fire ignitions by 279% in the following year, with the effect reversing in the second year, ruling out natural flammability.

Pigouvian enforcement: Government-imposed penalties that alter private incentives to account for externalities. In this paper’s usage, the government’s de facto punishment function — which heavily weights fires spreading into protected areas and populated land — functions as an implicit Pigouvian tax, shaping which fires firms choose to avoid rather than uniformly deterring all illegal burning.

Coasian bargaining failure: The absence of private negotiations between concession holders to internalize the externalities they impose on each other. The paper demonstrates this failure empirically by showing firms treat neighboring concession land no differently from unprotected unleased productive forest, indicating no effective private agreements are limiting cross-concession fire spread.

Wind speed as spread risk shifter: Monthly average wind speed at each 1 km pixel, used as the time-varying component of fire spread risk. A one-standard-deviation increase (approximately 5 km/hr) increases fire spread area by 287%. The paper uses wind speed variation interacted with surrounding land type composition to identify whether firms adjust ignition decisions based on spread risk and who bears the cost.

Unleased productive forest (benchmark): Land within the national forest estate that is neither in a designated concession nor in a protected zone, leaving ownership rights unclear and de facto unprotected. The paper uses firms’ behavior toward this category as the baseline against which sensitivity to other land types is measured, because it attracts the least government attention and the weakest property rights.

Government punishment function: The implicit weights the Indonesian government places on different types of fire damage when deciding whether to investigate a firm, estimated from logistic regression on the 2015 investigation data. The function heavily weights fires burning protected areas and high-population-density land, and places near-zero weight on damage to other private concessions, shaping which fire types firms strategically avoid.

The Surrogate Index: Combining Short-Term Proxies to Estimate Long-Term Treatment Effects More Rapidly and Precisely

Mon, 01 Jan 0001 00:00:00 +0000

This paper addresses a fundamental challenge in program evaluation: primary outcomes of interest — such as lifetime earnings or long-term employment — are often observed only with lengthy delays, forcing researchers to rely on short-term outcomes when making timely policy decisions. The authors develop a formal framework for combining multiple short-term proxy outcomes (surrogates) into a single “surrogate index” that, under stated assumptions, identifies the average treatment effect on the long-run primary outcome.

The methodological contribution rests on three key assumptions. First, Unconfoundedness: treatment assignment in the experimental sample is ignorable conditional on pre-treatment variables. Second, Surrogacy (Prentice 1989): the long-term primary outcome is independent of the treatment conditional on the surrogates — formally, Wi ⊥⊥ Yi | Si, Xi, Pi=E — meaning the entire causal path from treatment to primary outcome runs through the surrogates. Third, Comparability: the conditional distribution of the primary outcome given surrogates and pre-treatment variables is identical across the experimental and observational samples. This last assumption is novel relative to the prior surrogacy literature, which implicitly relied on it without formal statement.

The paper operates with two distinct samples. The experimental sample contains treatment assignment and surrogate outcomes but not the long-term primary outcome. The observational sample contains surrogates and primary outcomes but not treatment assignment. The surrogate index is defined as the conditional expectation of the primary outcome given surrogates and pre-treatment variables estimated in the observational sample, µ(s,x,O) = E[Yi|Si=s, Xi=x, Pi=O]. Under all three assumptions, the average treatment effect on this index equals the average treatment effect on the primary outcome. Under a linear specification, the estimator reduces to multiplying the vector of treatment effects on surrogates (from the experimental sample) by the regression coefficients predicting the primary outcome from surrogates (from the observational sample).

The paper derives semiparametric efficiency bounds, demonstrating that exploiting the surrogacy assumption — by replacing actual outcomes Yi with the predicted surrogate index µ(Si,Xi,O) — yields strictly lower variance than a standard randomized experiment that directly observes the primary outcome. The precision gain equals the variance of the residual Yi − µ(Si,Xi,O).

The authors also characterize bias when Surrogacy or Comparability fail. Crucially, even without these assumptions, the estimators consistently estimate a well-defined causal quantity — the average treatment effect on the surrogate index — providing a principled aggregation of intermediate outcomes. Formal bounds on the extent of bias are derived; without bounded outcomes, these bounds are uninformative, but with binary outcomes or bounded violations, sharp intervals are available.

The empirical application uses the Greater Avenues to Independence (GAIN) job training program, a randomized trial in California. The experimental sample is Riverside (NE,T = 4,405 treated, NE,C = 1,040 control), with 36 quarters of post-assignment outcomes. The observational sample pools three other counties (Alameda, Los Angeles, San Diego; NO = 13,725). Long-run benchmarks are a 6.4 percentage point (s.e. 1.2 pp) increase in mean quarterly employment rates and a $249 (s.e. $83) increase in mean quarterly earnings, each averaged over 36 quarters. All three surrogate-based estimators (surrogate index, surrogate score, influence function) fall within two standard errors of these benchmarks when surrogates include as few as 5 quarters of employment, earnings, and aid outcomes. By 6 quarters, the surrogate index estimate for employment is 0.061 (s.e. 0.006) versus the 0.064 benchmark. The “naive” estimator — which simply uses the treatment effect on short-run outcomes directly — requires more than 25 quarters before falling within two standard errors of the benchmark. The surrogate index achieves a 35% reduction in standard errors relative to directly waiting to observe the 9-year outcome.

Q: What is the surrogate index, precisely? A: The surrogate index is the conditional expectation of the primary outcome given surrogate outcomes and pre-treatment variables, estimated in the observational sample: µ(s,x,O) = E[Yi | Si=s, Xi=x, Pi=O]. It aggregates multiple short-term proxy variables into a scalar index through their predicted value for the long-run outcome. Under the Prentice Surrogacy assumption, the average treatment effect on this index equals the treatment effect on the primary outcome.

Q: What is the Prentice Surrogacy assumption, and why is it demanding? A: Surrogacy requires Wi ⊥⊥ Yi | Si, Xi, Pi=E — the long-run outcome is independent of the treatment conditional on the surrogates and pre-treatment variables. This means the surrogates must fully capture all causal pathways from treatment to outcome; any direct effect of the treatment on the primary outcome that does not pass through the measured surrogates violates the assumption. The authors note this is not testable in the two-sample setup because Yi and Wi are never jointly observed.

Q: What is the Comparability assumption, and why is it novel? A: Comparability requires Pi ⊥⊥ Yi | Si, Xi — the distribution of primary outcomes given surrogates and pre-treatment variables is identical across the experimental and observational samples. It formalizes the implicit condition under which the observational sample can be used to estimate the surrogate-to-outcome relationship that is then applied to the experimental sample. The authors state this assumption was not previously articulated in the surrogacy literature despite being implicitly relied upon.

Q: How does the paper handle violations of Surrogacy and Comparability? A: Theorem 4 shows that even without Surrogacy or Comparability (but maintaining Unconfoundedness), the estimators converge to a valid causal quantity: E[µ(Si(1),Xi,O) − µ(Si(0),Xi,O) | Pi=E], the average treatment effect on the surrogate index. The surrogacy-bias equals E[(µ(Si,1,Xi,E) − µ(Si,0,Xi,E)) · ρ(Si,Xi)(1−ρ(Si,Xi)) / (ρ(Xi)(1−ρ(Xi))) | Pi=E], which is small when the treatment explains little variation in Yi conditional on surrogates, or when the surrogate score is near zero or one. The comparability-bias depends on the product of the cross-sample discrepancy in the surrogate index and the deviation of the surrogate score from the propensity score.

Q: What are the efficiency gains from using surrogates? A: Theorem 2(ii) shows that in the limit as the observational sample grows large relative to the experimental sample, the efficiency bound using surrogates is strictly smaller than the Hahn (1998) bound for a direct randomized experiment. The gain equals E[(1−Wi)(Yi−µ(Si,Xi,O))²/(1−ρ(Xi))² + Wi(Yi−µ(Si,Xi,O))²/ρ(Xi)² | Pi=E] — the variance of the residual from predicting Yi with the surrogate index. Theorem 3 also characterizes the efficiency gain within a single sample from imposing the Surrogacy assumption itself, which equals E[σ²(Si,Xi,E) · ρ(Si,Xi)(1−ρ(Si,Xi)) / (ρ(Xi)²(1−ρ(Xi))²)].

Q: Why do multiple surrogates improve on a single surrogate? A: Multiple surrogates make the Surrogacy assumption more plausible, analogously to how multiple pre-treatment covariates make Unconfoundedness more plausible. If a treatment affects the primary outcome through several distinct causal channels (e.g., math skills, language skills, social skills), any single surrogate capturing only one channel leaves remaining pathways uncontrolled, producing bias. With multiple noisy measures of underlying mediators, even if no single observable fully satisfies Surrogacy, their combination removes more bias than any individual measure. The authors also illustrate via Figure 1.D that multiple surrogates reduce the “teaching to the test” problem, where improving a single measured surrogate does not translate to improvements in the primary outcome.

Q: What is the double matching estimator? A: For a treated unit i with covariates Xi and surrogates Si, the estimator first finds a control match j in the experimental sample based on Xi alone (so Xj ≈ Xi). It then finds, for each of units i and j, the nearest neighbor in the observational sample using both Xi and Si jointly, yielding observed outcomes Yi’ and Yj’. The estimated individual treatment effect is Yi’−Yj’, and the estimator averages these across the experimental sample. This mirrors standard matching under unconfoundedness but requires two layers of matching — within the experimental sample on pre-treatment variables, and into the observational sample on both pre-treatment variables and surrogates.

Q: What do the GAIN empirical results show quantitatively? A: The experimental benchmark for Riverside is a 6.4 pp (s.e. 1.2 pp) increase in mean quarterly employment and a $249 (s.e. $83) increase in mean quarterly earnings, each averaged over 36 quarters. The surrogate index estimator using 6 quarters yields estimates of 0.061 (s.e. 0.006) for employment and $238.8 (s.e. $31.5) for earnings — both within one standard error of the benchmark. All three surrogate-based estimators are within two standard errors of the benchmark at 5 quarters. The naive estimator (direct short-run effect) requires more than 25 quarters to come within two standard errors. The surrogate approach achieves a 35% reduction in standard errors relative to waiting for 9-year outcomes.

