American Economic Review | Macro Paper Warehouse

A Theory of Price Caps on Non-Renewable Resources

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

This paper asks what the optimal response of an exhaustible-resource producer is to sanctions in the form of a price cap, and how a sanctioning coalition should set the cap. The motivation is the $60-per-barrel cap on seaborne Russian crude imposed by the G7, EU and Australia in December 2022 (with $100/barrel for high-value and $45/barrel for low-value refined products), whose stated aim was to cut Russian revenue without triggering a global supply shock. The authors (two of whom were involved in designing the policy) argue that static models, frictionless Hotelling models, and truncated-supply-curve intuitions are all inadequate, and build a dynamic structural model.

Model setup: A petrostate extracts an exhaustible resource (reserves normalized to 1) whose price follows a Cox-Ingersoll-Ross (Feller square-root) process, estimated on monthly real oil prices 1973-2024 (deflated WTI), yielding long-run mean p̃=$76 (2024 prices), volatility ς=2.43, and mean reversion D=0.21 annually, implying a price half-life of ln2/D = 3.6 years and a right-skewed Gamma limiting distribution. Preferences are CRRA with γ=2 (baseline); marginal extraction cost M=$19/barrel (Osintseva 2021); real discount rate 3%; and non-oil income τ=2, implying commodity sales fund between 1/3 and 1/2 of state income. A two-period model first shows that sufficiently severe financial frictions (low saving returns, high borrowing rates, fixed participation costs Φ) make the producer endogenously live hand-to-mouth (Propositions 1-2), consuming oil proceeds directly; the infinite-horizon model takes this as given.

Main findings: (1) Even without physical adjustment costs, optimal supply is highly inelastic — supply falls sharply below $40/barrel and reaches zero just below $30 — matching Russia’s observed price-insensitivity. A novel decomposition attributes the shape to four forces: time-the-market, revenue-smoothing, precautionary, and non-homotheticity effects, with their balance governed by γ. (2) A perfect (universal, credible, permanent) price cap shifts the supply curve OUTWARD — the producer extracts MORE — because the cap removes price upside, making reserves less valuable (non-homotheticity) and, under market power, eliminating the point of restricting supply (a binding cap means cutting volume no longer raises price). (3) Consequently a binding perfect cap can LOWER and stabilize world prices, and the stabilizing benefit is LARGER the greater the producer’s market power (demand elasticity calibrated to 1/ϵ=0.25; short-run literature range [0.07,0.14]). (4) An imperfect (leaky and/or temporary) cap produces highly state-dependent behavior: when the market is already tight (reference price high, above ~$150/barrel in the calibration), the producer optimally ‘shuts in,’ cutting output toward the shadow-fleet capacity κ and selling only outside the cap — DESTABILIZING the market exactly when prices are high. With κ=0.01 (about one-third of normal extraction), a leaky cap reduces the welfare damage to the producer by about two-thirds relative to a perfect cap, even though contemporaneous profits fall up to 50% when shutting in. (5) The authors introduce a ‘sanctions possibility frontier’ trading producer harm v(p̄) against the excess probability of a price shock ϕ(p̄) (P(price>$120), ~12% historically). The optimal cap is HIGHER (less aggressive) the greater the leakage; preferences (weight λ) matter mainly at intermediate leakage. Policy corollary: effective enforcement is a precondition for setting a low cap.

In depth

Q1. What is the core conceptual contribution about how a price cap operates?

The paper argues a price cap is not a truncation of the existing supply curve but a fundamental change to the stochastic environment the producer faces. By capping prices at min{p,p̄}, it eliminates the upside of high prices, lowers the value of reserves, and reduces uncertainty. Because the environment changes, the policy rules must be recomputed rather than read off the pre-policy supply curve adjusted with a vertical segment above p̄.

Q2. Why does a perfect price cap make the producer extract MORE, counter to policymaker intuition?

Two mechanisms. First, the non-homotheticity effect: with outside income τ>0, less valuable reserves are depleted faster, so capping the price (which lowers reserve value) raises the extraction rate. Second, for a producer with market power, a binding cap removes the incentive to restrict supply — curbing volume no longer raises the (capped) price, rendering market power ineffective. The supply curve under a binding cap closely follows the no-volatility supply curve.

Q3. What are the four forces in the supply-curve decomposition and what governs them?

(1) Time-the-market: sell more when prices are high. (2) Revenue-smoothing: with γ>1 the income effect dominates, so the producer extracts more when prices are low/expected to rise to smooth revenue. (3) Precautionary: price volatility induces conservation (extract less today); found quantitatively small. (4) Non-homotheticity: a permanently less valuable resource (low or capped price) is extracted faster, like greater impatience. Their balance is governed by preferences, specifically γ (inverse IES). Higher γ strengthens revenue-smoothing and weakens time-the-market; as γ→0 the model collapses to the frictionless Hotelling benchmark with infinitely elastic supply.

Q4. What is the empirical evidence presented, and what is the identification?

Section 2.5 tests whether financially constrained producers have more inelastic supply. Using 53 OPEC supply-news announcements 1984-2017 (from Känzig 2021) as price shocks, the authors examine production changes in 70 non-OPEC countries in the month after versus before each announcement. The dependent variable is the change in log production, sign-flipped so that producing more when prices fall (or less when prices rise) counts negatively. Regressing on the share of years a country had above-median debt-to-GDP yields a negative coefficient of -0.026 (std err 0.010), consistent with financially constrained countries having more inelastic supply. A country-risk-premium measure (Damodaran 2022) gives a similar but noisier result. Identification rests on OPEC announcements being exogenous price-news shocks to non-OPEC producers; threats include the announcements not being clean exogenous shocks and the debt-to-GDP dummy proxying other country characteristics — the paper treats this as motivating, not causal-structural, evidence.

Q5. How does the model incorporate market power and how is it endogenous?

World demand is isoelastic: pw=δ(r+y)^(-ϵ), where r is stochastic rest-of-world residual supply, y is producer output, and 1/ϵ is demand elasticity. The effective elasticity εD=ϵ·y/(r+y) depends on the producer’s market share, so market power evolves endogenously with past extraction (Cournot intuition). Market power makes the producer more conservationist in normal times, exerting upward price pressure. 1/ϵ is set to 0.25; the process for r is estimated by simulated method of moments so the laissez-faire equilibrium price matches the estimated oil-price process.

Q6. How is the ’leaky’ cap modeled and what is the shut-in strategy?

A shadow-fleet parameter κ∈[0,1] is the fraction of reserves exportable outside the cap per unit time (κ=0 is a perfect cap). With market power plus leakage, when the market is tight and prices are high, the producer optimally cuts output toward κ, selling only outside the regime at elevated prices (‘shut-in’). In the calibration with κ=0.01 (about a third of normal extraction), shut-in to κ is optimal when prices exceed ~$150/barrel; between $60 and $120 the cap still expands supply. So the cap stabilizes near the $76 long-run average but destabilizes when prices are already high.

Q7. What is the welfare and profit impact of a leaky cap?

Shutting in is not driven by higher contemporaneous profits — those fall by up to 50% relative to a perfect cap unless prices already exceed ~$150 — but by a more spread-out production profile that raises intertemporal welfare. Producer welfare rises with κ. Quantitatively, a leaky cap with κ=0.01 reduces the welfare damage inflicted on the producer by about two-thirds relative to a perfect cap, showing leakage sharply blunts the sanction.

Q8. How is cap non-credibility (temporariness) modeled?

Cap removal is a Poisson event with intensity λ, so duration is exponentially distributed. With a perceived 50% probability of removal within the first year, λ=0.69. Expecting the cap to be temporary makes the producer more inclined to shut in and keep barrels underground for extraction after removal, reinforcing the shadow-fleet mechanism and further weakening the cap’s stabilization effect; intertemporal welfare effects are significantly diminished.

Q9. What is the sanctions possibility frontier and how is the optimal cap chosen?