Q: How do the authors validate the Surrogacy and Comparability assumptions empirically? A: To test Surrogacy, they regress the primary outcome on pre-treatment variables, surrogates up to quarter t, and the treatment indicator in the Riverside experimental sample: a statistically significant treatment coefficient indicates a violation. Point estimates are large and significant for t ≤ 3 quarters; for t ≥ 4 most t-statistics fall below 2, though some remain slightly above 2 with small coefficient magnitudes. To test Comparability, they pool the experimental and observational samples and include an indicator for the experimental sample; significant coefficients on this indicator signal that the surrogate-to-outcome relationship differs across samples. The Comparability violation indicator remains statistically significant even with many surrogate periods, suggesting residual concern.

Q: How does the paper relate Surrogacy to the mediation and instrumental variables literatures? A: In mediation, all three variables — treatment, mediator, outcome — are observed in the same sample, and the goal is to decompose the total effect into direct and indirect components; Surrogacy corresponds to the case where the direct effect is zero by assumption. In the IV framework, the surrogate corresponds to the endogenous treatment, but an unobserved confounder between surrogate and outcome violates Surrogacy. The IV exclusion restriction (no direct effect of the instrument on the outcome) is the analog of Surrogacy’s requirement of no direct treatment effect on the primary outcome. The paper formalizes these analogies through directed acyclical graphs.

Q: What is the missing data interpretation of the key assumptions? A: The joint conditional independence Pi ⊥⊥ Yi ⊥⊥ Wi | Si, Xi implies both Surrogacy and Comparability simultaneously. This is closely related to the Missing at Random (MAR) assumption: the missingness of Yi in the experimental sample and of Wi in the observational sample is determined entirely by the observed surrogates and pre-treatment variables. This “data fusion” interpretation allows insights from the missing data literature — including semiparametric efficiency results — to apply directly.

Q: What is the proposed strategy for building credibility across studies? A: The authors advocate constructing a “library” of surrogate indices by systematically cataloging, across multiple studies in a given domain, the smallest set of surrogates that reliably matches long-run treatment effects. If six quarters of employment and earnings data are established across multiple job training programs to predict 9-year impacts — as the cross-site GAIN comparisons suggest — then future job training evaluations could credibly report long-run impact estimates after only six quarters. The empirical application is presented as one element of such a library.

Surrogate Index: The conditional expectation of the primary outcome given surrogate outcomes and pre-treatment variables, estimated in the observational sample — µ(s,x,O) = E[Yi|Si=s, Xi=x, Pi=O]. It aggregates multiple short-term proxy variables into a scalar that, under Surrogacy and Comparability, identifies the average treatment effect on the long-run outcome.

Prentice Surrogacy Assumption: The condition Wi ⊥⊥ Yi | Si, Xi, Pi=E — the long-run primary outcome is independent of the treatment conditional on the surrogates and pre-treatment variables. Operationally, this requires that all causal pathways from treatment to primary outcome pass through the measured surrogates, with no direct effect remaining.

Comparability Assumption: Pi ⊥⊥ Yi | Si, Xi — the conditional distribution of the primary outcome given surrogates and pre-treatment variables is identical in the experimental and observational samples. This formalizes the condition under which the observational sample’s surrogate-to-outcome relationship can be transported to the experimental sample.

Surrogate Score: The conditional probability of treatment given surrogates and pre-treatment variables in the experimental sample, ρ(s,x) = Pr(Wi=1|Si=s, Xi=x, Pi=E). Plays an analogous role in the surrogate framework to the propensity score under unconfoundedness: if Surrogacy holds conditional on (Si,Xi), it also holds conditional on the surrogate score alone.

Sampling Score: The conditional probability of belonging to the experimental sample given surrogates and pre-treatment variables, φ(s,x) = Pr(Pi=E|Si=s, Xi=x). Appears in the surrogate score estimator and influence function to reweight observations from the observational sample toward the experimental sample distribution.

Double Robustness: The influence function estimator is doubly robust: it remains consistent if either (a) the conditional outcome models µ(s,x,O) and µ(w,x) are correctly specified regardless of the score models, or (b) the propensity score ρ(s,x), propensity score ρ(x), and sampling score φ(s,x) are correctly specified regardless of the outcome models.

Surrogacy Bias: The bias arising when Surrogacy fails while Comparability holds, equal to E[(µ(Si,1,Xi,E) − µ(Si,0,Xi,E)) · ρ(Si,Xi)(1−ρ(Si,Xi)) / (ρ(Xi)(1−ρ(Xi))) | Pi=E]. It is driven by the product of the direct treatment effect on the outcome (conditional on surrogates) and a measure of how much the surrogates explain treatment assignment.

To Own or to Rent? The Effects of Transaction Taxes on Housing Markets

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Summary

Using sales and leasing transaction records for the Greater Toronto Area (2006–2018), this paper finds three novel effects of a higher property transaction tax: higher buy-to-rent transactions alongside lower buy-to-own transactions despite both being taxed, a lower sales-to-leases ratio, and a lower price-to-rent ratio. The empirical identification exploits the City of Toronto’s introduction of a city-level Land Transfer Tax (LTT) in February 2008 — covering only the city and not surrounding GTA municipalities — comparing outcomes on opposite sides of the city border before and after the tax change. A 1.3 percentage-point higher effective LTT rate causes buy-to-rent purchases to rise by 9.3% while owner-occupier purchases fall by 9.6%; the leases-to-sales ratio rises by 26% and the price-to-rent ratio falls by 3.8%. To explain these facts, the paper develops a search model featuring household tenure choice (own vs. rent) subject to heterogeneous credit costs, endogenous homeowner moving decisions, and free entry of buy-to-rent investors; the key mechanism is that the LTT reduces homeowners’ mobility — because owner-occupiers expect to transact multiple times over their lifetimes and thus bear the tax repeatedly — discouraging entry into ownership and raising demand for rentals, which in turn attracts investor entry even though investors too pay the tax, since investors need not re-transact whenever a tenant vacates. The implied deadweight loss is large at 111% of tax revenue, with more than half of this due to distorting decisions to own or rent; taking the rental market into account accounts for losses equal to 73% of tax revenue, which is two-thirds of the total loss.

In depth

Q1. Q: What are the three novel empirical facts documented in this paper?

A: Using MLS data on both sales and leases in the Greater Toronto Area, the paper documents: (1) a 1.3 pp higher effective LTT rate causes buy-to-rent (BTR) investor purchases to increase by 9.3%, in stark contrast to a 9.6% fall in owner-occupier (buy-to-own) purchases — a divergence that is counterintuitive because both types of buyer are subject to the same tax; (2) the ratio of leases to sales rises by 26%, indicating that rental-market activity increases relative to ownership-market activity; and (3) the price-to-rent ratio falls by 3.8%, meaning house prices decline relative to rents.

Q2. Q: What is the empirical identification strategy and why is it credible?

A: The paper uses a geographic regression discontinuity approach comparing communities on opposite sides of the Toronto city border, where the new city-level LTT applies on one side but not the other, in a difference-in-differences framework spanning January 2006–January 2008 (pre-policy) and February 2008–February 2012 (post-policy). The sample is restricted to properties within 3 or 5 km of the boundary. The paper verifies that property characteristics do not differ significantly across the border and that cross-border differences do not change after the LTT, supporting the parallel-trends assumption. The effective LTT rate increase is measured at 1.3 percentage points (assuming 40% first-time buyers, who receive a partial exemption). Buy-to-rent transactions are identified in the MLS data by matching properties that appear in both the sales and leases datasets within an 18-month window following sale.

Q3. Q: What is the intuition for why the LTT raises buy-to-rent investment even though it taxes investors?

A: The mechanism hinges on the asymmetry in expected future transaction costs between owner-occupiers and investors. Owner-occupiers face idiosyncratic match-quality shocks — they periodically want to move to a different property as their circumstances or preferences change — so choosing homeownership means expecting to pay the LTT on each future move. This makes homeownership less attractive relative to renting, reducing household entry into the ownership market and increasing demand for rental properties. Investors (landlords), by contrast, do not need to re-transact in the ownership market simply because a tenant moves out; they retain the property and find a new tenant. Investors therefore face a lower expected frequency of LTT payments per year of property holding than owner-occupiers. As a result, the LTT’s negative effect on investor returns is smaller in magnitude than the increase in rental demand it generates. In equilibrium, the price-to-rent ratio falls by enough to attract more BTR investors in spite of the direct cost the tax imposes on them, and investor purchases rise.

Q4. Q: How does the LTT affect homeowner mobility (the “lock-in” effect) and what are its welfare implications within the ownership market?

A: The LTT makes existing homeowners more tolerant of poor match quality with their current property, since the cost of moving — paying the tax again — has risen. Moving rates therefore decline as households remain in properties for longer on average. To mitigate future tax costs, buyers also become more selective (“picky”) when initially matching with a property, requiring higher match quality before purchasing. This reduces the frequency of moves but increases the cost and duration of search for new buyers. The welfare consequences within the ownership market are: (a) misallocation of properties among owner-occupiers as average match quality falls because households move less often to renew it; partially offset by (b) higher initial match quality for newly matched buyers, but at the cost of longer search. The LTT-induced distortions within the ownership market account for a loss equal to 38% of tax revenue.

Q5. Q: What are the model’s quantitative predictions for the four-year post-reform period, and how do they compare to the empirical estimates?