The policymaker minimizes v(p̄)+λ·ϕ(p̄), where v is proportional producer welfare loss from the value function and ϕ is the excess probability of an oil shock (P(pw>$120), baseline ~12% matching history). For each leakage level κ, the sanctions possibility frontier maps achievable (v,ϕ) combinations across cap levels. With a perfect cap the frontier is upward-sloping (no trade-off) and the optimum is the lowest cap above marginal cost. With leakage it becomes downward-sloping, creating a trade-off, and the frontier steepens as κ rises. Example: at κ=1/6, a cautious policymaker (λ=2) picks $55/barrel while an aggressive one (λ=1) picks $20; as leakage grows both converge to about $100. The optimal cap rises with leakage; preferences matter mainly at intermediate leakage.

Q10. How does this paper relate to and differ from prior work?

It contrasts with the frictionless Hotelling (1931) model (perfectly elastic supply) and with Anderson, Kellogg & Salant (2018), who derive inelasticity from geological well-pressure constraints — here inelasticity comes instead from financial frictions and market power. It differs from Stiglitz (1976), who found market power irrelevant to extraction quantity, because of positive marginal costs, financial frictions, and non-oil income. It complements empirical work (Babina et al. 2023 on market fragmentation and discounts), Salant (2023) on pre-announcement, Sappington & Turner (2023, static Cournot), Wachtmeister et al. (2023, quantitative), and Cardoso et al. (2024, endogenous shadow fleet). No separate drilling decision is modeled, for parsimony.

Q11. What robustness checks are reported?

Results are robust to: (a) excluding US/UK from the cross-country regression or using a 6-month horizon; (b) using the Damodaran country-risk-premium measure; (c) an alternative increasing, L-shaped marginal-cost curve with a 3% capacity constraint (Rystad/Wachtmeister data, M(y)=1.5+sqrt(0.25/(0.03-y))) — all conclusions hold, except predicted extraction is capped at the 3% capacity limit; and (d) HARA utility (nesting CRRA and CARA), available on request. The constant-marginal-cost main specification is chosen because it more clearly exposes the incentive to increase extraction (medium-term view).

Q12. What are the scope conditions and caveats on the policy conclusions?

The stabilizing-cap result requires the cap to be ’not too leaky’ and credible. The destabilizing shut-in only kicks in at high reference prices (above ~$150 in calibration). The financial-frictions/hand-to-mouth assumption is motivated by sanctioned petrostates specifically (frozen reserves — $300bn of Russian central-bank reserves frozen — sanctioned banks, war financing); it may apply less to unconstrained producers. The model is partial equilibrium (no general-equilibrium world economy, no strategic multi-state interaction, no endogenous shadow-fleet investment in the main analysis), and abstracts from storage and from a separate drilling margin. The policymaker objective is assumed linear in (v,ϕ).

Key Concepts

Price cap (as a tool of statecraft): In this paper, a sanction that lets the producer sell only at or below a ceiling p̄ when using coalition-controlled services, so the price received is pr=min{p,p̄}. Crucially it is interpreted not as a truncation of the supply curve but as a fundamental change to the stochastic environment, eliminating price upside and reducing reserve value and uncertainty.

Endogenous hand-to-mouth behavior: The result (Propositions 1-2) that sufficiently severe financial frictions — low saving returns, high borrowing costs, and/or fixed participation costs Φ — make the producer optimally consume oil proceeds period-by-period without using financial markets, regardless of its preferences. This is taken as the operating assumption for the dynamic model.

Non-homotheticity effect: With outside (non-oil) income τ>0, a permanently less valuable resource — whether from a low permanent price or a binding cap — is extracted faster, because reserve depletion is a less threatening prospect. It makes the producer behave as if more impatient and is a key driver of the outward supply shift under a cap.

Shut-in strategy: Under a leaky cap with market power, the producer sharply cuts extraction toward the shadow-fleet capacity κ when prices are already high, selling only outside the cap at elevated prices. It lowers contemporaneous profits (up to 50%) but raises intertemporal welfare via a more spread-out production profile; it destabilizes the market precisely when it is tight.

Shadow fleet / leakage (κ): The fraction of reserves the producer can export outside the cap regime per unit time (κ∈[0,1]); κ=0 is a perfect cap. For Russia it represents non-coalition tanker/insurance capacity; the paper notes the share of Russian oil outside the cap rose from about 20% (April 2022) to 67% (August 2024).