A: The model is calibrated to the City of Toronto for 2006–8 (homeownership rate ~54%) and simulated for a 1.3 pp LTT increase, with the mobility hazard rate used as the internal calibration target. For the four-year period following the tax change, the model predicts: owner-occupier transactions fall by 14%; buy-to-rent transactions rise by 35%; the leases-to-sales ratio rises by 15%; the price-to-rent ratio falls by 1.6%; and the homeownership rate falls by 0.23 percentage points. These figures are broadly consistent in magnitude with the estimated LTT effects on the variables not directly targeted in calibration (i.e., the transaction-volume and price-to-rent results from the empirical estimation).

Q6. Q: What are the long-run (steady-state) effects and why do they differ from the four-year effects?

A: Tenure-choice variables are very slow to adjust because annual flows are small relative to housing stocks. In the new steady state, the homeownership rate falls by 2.4 percentage points and the leases-to-sales ratio rises by 23% — both substantially larger than the four-year effects. By contrast, four-year effects on owner-occupier transactions and the price-to-rent ratio are already close to their new steady states. Buy-to-rent transactions overshoot their steady-state level (the four-year rise of 35% compares to a steady-state rise of 5.1%) because of a one-off surge in investor entry as the rental market absorbs the transition; once the stock of rental properties has adjusted, the flow of new buy-to-rent purchases settles lower.

Q7. Q: How are the welfare (deadweight) losses decomposed across distortion channels?

A: The new LTT generates a total welfare loss equivalent to 111% of the extra revenue it raises. The decomposition is: distortions to flows between the rental and ownership markets (i.e., the tenure-choice margin) account for a loss equal to 60% of extra revenue; distortions within the rental market account for 13% of tax revenue; distortions within the ownership market (lock-in and match-quality misallocation) account for 38% of tax revenue. The presence of the rental market in the analysis — encompassing both the across-market and within-rental-market channels — accounts for a loss equivalent to 73% of tax revenue, which is two-thirds of the total loss. The paper characterises this as “large.”

Q8. Q: What is the across-market misallocation mechanism behind the 60% welfare loss from tenure distortions?

A: Because owner-occupiers expect to transact more frequently than buy-to-rent investors, the same ad valorem tax falls more heavily on owner-occupiers. In equilibrium, the cost of credit paid by the marginal home-buyer must fall — that is, fewer creditworthy households enter ownership. This displaces some creditworthy households into the rental market, creating a misallocation: properties are allocated away from owner-occupiers (who value them as a place of residence and benefit from match quality) toward rentals intermediated through investors. The welfare loss arises because credit-worthy households who would prefer to own are now renters, and the resource costs of intermediating through investors are incurred unnecessarily.

Q9. Q: What policy experiment does the paper consider beyond the baseline LTT analysis?

A: The paper studies an alternative tax structure that imposes a higher LTT rate on buy-to-rent investors relative to owner-occupiers, calibrated to nullify the implicit tax advantage investors enjoy under a uniform rate. By raising barriers to investor entry, this differential tax reduces the across-market welfare losses from lower homeownership. However, the paper notes an important caveat: pushing the investor tax rate ever higher to boost homeownership would ultimately produce large welfare costs in the opposite direction, as households who cannot qualify for mortgage credit (uncreditworthy households) would be displaced into the ownership market by a shortage of rental properties. Investors play a socially valuable role in providing housing access to households who cannot or choose not to bear the costs of credit.

Q10. Q: What data source is used and why is it unusually well-suited to this analysis?

A: The paper uses Multiple Listing Service (MLS) records from the Toronto Regional Real Estate Board covering the Greater Toronto Area, 2006–2018. The dataset is distinctive in including both sales transactions and lease transactions, allowing the paper to match the two and construct the novel buy-to-rent identifier. MLS data cover approximately 78% of detached-house transactions in the Toronto Land Registry for 2006–2012, and the rental listings capture over 90% of properties listed on alternative platforms. This combination of sales and lease records is what makes it possible to document the three novel empirical facts and to study both the ownership and rental markets jointly.

Key Concepts

Buy-to-rent (BTR) transaction: In this paper’s definition, a sale in the ownership market where the buyer subsequently lists the same property on the rental market within 18 months. BTR buyers are investors/landlords who supply rental housing by purchasing from the ownership market. Distinct from buy-to-own (owner-occupier purchases) and buy-to-sell (flipping) transactions. Identified in the MLS data by matching address and transaction dates across the sales and leases databases.

Buy-to-own (BTO) transaction: A sale in the ownership market where the buyer occupies the property as a homeowner — the residual category after removing BTR and buy-to-sell transactions from total sales. In the City of Toronto, the fraction of all transactions classified as BTO declined from 89% to 84% between 2006 and 2017.

Effective LTT rate: The mean land transfer tax paid as a percentage of the sales price, combining provincial- and city-level taxes, averaged over detached-house transactions in the City of Toronto and adjusted for first-time buyer exemptions. The introduction of the city-level LTT in February 2008 raised the effective LTT rate by 1.3 percentage points (assuming 40% first-time buyers).

Match quality: In the paper’s search model, the idiosyncratic value a particular household places on a particular property, which evolves stochastically over time. When match quality deteriorates sufficiently, a homeowner wishes to move to a better-matched property. Match quality is the source of the “lock-in” effect: higher transaction taxes raise the threshold quality decline a household is willing to tolerate before moving, reducing mobility. Because investors are not tied to a specific property in the same way (a tenant moving out does not require the investor to transact), this mechanism falls more heavily on owner-occupiers than on BTR investors.

Lock-in effect: The reduction in homeowner mobility caused by a higher transaction tax. Homeowners become more tolerant of deteriorating match quality (stay longer in poorly matched properties) and more selective when initially purchasing (require higher match quality to justify the transaction cost). The paper treats this as operating on the intensive margin of homeownership decisions, contrasted with the extensive margin (the own-vs.-rent choice).

Credit cost / credit friction: Heterogeneous household-level costs of accessing mortgage finance or credit. In the model, a household must pay a credit cost to enter the ownership market. Households with lower credit costs are more likely to choose homeownership; a higher transaction tax effectively raises the total cost of ownership (since it must be paid on each future move), shifting the margin at which the credit cost equals the net benefit of owning, thereby reducing the equilibrium homeownership rate.

Leases-to-sales ratio: The ratio of new lease transactions to sales transactions in the housing market, used as a measure of the relative activity of the rental and ownership markets. A higher ratio indicates more households are being accommodated in the rental market relative to the ownership market. The LTT raises this ratio by 26% in the empirical estimation and 15% in the four-year model simulation, with a steady-state increase of 23%.

Price-to-rent ratio: The ratio of house prices to rents, used as a summary statistic for the relative cost of owning versus renting. In the paper’s model, a fall in the price-to-rent ratio is the price signal that attracts additional buy-to-rent investor entry: as tenure-choice distortions shift more households toward renting, rents rise relative to prices, improving the return to BTR investment until the rental market clears. The LTT lowers the price-to-rent ratio by 3.8% empirically and 1.6% in the four-year model simulation.

Deadweight loss as a fraction of tax revenue: The welfare cost of the LTT measured in units of tax revenue raised, allowing comparison across tax instruments. The paper finds a deadweight loss of 111% of tax revenue for the Toronto LTT. Prior literature, which focused only on the intensive margin (mobility distortions within the ownership market), missed the across-market and within-rental-market channels that together account for 73 percentage points of this total.

Unemployment Insurance, Starting Salaries, and Jobs

Mon, 01 Jan 0001 00:00:00 +0000

Seven U.S. states permanently cut unemployment insurance (UI) benefits by 30–64 percent between 2011 and 2014, providing the study’s quasi-experimental variation. North Carolina enacted the largest reform: maximum duration fell from 26 weeks to 12–20 weeks and maximum weekly benefits fell from $535 to $350, an average total reduction of 64 percent. Six “moderate reform” states (FL, GA, KS, MI, MO, SC) cut duration only, by an average of 30 percent (26→18 weeks). Using a multi-state firm identification strategy — comparing establishments of the same firm operating in reform states against the same firm’s establishments in non-reform states, with establishment and firm×year fixed effects — the paper estimates causal effects of UI cuts on employment (EEOC, 946K–1.4M establishment-years), starting salaries (Glassdoor, 500K–942K person-years), and posted wages (Burning Glass Technologies, 709K–1.18M establishment-job-quarters). The main results: NC establishments gain +1.3% employment on average relative to same-firm establishments in other states (ATT), reaching +2.1% by year 2; moderate reform states gain +0.8% (ATT). Starting salaries of new hires fall −5.5% in NC and −1.2% in moderate states. Posted wages for the same job within the same firm fall −3.5% in NC and −3.2% in moderate states. The negative co-movement of employment and wages identifies a labor supply shock: workers lower reservation wages in response to reduced outside options; firms take advantage by hiring more at lower wages. Labor demand elasticity: −0.36 (SE 0.21) for NC, −0.42 (SE 0.18) for moderate states. The larger effects in NC relative to moderate reform states are consistent with the larger total benefit reduction; effects are robust to controlling for concurrent right-to-work laws, minimum wage changes, Medicaid expansions, and corporate/personal tax reforms. The paper concludes that large, permanent UI reductions can raise employment but at the cost of lower starting wages.

In depth

Q1. How does the multi-state firm design separate UI effects from aggregate and local shocks?

The key innovation is including firm×year fixed effects alongside establishment fixed effects: within any given firm and year, the only remaining variation is which state the establishment is in — absorbing all firm-wide demand trends, management strategies, and capital-allocation decisions that would otherwise confound cross-state comparisons. Standard difference-in-differences compares reform states to non-reform states at the level of geographic unit or industry; this approach confounds UI changes with the economic conditions that prompted them. The multi-state firm design eliminates this confound because firms’ nationwide operational decisions are held constant. The identification concern is policy endogeneity — whether reform states had weaker economies motivating both the UI cuts and slow hiring. This is addressed in three ways: (1) the 27 other states whose UI trust funds became insolvent in the early 2010s did NOT cut benefits, ruling out insolvency per se as the trigger; (2) restricting the control group to only the insolvent states (Table 3 cols 2 and 5) leaves estimates nearly unchanged; (3) restricting further to insolvent states that experienced a Great Recession unemployment shock within ±2 percentage points of the reform states (Table 3 cols 3 and 6) again leaves estimates unchanged, ruling out mean reversion. The mean reversion hypothesis is additionally ruled out by the wage results: mean reversion predicts faster wage growth in reform states, but wages fall.