Sanctions possibility frontier: A novel menu, for each leakage level κ, of the achievable combinations of damage inflicted on the producer (v) and the probability of an oil-market shock (ϕ) across cap levels. Upward-sloping under a perfect cap (no trade-off; pick lowest cap), it becomes downward-sloping and steeper under leakage, making the optimal cap preference-dependent and increasing in leakage.

Reference price: The hypothetical equilibrium price that would prevail if the producer did not exercise market power — a monotone transformation of the state variable rt. It measures market tightness cleaned of the sanctioned producer’s endogenous decisions, and the cap’s price-lowering effect is larger when the reference price is high.

Market Opacity and Fragility: Why Liquidity Evaporates When It Is Most Needed

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: The paper asks why market liquidity sometimes behaves in a stabilizing way (an illiquidity hike curbs liquidity demand and attracts liquidity supply) but on other occasions “evaporates when it is most needed,” degenerating into a disorderly run for the exit and a flash crash, often with no fundamentals news. Motivated by flash events (the May 6, 2010 US flash crash where the Dow Jones fell about 9% intraday; the October 15, 2014 Treasury crash; the August 24/25, 2015 ETF freeze; the 1987 crash; and the COVID-19 Treasury market dislocation), Cespa and Vives argue that lack of transparency about order flow is a key ingredient that can jam the “rationing” function of the cost of trading.

Model setup: It is a stylized, two-period (trading rounds) rational-expectations model with no noise traders and no asymmetric information about payoffs — only about order flow. A single risky asset (liquidation value v ~ N(0, 1/tau_v)) is traded by competitive CARA agents. There are risk-averse dealers with risk tolerance gamma: a mass mu in [0,1] of “full” D-dealers present in both periods and 1-mu “restricted” RD-dealers present only in period 1; both post price-contingent (limit) orders. Overlapping unit-mass cohorts of risk-averse hedgers (risk tolerance gamma_H) receive independent endowment shocks u_t ~ N(0, 1/tau_u) in a non-tradable, perfectly correlated security and submit MARKET orders. Second-period hedgers observe a noisy signal s_u1 = u1 + eta of the first-period order imbalance, with eta ~ N(0, 1/tau_eta); tau_eta indexes transparency (infinity = full transparency, 0 = full opacity). The authors solve for linear equilibria and introduce a novel total-illiquidity measure, the Weighted Average Price Impact (WAPI), which volume-weights the heterogeneous price impacts of u1, u2, and eta.

Main findings and mechanism: Under full transparency, second-period hedgers can perfectly infer u1, face no price (execution) risk, and supply liquidity via contrarian marketable orders (speculative aggressiveness b > 0); the price impacts of the two cohorts’ shocks (Lambda_2 and Lambda_21) are independent, liquidity demand slopes DOWN in trading cost, and the equilibrium is unique. Under opacity the signal is noisy (b = 0 under full opacity), Lambda_2 and Lambda_21 become strategic SUBSTITUTES, generating strategic complementarity in illiquidity that can produce MULTIPLE equilibria and make liquidity demand slope UP in trading cost. Multiplicity arises when 0 < tau_utau_v < gamma/(4(gamma+gamma_H)^3): three equilibria (two stable extremal, one unstable intermediate). Example with tau_u = 0.1, tau_v = 0.1, gamma = 1, gamma_H = 0.1: Lambda_2 in {8.96, 1.98, 0.12}, Lambda_21 in {0.12, 1.98, 8.96}, Lambda_1 in {0.0001-ish (10^-2), 0.43, 8.84}; with tau_u = 2 a unique equilibrium with Lambda_21 = Lambda_2 = 4.61, Lambda_1 = 2.34. Traders facing the LARGEST trading cost trade most intensely at equilibrium.