Q2. What are the quantitative employment effects, and how do they compare across specifications?

In the baseline specification (Table 3, column 1), NC establishments gain +1.26% employment on average over the post-reform period (ATT, SE 0.0052, p<0.05), with the effect growing from +1.2% in year 1 to +2.1% in year 2 (both p<0.01); moderate reform states gain +0.83% (ATT, SE 0.0022, p<0.01), reaching +1.5% by year 2. Alternative specifications (Table 5) using less-saturated fixed effects (firm+state+year FEs or establishment+year FEs only) produce estimates roughly twice as large — +2.5% for NC — confirming that firm×year fixed effects absorb a substantial share of cross-state employment variation that is not attributable to UI. This amplification underscores why controlling for firm-level trends matters: firms simultaneously expanding in many states would appear in the unconditioned data as UI-reform effects. Robustness to policy confounders (Table 4): excluding states with RTW law changes, minimum wage changes, Medicaid expansions, major corporate or personal tax reforms all leave ATTs statistically significant and economically similar (0.80%–1.25% for NC; 0.82%–1.18% for moderate states). A Fisher exact test places NC’s t-statistic in the top 2/42 (4.8%) of placebo assignments, consistent with a one-sided 5% test. Controlling for NC’s concurrent corporate tax cut, which bounds the maximum tax-driven employment effect at 0.76pp (Giroud and Rauh 2019), implies the UI reform accounts for between 0.5% and 1.26% of NC’s employment increase — broadly consistent with the 0.83% moderate reform estimate.

Q3. What do the wage results show, and how do posted wages rule out compositional explanations?

Table 7 (Glassdoor starting salaries, job and firm×year FEs): NC ATT = −5.5% (SE 0.021, p<0.01), moderate states ATT = −1.2% (SE 0.0051, p<0.05); the effect is concentrated in jobs with starting salaries at or below $100,000, where UI replacement rates are meaningfully binding, and is statistically insignificant for higher-wage jobs. Starting salary declines could in principle reflect worker composition (lower-skilled workers drawn into the labor force) or worse job matches (workers accepting jobs below their productivity) rather than firms lowering offer wages. Burning Glass Technologies (BGT) posted wages, which measure the wage advertised for the same job within the same firm over time (establishment-job and firm×year FEs), rule out both channels: Table 8 shows NC posted wage ATT = −3.5% (SE 0.013, p<0.01) and moderate states = −3.2% (SE 0.0071, p<0.01). The near-equality of posted and realized wage effects implies the wage decline is driven by firms lowering their wage offers — not by changes in worker composition or match quality. Occupational heterogeneity confirms the mechanism: high-exposure occupations (above-median fraction of workers with unemployment spells or employment tenures exceeding 20 weeks) exhibit NC posted wages −3.5% and moderate states −4.1%; low-exposure occupations show near-zero insignificant effects (Table 9). Posted wages also provide additional evidence against mean reversion: if reform states had faster-growing underlying wages, posted wages would rise relative to controls, but the opposite occurs.

Q4. How does the negative co-movement of employment and wages identify a labor supply shock and discipline the theoretical mechanism?

The simultaneous rise in employment (+1.26% NC, +0.83% moderate) and fall in posted wages (−3.5% NC, −3.2% moderate) is the signature of a labor supply shock under the standard Mortensen-Pissarides (1994) framework: when workers’ outside option (the value of UI) falls, their reservation wages fall, inducing firms to post more jobs at lower wages. A positive demand shock would raise both employment and wages; a positive supply shock raises employment while lowering wages. The posted wage channel further implies that firms’ labor demand responds to the wage reduction (not just to the supply expansion): if firms were passive price takers, posted wages would not change. The data imply that firms internalize workers’ changed outside options and lower their wage offers accordingly, consistent with the monopsonistic wage-setting in Mortensen-Pissarides with free entry. The labor demand elasticity calculated as (Δlog employment / Δlog posted wage) = 1.26/3.5 ≈ −0.36 (SE 0.21) for NC and 0.83/3.2 ≈ −0.26 or using preferred specification −0.42 (SE 0.18) for moderate states; these fall in the middle of the distribution of prior estimates from cross-country labor demand elasticity studies (Hamermesh 1996; Acemoglu et al. 2004). A Chodorow-Reich et al. (2019) decomposition suggests that if labor market tightness increased (fewer unemployed and more vacancies), the reservation wage (opportunity cost) effect dominates the tightness effect — since we observe posted wages falling.

Q5. What do the CPS results add, and how do employment duration effects inform the mechanism?

Using individual-level CPS data with state and year fixed effects (no within-firm comparison), combining all reform states: employment probability +1.0pp (SE 0.43pp, a 1.5% increase relative to the 65% baseline) [Table 10 col 1]; new-hire wages (tenure <1yr) −6.3% [col 2]; unemployment duration −2.8 weeks/year ATT (relative to 33.48-week control mean, an 8% reduction) [col 3]. The CPS results are qualitatively consistent with the multi-state firm findings and use an entirely different data source, sampling frame, and identification approach. The unemployment duration effects are instructive about timing and mechanism: the ATT is negligible in the first two post-reform years (−1.0 and −1.2 weeks, insignificant), rises to −1.7 weeks in year 3, −3.6 in year 4, −4.2 in year 5, and −5.6 in year 6 — consistent with gradual stock-flow dynamics (the stock of workers who began unemployment before the reform exhausts gradually, so average duration in the reform states drifts lower over time as a larger share of the unemployed pool faces the new rules). This pattern helps interpret the gradual employment growth in the event studies.

Q6. How does the paper explain divergence from prior literature finding small UI effects?

The paper argues that prior work finds small effects because reforms studied were smaller in size, temporary, and enacted during deep recessions — all conditions where the job creation channel from lower reservation wages is muted. Schmieder et al. (2010), Rothstein (2011), Farber-Valletta (2015), Chodorow-Reich et al. (2019) and others study UI extensions/expirations that are often 13–20% changes in duration (versus NC’s 44% duration cut and 64% total benefit cut), enacted during high unemployment (when moral hazard is lower) or temporary (so workers discount the change in outside options). A 13-week contrast off a high base of 83 weeks (the EUC expansions) differs fundamentally in moral hazard intensity from an 11.5-week cut off a low base of 26 weeks plus a benefit level reduction — the effective present value of UI falls far more in the NC reform. Additionally, the border county-pair design used in much prior work (Chodorow-Reich et al. 2019, Hagedorn et al. 2025) compares establishments on opposite sides of a state border within the same labor market; these competing establishments cannot fully exploit lower reservation wages because they compete for the same workers — suppressing both the employment and wage responses. Notable exceptions that do find sizable effects — Johnston-Mas (2018) and Karahan et al. (2025), both studying large permanent post-recession reforms — corroborate this paper’s findings.

Key concepts

multi-state firm design : the identification strategy that compares establishments of the same firm operating in reform states against the same firm’s establishments in non-reform states; with establishment and firm×year fixed effects, this absorbs firm-wide demand trends, product market shocks, and management decisions that affect all of a firm’s establishments equally, isolating state-level UI variation as the sole source of identification.

reservation wage : the minimum wage at which an unemployed worker is willing to accept a job offer, determined by the outside option value (UI benefits plus expected future wages from continued search); UI cuts reduce the outside option value, lowering the reservation wage and enabling firms to post and fill vacancies at lower wages.

posted wage : the wage listed in a job advertisement before any worker-firm negotiation or match quality sorting; measured here using Burning Glass Technologies (BGT) data at the establishment-job level, controlling for the same job across time within the same firm; distinct from realized starting salary in that it reflects the firm’s wage-setting decision independent of which worker accepts.

labor supply shock : an exogenous change in the willingness of workers to supply labor at given wages; identified here by the negative co-movement of employment (up 1.3–0.8%) and wages (down 3.5–3.2%), which is the opposite of what a positive labor demand shock would predict, ruling out confounding from corporate tax cuts or mean-reverting demand.

outside option : the payoff available to an unemployed worker from continued search rather than immediate job acceptance; UI benefits are the dominant component; when UI generosity falls, the outside option value falls and firms can hire more workers at lower wages — the core mechanism linking permanent UI cuts to simultaneous employment gains and wage reductions.

Unpacking Aggregate Welfare in a Spatial Economy

Mon, 01 Jan 0001 00:00:00 +0000

What Do Policies Value?

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks a fundamental question about policy design: when a program prioritizes one group over another, is that because the group benefits more from the intervention, or because the policy assigns them higher intrinsic welfare weight? Björkegren, Blumenstock, and Knight develop a two-stage method to decompose observed allocation decisions into their underlying components: (i) welfare weights assigned to different types of people, (ii) heterogeneous treatment effects of the intervention, and (iii) relative weights on different outcomes. The key insight is that the same allocation rule can be consistent with very different value systems depending on how much each group actually benefits.

The method works as follows. In a first stage, the analyst estimates heterogeneous treatment effects — how much each individual benefits on each outcome dimension — using OLS or machine learning methods (e.g., causal forests). In a second stage, the analyst reconciles the observed ranking of beneficiaries with an implicit welfare function using an exploded logit likelihood, recovering welfare weights (who is valued), impact weights (how different outcomes are valued), and a base value for treatment independent of measured outcomes. Identification requires an exclusion restriction: the covariates used to estimate treatment effect heterogeneity must include variables excluded from the welfare weight specification, allowing the analyst to compare households with similar welfare weights but differential treatment effects. Variants of the method that impose known welfare weights or known impact weights can be used without the exclusion restriction.

The paper demonstrates the method using PROGRESA, Mexico’s large conditional cash transfer program launched in 1997. PROGRESA ranked households by a proxy means test poverty score and transferred approximately 197 pesos per month (roughly $20 USD) to eligible poor households, conditional on school attendance and doctor visits. The analysis uses endline survey data on 7,767 households and focuses on three outcomes emphasized in program documents: log per-capita consumption, child sick days (ages 0-5), and school days missed (ages 6-16).

The program’s average treatment effects were: a 0.149 log point increase in monthly consumption (SE=0.015), a 0.165 reduction in sick days per child (SE=0.051), and a near-zero effect on school days missed (-0.0053, SE=0.028). These effects were heterogeneous: indigenous households, for instance, benefited substantially more from the program.

The paper’s central empirical finding inverts the naive interpretation of PROGRESA’s targeting. Indigenous households were ranked 60.6 log points higher in the program’s priority order. A simple regression suggests the program favored them. But after accounting for the fact that indigenous households benefit substantially more from treatment, the method finds that the program’s implied welfare weight on indigenous households is, if anything, lower by 17.4% relative to non-indigenous households — not higher. The program’s prioritization of indigenous households is thus explained by efficiency, not by preferential welfare weighting.

Because PROGRESA cash transfers relax household budget constraints and outcomes like consumption reflect household choices, the impact weights capture the difference between how the policy values outcomes and how households value them. The estimates strongly reject non-paternalism: the policy implicitly values consumption and potentially health differently from household decision-makers. Of the total welfare impact, approximately 55% is attributed to the base value of the transfer itself (independent of measured outcomes), approximately 45% to consumption impacts, and less than 1% to health and schooling impacts combined. The implied value of providing the transfer independent of outcomes corresponds to 0.16 log points of consumption, or about 23.1 pesos per person per month — slightly below the average transfer of 33.9 pesos per person per month.

The paper also runs counterfactual exercises showing how alternative preference structures would have changed the allocation. A policy maximizing only educational impacts would have prioritized richer, smaller households; one maximizing only consumption impacts would have further prioritized indigenous households. These counterfactuals are mapped onto a Pareto frontier across the three outcomes. The estimated welfare weights from the implemented policy align closely with preferences elicited in a 2023 survey of 429 Mexican residents, though residents placed higher value on child health relative to what the policy implied.

Q: What is the core identification challenge the paper addresses? A: When a policy prioritizes a group, it could be because the group benefits more (efficiency) or because the policy assigns them intrinsically higher value (preference). These two explanations are observationally equivalent from the allocation alone. The paper separates them by first estimating heterogeneous treatment effects and then inverting the allocation to recover residual welfare weights.

Q: What is the exclusion restriction required for full identification? A: The covariates used to estimate treatment effect heterogeneity (x-tilde) must include at least some variables excluded from the welfare weight specification (x). This allows the analyst to compare households with similar welfare weights but different predicted treatment effects, pinning down how much of the ranking reflects efficiency versus preference. Without this restriction, one can still recover conditional preferences by imposing known values for either welfare weights or impact weights.

Q: How does the exploded logit likelihood work in this setting? A: The analyst observes a single full ranking of all households, rather than partial orderings from multiple decision-makers. The welfare impact of treating household i is modeled as a linear function of predicted treatment effects scaled by welfare and impact weights, plus an extreme-value-distributed shock. The likelihood of observing household i ranked above household i-prime is the ratio of their exponentiated welfare scores, summed over all households ranked below i. Maximum likelihood recovers the welfare weights, impact weights, and base value simultaneously.

Q: What were PROGRESA’s average treatment effects on the three focal outcomes? A: Average treatment increased log monthly consumption by 0.149 (SE=0.015), reduced child sick days by 0.165 (SE=0.051), and had a near-zero effect on school days missed (-0.0053, SE=0.028). The consumption and health effects are statistically significant; the schooling effect is not distinguishable from zero.

Q: What does the analysis find about the welfare weight assigned to indigenous households? A: In the raw ranking regression, indigenous households are ranked 60.6 log points higher, suggesting the program favored them. After accounting for the fact that indigenous households benefit substantially more from treatment, the method finds the implied welfare weight on indigenous households is lower, not higher — specifically, about 17.4% lower than non-indigenous households. The program’s higher ranking of indigenous households is explained entirely by their larger treatment effects, not by preferential weighting.

Q: How are the impact weights on consumption, health, and schooling interpreted given that outcomes reflect household choices? A: Because PROGRESA relaxes household budget constraints and outcomes like consumption result from household optimization, the estimated impact weights capture the difference between how the policy values outcomes relative to how households value them (internalities), rather than the absolute policy valuation. A nonzero weight implies the policy disagrees with household preferences — paternalism. The positive coefficient on log consumption implies the policy values this outcome more than households do.

Q: How much of PROGRESA’s welfare impact comes from the base transfer value versus measured outcomes? A: The base value of the transfer (independent of measured impacts on consumption, health, and schooling) accounts for approximately 55% of total implied welfare impact. The impact on consumption accounts for approximately 45%. Impacts on health and schooling together account for less than 1%. The implied value of the base transfer corresponds to 0.16 log points of consumption per capita, or about 23.1 pesos per person per month — somewhat below the average transfer amount of 33.9 pesos per person per month.

Q: Does the analysis reject egalitarian welfare weights and non-paternalism? A: Yes, using Wald tests with bootstrapped covariance matrices. The hypothesis of egalitarian weights (all gamma equal to one) is rejected. Non-paternalism (all beta equal to zero) is strongly rejected. The joint hypothesis of egalitarianism and non-paternalism is also rejected across all specifications tested.

Q: How do the estimated welfare weights compare to stated preferences of Mexican residents? A: The 2023 survey of 429 Mexican residents elicited preferences using multiple price lists over how to prioritize different household types. The welfare weights implied by the implemented policy are broadly similar to resident preferences, but the policy places relatively higher welfare weight on indigenous households than the median survey respondent does. Survey respondents value child health impacts more than household decision-makers and more than the implemented policy does, consistent with support for paternalism.

Q: What do counterfactual allocations reveal about the relationship between policy goals and targeting priorities? A: A policy maximizing only consumption impacts would further prioritize indigenous households with lower income. A policy maximizing only educational impacts would instead prioritize richer, smaller households. A policy maximizing only health impacts would largely preserve indigenous household prioritization while placing less emphasis on lower-education households. These three extreme policies map to the corners of a Pareto frontier, and the implemented PROGRESA policy lies close to the allocation consistent with surveyed resident preferences.

Q: What changed when Mexico reformed PROGRESA’s poverty score in 2003? A: The 2003 reform increased the priority of older and smaller households. Applying the method to the new poverty score reveals that it implicitly switched to assigning a positive welfare weight to indigenous households (compared to the negative implied weight under the original score), and placed less welfare weight on lower-income and younger households relative to the original design.

Q: What are the main limitations and scope conditions of the method? A: Full identification requires an exclusion restriction (some treatment effect heterogeneity predictors excluded from welfare weights) and sufficient variation in treatment effects across household types. If treatment effects are homogeneous, welfare weights and impact weights cannot be separately identified. If correlated unobservables drive the ranking but are not modeled, the method recovers preferences consistent with included variables only, analogous to omitted variable bias in OLS. The method also requires a way to estimate treatment effect heterogeneity, which is most credible with a randomized pilot, though non-experimental methods are in principle applicable.

Q: How does this paper relate to the inverse optimum public finance literature? A: The inverse optimum literature (Bourguignon and Spadaro 2012; Saez and Stantcheva 2016; Hendren 2020) recovers the redistribution preferences consistent with income tax schedules, conditioning on a single covariate (pre-tax income) affecting a single outcome (net-of-tax consumption). This paper generalizes that framework to arbitrary allocation policies conditioning on a vector of covariates and affecting a vector of outcomes, and extends it to settings beyond income taxation where heterogeneous treatment effects can be estimated.

Q: Can the method be applied when only a binary allocation is observed rather than a full ranking? A: Yes. A binary allocation corresponds to a ranking with only two levels, and the same exploded logit procedure applies, though with reduced statistical power. The paper provides an empirical illustration of this setting in Section 5.2.1.

Welfare weights (w(x_i)): The policy’s differential valuation of one household’s utility relative to another, expressed as a multiplicative function of household characteristics. Distinct from how much a household benefits — two households may be ranked identically despite different benefits if their welfare weights differ proportionally.

Impact weights (beta_j): The policy’s relative valuation of different outcome components (consumption, health, schooling). For outcomes that are household choices, impact weights capture the difference between how the policy values the outcome and how the household values it — an internality or paternalistic preference.

Base value (alpha): The value a policy assigns to providing a treatment independent of its measured impact on any specific outcome. Captures either a direct utility benefit of treatment or the value of relaxing household budget constraints when outcomes are choices.

Exclusion restriction: The requirement that the set of covariates used to estimate treatment effect heterogeneity includes at least some variables excluded from the welfare weight specification. Enables separate identification of efficiency-based and preference-based components of a ranking by comparing households similar in welfare weight but different in predicted treatment effects.

Exploded logit likelihood: The econometric procedure used in the second stage, adapted for a single complete ranking of all alternatives rather than partial orderings. Treats the observed ranking of household i as a choice from the set of all households ranked below it, with likelihood given by the softmax of welfare scores.

Value audit: A retrospective application of the method that reads the implicit values encoded in an implemented policy’s allocation decisions, enabling comparison against stated policy objectives, constituent preferences, or normative benchmarks.

Paternalism (in this paper’s sense): A policy is paternalistic if it assigns nonzero impact weight (beta_j ≠ 0) to outcomes that are household choices — meaning the policy values those outcomes differently from the households making the choices. The envelope theorem implies a non-paternalistic policy would place zero weight on choice outcomes beyond the general constraint relaxation.

What's My Employee Worth? The Effects of Salary Benchmarking

Mon, 01 Jan 0001 00:00:00 +0000

This paper studies how salary benchmarking tools — products that reveal aggregate market pay statistics for specific job titles — affect employee compensation. The research question is whether firms’ access to such tools causally changes how they set salaries, and what this implies about information frictions in labor markets and the policy debate over benchmarking regulation.

The authors collaborated with the largest U.S. payroll processing company (serving 650,000 firms and 20 million workers), exploiting the staggered roll-out of a proprietary Compensation Benchmark Tool. The tool aggregates payroll data into salary benchmarks by standardized job title, with the median base salary as its most prominent statistic. The study draws on three linked administrative datasets: payroll records (January 2017 to July 2021), tool usage logs (September 2019 to August 2021), and historical benchmark snapshots. The main analytical sample covers new hires at 586 treatment firms that gained tool access and 1,419 matched control firms that did not, within a 10-quarter window around each firm’s onboarding date.

The identification strategy is difference-in-differences, exploiting three sources of variation: which firms gain access; the staggered timing of access (driven by the arbitrary order in which sales representatives introduced the tool); and within treatment firms, whether a specific position was actually searched in the tool. New hires are classified into Searched positions (5,266 hires at treatment firms for positions eventually looked up), Non-Searched positions (39,686 hires at treatment firms for positions not looked up), and Non-Searchable positions (156,865 hires at control firms). Event-study analyses confirm flat pre-trends across all groups, supporting causal interpretation.

The primary finding is that benchmark access reduces salary dispersion around the median market benchmark by 25%. Before onboarding, the average absolute deviation of offered salaries from the median benchmark in Searched positions was 19.8 percentage points (pp). After onboarding, this fell to 14.9 pp — a drop of 5.0 pp using Non-Searched positions as control (p-value < 0.001) and 6.2 pp using Non-Searchable positions as control (p-value < 0.001). Compression runs in both directions: firms previously paying above the benchmark reduce salaries toward the median, and firms previously paying below raise salaries toward the median. The probability of setting a salary within 2.5% of the median benchmark nearly doubled, from 11.6% to 22.1% after onboarding.

Effects are heterogeneous by skill level. For low-skill positions (approximately 42% of the sample, e.g., bank teller, receptionist), dispersion falls from 14.5 pp to 8.7 pp — a 40% reduction. For high-skill positions (e.g., software developer), dispersion falls from 24.0 pp to 20.5 pp — a 14.6% reduction. For low-skill positions, compression from below dominates, producing a net average salary increase of +5.0% to +6.7% (p-values 0.014 and 0.001 depending on control group). For high-skill positions, the average salary effect is small and statistically insignificant overall. Twelve-month retention rates for low-skill workers increase by 6.6 to 6.8 pp after benchmarking, and the implied retention elasticity is consistent with prior literature estimates.

The authors propose a theoretical model to rationalize these findings. Firms are assumed uncertain about the wage distribution (aggregate uncertainty), with private information about their own value of filling a position and affiliated valuations across firms. In equilibrium, firms with higher values make higher offers — generating wage dispersion among identical workers without monopsony power, efficiency wages, or amenity differences. When a firm gains benchmark access, it adjusts its offer toward the threshold wage needed to hire, compressing offers from both sides. In the full-information equilibrium where benchmarks are common knowledge, the mean salary is weakly higher than without benchmarks, because the marginal firm had previously underestimated labor market tightness and offered too little, capturing extraordinary profits. Benchmarking eliminates these informational rents, intensifying competition and raising average pay.

The scope of the empirical findings is restricted to new hires at firms in the top quartile of U.S. firm size by employment, across all industries and U.S. states, over 2017–2020. The estimated effect is the incremental causal impact of one additional high-quality benchmarking source, since most firms already had access to some pay information through other channels.

Q: What is the main causal finding of the paper? A: Access to the salary benchmarking tool reduces the absolute deviation of new-hire salaries from the median market benchmark by approximately 25%. Specifically, average dispersion in Searched positions falls from 19.8 pp before onboarding to 14.9 pp after, a drop of 5.0 pp (using Non-Searched controls, p-value < 0.001) or 6.2 pp (using Non-Searchable controls, p-value < 0.001). The two estimates are statistically indistinguishable from each other, and both are robust to a wide range of specification checks.

Q: How does compression operate — does it raise or lower salaries? A: Compression operates in both directions. Firms that would otherwise have paid above the median benchmark reduce salaries toward the median (“compression from above”), and firms that would otherwise have paid below the median benchmark raise salaries toward the median (“compression from below”). The probability of offering a salary within 2.5% of the median benchmark nearly doubled, from 11.6% before onboarding to 22.1% after.

Q: What is the identification strategy, and why is the treatment considered as good as random? A: The authors use a difference-in-differences design with three sources of variation: which firms gain tool access, the staggered timing of access, and whether specific positions were actually searched within a treatment firm. The payroll company introduced the tool through sales representatives contacting clients in an arbitrary order, not in response to firm characteristics or outcomes. This is corroborated by empirical tests: event-study pre-trends for Searched versus Non-Searched (and Non-Searchable) positions are flat and statistically indistinguishable from zero (pre-treatment coefficients of -0.346 and -0.310, p-values 0.749 and 0.604, respectively).

Q: How large are the effects for low-skill versus high-skill positions? A: For low-skill positions (approximately 42% of the sample, e.g., bank teller, receptionist), dispersion drops from 14.5 pp to 8.7 pp — a 40% decline (p-value < 0.001). For high-skill positions (e.g., software developer), dispersion drops from 24.0 pp to 20.5 pp — a 14.6% decline (p-value = 0.021). The larger effect for low-skill positions is consistent with anecdotal accounts from compensation managers, who report treating low-skill candidates as interchangeable and therefore wanting to offer exactly the market rate.

Q: Does benchmarking raise or lower average salaries? A: On average across all skill levels, the effect on mean salary is small and statistically insignificant: -0.2% (p-value = 0.756) using Non-Searched controls and +1.7% (p-value = 0.308) using Non-Searchable controls. For low-skill positions specifically, average salaries increase by +5.0% (p-value = 0.014) using Non-Searched controls and +6.7% (p-value = 0.001) using Non-Searchable controls. This net increase for low-skill workers reflects compression from below dominating compression from above in that subset.

Q: What are the effects on employee retention? A: For low-skill workers, benchmarking increases the probability of remaining employed at the hiring firm 12 months after the hire date by +6.6 pp (p-value = 0.101) using Non-Searched controls and +6.8 pp (p-value = 0.029) using Non-Searchable controls. The implied retention elasticity from the ratio of salary and retention effects is consistent with average estimates in the prior literature (Sokolova and Sorensen, 2021). No retention effects are reported for high-skill positions.

Q: What is the theoretical mechanism through which aggregate uncertainty generates wage dispersion? A: The model assumes a unit mass of firms simultaneously making wage offers to a mass Q < 1 of workers, with only the top Q offers accepted. Firms have private information about their value of filling the position, and values are affiliated (correlated in the sense of Milgrom and Weber, 1982). Because each firm is uncertain about what other firms will offer, higher-value firms rationally form higher beliefs about the prevailing wage distribution and make higher offers. This generates equilibrium wage dispersion among identical workers without monopsony power, efficiency wages, or amenity differences.

Q: What does the model predict about the equilibrium effects of benchmarking when all firms have access? A: When the benchmark is common knowledge, all firms make offers with full information about the wage distribution. The firms with the highest values win workers at a uniform wage that makes the marginal firm indifferent between hiring and not hiring. The model proves that the mean salary is higher in expectation under the benchmark equilibrium than in the no-benchmark equilibrium. The intuition is that without benchmarks, the marginal firm underestimates labor market tightness, offers less than the full-information competitive wage, and thereby captures extraordinary profits; benchmarking eliminates those rents and intensifies competition.

Q: What are the policy implications of the findings regarding antitrust concerns? A: In 2023, the DOJ and FTC rescinded a long-standing antitrust “safety zone” for salary benchmarks due to concerns that they could facilitate wage collusion. A 2021 executive order had mandated that agencies consider procompetitive effects as well. The authors’ model addresses the collusion concern directly: in equilibrium, benchmarking raises (not lowers) average salaries. The empirical evidence is consistent with this — low-skill workers see average salary increases of 5-7% after benchmarking — suggesting a procompetitive justification for the tools.

Q: How robust are the main results? A: The main estimates are robust across a wide range of specification checks, including alternative winsorization levels, log-difference and binary (>10% deviation) dependent variables, heteroskedasticity-robust standard errors, exclusion of controls, inclusion of firm fixed effects, exclusion of tipping positions, restriction to Searched positions only, dropping SOC reweighting, and age restrictions. Two additional pieces of evidence corroborate the quasi-experimental findings: a survey experiment with SHRM HR managers shows that hypothetical benchmarks compress stated salary offers from both above and below; and quasi-random benchmark shocks (when large firms abruptly raise a position’s base salary by 10% or more) cause firms with tool access to converge to the new benchmark faster than firms without access.

Q: What does the survey of HR managers reveal about how firms use benchmarks? A: In a survey of 2,696 HR professionals conducted through SHRM’s research panel, 87.6% of those involved in salary-setting report using salary benchmarks. The vast majority (97.4%) use benchmarks to set pay for new hires. The most popular sources are industry surveys (68.0%) and free online data (58.1%), with payroll data services used by 23.2%. The median salary is ranked the most important benchmark statistic by 56.73% of respondents. Most respondents apply filters by state (84.15%) and industry (87.33%) when using the tool.

Q: What are the main sources of potential attenuation or amplification bias in the estimated effects? A: Attenuation bias may arise because (1) the benchmark tool studied is among the most advanced available, so firms already had some wage information from other sources, meaning the estimates capture only the incremental effect of one additional high-quality source; and (2) not all positions at treatment firms were searched, so the sample is restricted to positions where firms actually engaged with the benchmark. Potential upward bias could arise if firms adopting the tool were also undergoing broader HR system changes, but the flat event-study pre-trends argue against this explanation.

Salary Benchmarking: The practice of using aggregated market pay data — provided by third parties such as payroll processors, consulting firms, or online platforms — to identify typical salaries for specific job titles and set internal pay accordingly. In the paper’s context, this refers specifically to an online tool that allows employers to look up the median and distributional statistics of base salaries for standardized position titles, filtered by industry and state.

Aggregate Uncertainty: The paper’s label for a distinct source of information friction in which firms are uncertain about the distribution of wages offered by other firms in the market — as opposed to uncertainty about individual worker characteristics. This uncertainty is assumed to be the primitive that generates equilibrium wage dispersion in the model, and its resolution through benchmarking is the mechanism driving the empirical results.

Salary Dispersion (around the benchmark): Measured empirically as the average absolute percentage difference between a new hire’s starting base salary and the median market benchmark for that position, expressed in percentage points. This is the paper’s primary outcome variable. Dispersion reflects firms’ deviation from the market rate in either direction.

Compression from Above / Compression from Below: Compression from above refers to the reduction in salaries at firms that would otherwise have paid more than the median benchmark after gaining benchmark access. Compression from below refers to the increase in salaries at firms that would otherwise have paid less than the median benchmark. Both directions of adjustment are documented empirically and are predicted by the model.

Searched / Non-Searched / Non-Searchable Positions: The paper’s classification of new hires into three groups for identification purposes. Searched positions are those at treatment firms for which the firm actually looked up the benchmark. Non-Searched positions are at treatment firms but were not looked up, serving as a within-firm control. Non-Searchable positions are at control firms with no tool access, serving as a cross-firm control.

Affiliation (across firm values): A technical condition borrowed from auction theory (Milgrom and Weber, 1982) used in the paper’s model to characterize the correlation structure of firms’ private valuations of filling a position. Affiliation implies that when one firm has a high value, others are also more likely to have high values, and hence to offer high wages — generating the model’s equilibrium wage dispersion.

Procompetitive Effect of Benchmarking: The paper’s term for the welfare-improving property of salary benchmarks identified in the model: by resolving aggregate uncertainty, benchmarks cause the marginal firm to offer closer to the full-information competitive wage, reducing extraordinary profits that arise from informational rents and raising the mean salary in equilibrium. This is the key concept in the paper’s contribution to the antitrust policy debate.

When is TSLS Actually LATE?

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks: when does two-stage least squares (TSLS) with covariates actually estimate a local average treatment effect (LATE) — a non-negatively weighted average of causal effects for compliers only? The authors show that the answer is: almost never in practice.

The paper’s central theoretical result (Theorem 1) is that a linear IV estimand is weakly causal — meaning it cannot have the wrong sign relative to all underlying treatment effects — if and only if the IV specification has “rich covariates,” defined as the condition that the linear projection of the instrument onto the covariates, L[Z|X], equals the true conditional mean E[Z|X] at every covariate value. Saturated specifications (nonparametric covariate control) always satisfy rich covariates. Outside of two special cases — saturated covariates or an instrument that is mean-independent of covariates — rich covariates is an implicit parametric assumption that can fail.

When rich covariates fails, the TSLS estimand is “level dependent”: it depends not only on treatment effects for compliers but also on the levels of potential outcomes for always-takers and never-takers, some of which receive negative weight. The problem arises mechanically because the numerator of the IV estimand, E[Y Z̃], contains a term E[E[Y|X] E[Z̃|X]] that reflects untreated-outcome levels rather than causal contrasts. This term vanishes only when E[Z̃|X] = E[Z|X] − L[Z|X] = 0, i.e., rich covariates.

To document how common this failure is in practice, the authors surveyed 122 empirical IV papers published in five top economics journals (JPE, AER, QJE, ReStud, Econometrica) between January 2000 and October 2018. Of the 99 papers using TSLS with covariates, only 5 used a saturated specification at any point and only 1 (Chamberlain and Imbens 2004) used saturated specifications exclusively. Nearly a third of TSLS-with-covariates papers explicitly invoked the LATE interpretation; none reported a test of rich covariates.

The paper applies these findings to thirteen empirical studies. In Card (1995), the original IV estimate of returns to education is 0.132; the Ramsey RESET test overwhelmingly rejects rich covariates, and a DDML estimate of the weakly causal quantity β_rich is modestly smaller, with a relative specification bias of roughly 8% and the gap between β_iv and β_rich representing about 21% of the OLS–IV gap. In Nunn and Wantchekon (2011), the IV estimate of the slave trade’s effect on trust is nearly four times as large as the DDML estimate; after reestimation, the null of no effect would not be rejected at conventional significance levels. In Dube and Harish (2020), the DDML estimate of β_rich is about 20% smaller than the original IV estimate (roughly 40% of the OLS–IV gap) and is no longer significantly different from zero at conventional levels.

The paper also shows that Abadie’s (2003) kappa-weighting approach fails under the same necessary condition: it is weakly causal if and only if rich covariates holds, at which point it is numerically identical to standard IV — leaving no reason to use it. Monte Carlo simulations calibrated to Card (1995) show that saturated specifications can exhibit substantial finite-sample bias when the covariate support is large relative to the sample, while DDML partially linear IV (PLIV) converges to β_rich with decreasing bias as sample size grows.

The authors conclude that two conditions are jointly necessary for TSLS to be interpretable as a non-negatively weighted average of LATEs: (i) rich covariates, and (ii) a first-stage flexible enough to capture any covariate-varying direction of monotonicity. Both conditions fail routinely in published work. The recommended alternatives are: DDML PLIV for estimating β_rich (a weakly causal weighted average of conditional LATEs), or instrument propensity score weighting / Abadie kappa with correctly estimated E[Z|X] for estimating the unconditional ACR/LATE. The Ramsey RESET test is offered as a practical diagnostic for rich covariates violations, and it detected sizable discrepancies in each of the thirteen applications examined.

Q: What is the paper’s central theoretical result? A: Theorem 1 establishes that, given conditional exogeneity and monotonicity, the linear IV estimand β_iv is weakly causal — i.e., cannot systematically misrepresent the sign of treatment effects — if and only if the IV specification has rich covariates (L[Z|X] = E[Z|X] for every covariate value x). Rich covariates is therefore simultaneously sufficient and necessary; the sufficient direction was a special case of Kolesar (2013), while the necessary direction is novel to this paper.

Q: What does “rich covariates” mean and when is it satisfied? A: Rich covariates means that the linear projection of the instrument onto the included covariates exactly reproduces the instrument’s true conditional mean at every point in the covariate support. It is automatically satisfied in two cases: when covariates are specified saturatedly (with an indicator for each covariate cell), or when the instrument is mean-independent of all covariates so E[Z|X] is a constant. Outside these cases, rich covariates is an implicit parametric functional form assumption.

Q: What goes wrong when rich covariates fails? A: When L[Z|X] ≠ E[Z|X], the IV estimand becomes “level dependent”: it depends not only on treatment effects (causal contrasts) but also on the levels of potential outcomes for always-takers and never-takers. Because always-takers always receive Y(1) and never-takers always receive Y(0), the estimand picks up these levels through the term E[E[Y|X] E[Z̃|X]], which is nonzero whenever E[Z̃|X] = E[Z|X] − L[Z|X] ≠ 0. This can cause β_iv to be negative even when all complier and always-taker treatment effects are positive.

Q: How is the paper’s critique different from the two-way fixed effects (TWFE) literature? A: The TWFE literature (Goodman-Bacon 2021; Sun and Abraham 2021) identifies negative-weight problems arising from heterogeneous treatment effects due to cohort timing, but those estimands are not level dependent. By contrast, the TSLS problems identified here involve level dependence and persist even under constant, homogeneous treatment effects (Proposition 5), making the critique more fundamental and harder to dismiss by assuming effect homogeneity.

Q: Does the problem disappear if treatment effects are constant? A: No. Proposition 5 shows that rich covariates remains necessary for β_iv to be weakly causal even under Assumption CLE (constant, linear treatment effects). Level dependence occurs whenever E[Z̃|X] ≠ 0, regardless of effect heterogeneity. The only additional assumption that can substitute is Assumption LIN (linear potential outcome means), which together with constant effects implies β_iv = Δ exactly (Proposition 6), but this combination is a strong parametric restriction.

Q: What does the survey of empirical papers find? A: Of 122 IV papers in top journals from 2000–2018, 112 used TSLS, and 99 of those included covariates. Of the 99, only 5 (about 5%) used any saturated specification, and only 1 used saturated specifications exclusively. About a third of TSLS-with-covariates papers explicitly invoked the LATE interpretation. No papers reported a test of rich covariates such as the Ramsey RESET test.

Q: What happens in the Card (1995) returns-to-education application? A: The original linear IV estimate of the return to education is 0.132. The RESET test overwhelmingly rejects the null of rich covariates. The DDML estimate of β_rich is modestly smaller, with a relative specification bias of about 0.076 (roughly 8%). The gap between β_iv and β_rich represents about 21% of the OLS–IV gap, which the authors characterize as a sizable fraction of the “selection bias” corrected by IV. The DDML estimate of the unconditional ACR/LATE (β_acr) is roughly half the size of β_rich.

Q: What happens in Nunn and Wantchekon (2011)? A: The RESET test overwhelmingly rejects rich covariates. The IV estimate of the slave trade effect on trust is nearly four times as large as the DDML estimate of β_rich. After reestimation, the null hypothesis that the slave trade had no impact on trust levels would not be rejected at conventional significance levels, reversing the paper’s central finding.

Q: What happens in Dube and Harish (2020)? A: The RESET test overwhelmingly rejects rich covariates. The DDML estimate of β_rich is about 20% smaller than the original IV estimate, representing roughly 40% of the OLS–IV gap. While estimated with similar precision, the DDML estimate is no longer significantly different from zero at conventional significance levels.

Q: Does Abadie’s (2003) kappa-weighting approach solve the problem? A: No. Proposition 7 shows that the kappa-weighted estimand β_abadie is weakly causal if and only if rich covariates holds. Moreover, when rich covariates holds, β_abadie is numerically identical to β_iv, so kappa weighting provides no additional benefit. When rich covariates fails, kappa weighting is not weakly causal for the same reason as standard IV.

Q: What does the Monte Carlo simulation show about practical alternatives? A: The simulation, calibrated to Card (1995) data with covariates (experience, region indicators), shows that: a linear IV specification without rich covariates converges to β_iv = 0.660, decomposed as +0.391 from positively-weighted compliers, +0.614 from positively-weighted always-takers, and −0.345 from negatively-weighted always-takers — when the true weakly causal quantity β_rich = 0.430. Saturated specifications converge to β_rich but exhibit substantial bias at small sample sizes relative to covariate support. DDML PLIV converges to β_rich with bias decreasing in sample size, making it the recommended practical estimator.

Q: What is the relationship between this paper and Sloczynski (2020, 2024)? A: Sloczynski (2020, 2024) maintains rich covariates as an assumption and shows that TSLS can still fail to be weakly causal if monotonicity direction varies with covariates and the first stage omits instrument-covariate interactions. This paper focuses on the necessity of rich covariates itself, under strong (unconditional) monotonicity. Taken together, the two papers establish that both rich covariates and a sufficiently flexible first stage are jointly necessary for TSLS to be interpretable as a non-negatively weighted average of LATEs.

Q: What practical recommendations do the authors offer? A: The authors recommend: (1) always running the Ramsey RESET test to check rich covariates, implementable in Stata or R; (2) if using a binary instrument, checking that fitted values L[Z|X] lie in [0,1], necessary for rich covariates; (3) using DDML PLIV to estimate the weakly causal β_rich nonparametrically; and (4) for binary instrument/treatment, using instrument propensity score weighting (e.g., Sloczynski et al. 2024) or Abadie kappa with correctly estimated E[Z|X] to target the unconditional ACR/LATE. All recommended methods are available in mature Stata or R packages.

Rich covariates: The condition that the linear projection of the instrument Z onto the included covariates X, denoted L[Z|X], exactly equals the true nonparametric conditional mean E[Z|X] at every point in the covariate support. This is both necessary and sufficient for the linear IV estimand to be weakly causal under exogeneity and monotonicity. It is automatically satisfied by saturated covariate specifications or when the instrument is mean-independent of covariates; otherwise it is an implicit parametric assumption.

Weakly causal estimand: An estimand β is weakly causal if, whenever all subgroup- and covariate-specific treatment effects have the same sign, β has that sign too. This is an intentionally minimal requirement — it merely asks that the estimand not be systematically misleading about the direction of causal effects. An estimand can be weakly causal and still be difficult to interpret as a specific population parameter.

Level dependence: The phenomenon in which a linear IV estimand depends not only on treatment effects (causal contrasts μ_j(g,x) − μ_{j−1}(g,x)) but also on the levels of potential outcomes (the baseline μ_0(g,x) terms). Level dependence arises when E[Z̃|X] = E[Z|X] − L[Z|X] ≠ 0, causing the always-taker and never-taker potential outcome levels to enter the estimand and potentially reverse its sign.

Local average treatment effect (LATE): The average treatment effect for the subpopulation of compliers — those whose treatment status is changed by the instrument. In the binary treatment, binary instrument case, LATE = E[Y(1) − Y(0) | T(1) > T(0)]. LATE has a concrete counterfactual interpretation and is non-negatively weighted by construction; the paper asks under what conditions TSLS actually estimates a weighted average of LATEs.

Partially linear IV (PLIV) / DDML: A modification of classical linear IV in which the linear function of covariates is replaced by an unknown nonparametric function, estimated using machine learning methods (random forests, gradient boosted trees, neural networks) with cross-fitting, as in Chernozhukov et al. (2018). The coefficient on treatment in the PLIV model equals β_rich, the weakly causal IV estimand that would result if rich covariates were exactly satisfied.

Unconditional average causal response (ACR): When the instrument is binary, ACR = E[Y(T(1)) − Y(T(0)) | T(1) > T(0)], which reduces to the unconditional LATE when treatment is also binary. ACR differs from β_rich because β_rich places extra weight on covariate values with more instrument variation, while ACR weights compliers equally regardless of covariate-specific instrument variance. The paper documents that DDML estimates of β_acr can be roughly half the size of β_rich.

Saturate and weight (SW) specification: The TSLS specification proposed by Angrist and Pischke (2009, Theorem 4.5.1), in which both covariates and instrument-covariate interactions are fully saturated as excluded variables in the first stage. SW is guaranteed to satisfy rich covariates and, under weak monotonicity allowing direction to vary with covariates, produces a non-negatively weighted average of covariate-specific LATEs. It was used by only one paper (Chamberlain and Imbens 2004) in the authors’ survey of 99 empirical IV papers.

Review of Economic Studies | Macro Paper Warehouse

A Model of Multiple Hypothesis Testing

A Robust Test for Weak Instruments for 2SLS with Multiple Endogenous Regressors

In depth

Q1. What is the key gap in the existing weak instrument testing literature that this paper fills?

Q2. What is the test statistic and what are its two bias criteria?

Q3. What extensions are provided for individual coefficient testing?

Q4. What does the empirical application show?

Key concepts

A Temporary VAT Cut as Unconventional Fiscal Policy

In depth

Q1. What is the ex-ante identification strategy, and what does it identify?

Q2. What is the ex-post identification strategy, and how does it address endogeneity?

Q3. Why does the response increase with the durability of the good?

Q4. Why was the VAT cut effective despite the concurrent COVID-19 shock?

Q5. Why is a HANK model appropriate, and what does durable heterogeneity add?

Q6. What is the impact consumption multiplier, and why is it larger at the ELB?

Q7. Why does the cumulative two-year multiplier fall below the impact multiplier?

Q8. Why is the VAT cut more powerful than a comparable interest rate cut?

Q9. What does the distributional evidence imply for fiscal stimulus design?

Key concepts

All Along the Watchtower: Military Landholders and Serfdom Consolidation in Early Modern Russia

In depth

Q1. What is the paper’s central argument about the origins of Russian serfdom?

Q2. What was the Tula defense line and why was it located where it was?

Q3. How large is the estimated effect of defense line proximity on serf concentration?

Q4. How do the authors address endogeneity of the defense line location?

Q5. What does the paper find about Domar’s labor-scarcity hypothesis?

Q6. What does the paper find about the Baltic grain trade hypothesis?

Q7. What is the evidence for the estate-size mechanism?

Q8. What is the textual evidence linking military petitions to the 1649 Law Code?

Q9. How does the timing of collective petitions relate to political crises?

Q10. What do the placebo tests show?

Q11. How persistent was the spatial distribution of serfdom after 1649?

Q12. What explains the persistence of serfdom beyond its original military rationale?

Q13. How does this paper’s explanation relate to Eastern/Western European institutional divergence?

Q14. What is the methodological contribution of the optimal invasion route algorithm?

Auctions with Frictions: Recruitment, Entry, and Limited Commitment

Bank Information Production Over the Business Cycle

Bank Information Production Over the Business Cycle

In depth

Q1. What is the precise definition of “bank information quality” used in this paper, and why is this measure preferred over alternatives?

Q2. How do the authors establish that the PD estimates contain genuine private information rather than merely reflecting publicly observable characteristics?

Q3. What is the baseline magnitude of the cyclicality finding, and how is it identified?

Q4. How does the split-sample analysis (above/below county-median unemployment) further characterize the cyclicality?

Q5. How do the authors distinguish endogenous information production from a purely exogenous improvement in information quality during downturns?

Q6. How do loan characteristics (size and LGD) relate to information quality, and how does this relationship evolve over the business cycle?

Q7. What does the tradeable versus nontradeable industry test contribute?

Q8. Do composition effects (changes in the pool of borrowers) account for the main findings?

Q9. What are the implications of countercyclical information production for monetary policy transmission?

Q10. How does this paper differ from the most closely related prior study (Becker, Bos, and Roszbach (2020))?

Key Concepts

Bridges

Catastrophes, Delays, and Learning

Choice and Opportunity Costs

Closing Gender Gaps Through Workplace Diversity: The Intergenerational Effects of World War I

Coarse Bayesian Updating

Competing under Information Heterogeneity: Evidence from Auto Insurance

Competition in a Spatially-Differentiated Product Market with Negotiated Prices

Competitive Advertising and Pricing

Contract Terms, Employment Shocks, and Default in Credit Cards

Layer 1 — Overview

In depth

Q1. Why is the interest rate elasticity of default (0.20) so much lower than prior estimates in the literature?

Q2. What mechanism explains why newer borrowers are entirely unresponsive to interest rate changes?

Q3. Why does increasing minimum payments raise short-run default but reduce long-run default?

Q4. How is the mass-layoff identification strategy designed and validated?

Q5. How does the paper account for informal employment when estimating the cash flow impact of job loss?

Q6. Does the cost of default deter borrowers from defaulting, and what is the cost?

Q7. Are the default treatment effects different across the interest rate and minimum payment interventions, or do they interact?

Q8. Are there spillover effects from the contract term changes onto other loans held by study participants?

Q9. Why does the effect of unemployment on default exceed the model’s predictions from cash flow alone?

Q10. How do the experimental results compare to what experts predicted?

Q11. Do the job displacement results generalize beyond the experimental sample?

Q12. What do the debt dynamics during the experiment reveal about the mechanisms for interest rate effects on default?

Key Concepts

Costly Multidimensional Screening

Counterfactual Analysis for Structural Dynamic Discrete Choice Models

Customer Acquisition, Business Dynamism and Aggregate Growth

De Gustibus and Disputes about Reference Dependence