Quantitative comparative statics: An unanticipated, perceived-permanent rise in endowment-shock dispersion produces a flash crash raising WAPI by 44% (from 4.62 to 6.67) and price volatility by 70% (from 4.62 to 7.87); recovery restores the original equilibrium. Halving tau_v raises WAPI by 89% and price volatility by 138%; an 11% decline in gamma raises WAPI by 20% and volatility by 14% (the latter preserving a unique equilibrium — fragility without multiplicity). With restricted dealers, an 11% cut in mu (0.9 to 0.8) when transparency is low can plunge the market to the opposite equilibrium: Lambda_2 from 1.47 to 9.6 (a 653% jump) and WAPI from 5.7 to 10.3 (+80%); a 10% cut (mu 1 to 0.9) raises WAPI from 4.55 to 6.19 (+36%) without multiplicity.

Implications: When the equilibrium is unique, total welfare is increasing in transparency (tau_eta) and in the mass of always-present dealers (mu), with gains accruing to hedgers and a transfer away from dealers. This supports policies for cheaper, consolidated order-flow information (EU/UK consolidated tape; US Treasury post-trade transparency; the SEC February 2024 dealer rule), while flagging a trade-off: more transparency can erode dealer participation, particularly for riskier securities.

In depth

Q1. What is the core mechanism that turns a benign illiquidity hike into a liquidity rout?

Order-flow opacity. When second-period hedgers cannot observe the first-period endowment shock u1, the price impacts of the first- and second-period shocks (Lambda_21 and Lambda_2) become strategic substitutes: a higher Lambda_2 makes the price more driven by u2, raising cohort-1 hedgers’ execution risk and shrinking their liquidity demand (|a21| down), which lowers Lambda_21, which in turn lowers cohort-2 execution risk and boosts their demand (|a2| up), further raising Lambda_2. This self-reinforcing loop (formalized by an aggregate best-response Phi(Lambda_2) that is strictly increasing in Lambda_2) is the strategic complementarity that can yield multiple equilibria and fragility. Under transparency the loop is killed because Lambda_2 and Lambda_21 are independent.

Q2. How is this an ‘identification’/equilibrium-selection question rather than an empirical one?

This is a theory paper with no econometric identification. The analogue of ‘identification’ is equilibrium selection and the formal conditions for multiplicity. The sufficient conditions for fragility are: overlapping cohorts of risk-averse hedgers suffering endowment shocks and submitting market orders; enough opacity about period-1 order flow; and risk-averse dealers. The necessary condition for multiplicity is sufficiently strong strategic complementarity, which is increasing in opacity. The closed-form multiplicity region is 0 < tau_utau_v < gamma/(4(gamma+gamma_H)^3).

Q3. How does the model distinguish a ’liquidity dry-up’ from a ‘flash crash’?

Both arise when an unexpected shock (a jump in endowment-shock dispersion, i.e. a fall in tau_u, or a rise in dealer risk aversion / fall in gamma, or a fall in tau_v) pushes a market from a unique high-liquidity equilibrium into the multiplicity region and best-response dynamics attract it to a low-liquidity equilibrium. A dry-up is the transition to low liquidity; a flash crash is the same plus rapid recovery once the shock dissipates, all over a short interval. A shock to dispersion gravitates the market to the high-Lambda_2/low-Lambda_21 equilibrium; a shock to dealer risk aversion gravitates it to the low-Lambda_2/high-Lambda_21 equilibrium; in both, WAPI and price volatility rise.

Q4. What does the WAPI measure add and why is it needed?

Because period-2 price reacts with DIFFERENT impacts to u1, u2, and the signal noise eta (coefficients Lambda_21, Lambda_2, Lambda_22), no single price coefficient captures total illiquidity. WAPI is a volume-weighted average of these price impacts, with weights given by the expected absolute volumes from equilibrium responses (using E|z| = sqrt(2/pi)*sigma_z for normals). It is analogous to a volume-weighted spread for an order that walks the book. WAPI is shown to be U-shaped in transparency tau_eta, even though total welfare is monotonically increasing in tau_eta.

Q5. What is the role of the contrarian marketable order by second-period hedgers?

With good information on u1, second-period hedgers post a contrarian market(able) order (b > 0) that offsets the first cohort’s selling/buying pressure, providing additional risk-sharing, enhancing the market’s risk-bearing capacity, and rationalizing first-period hedgers’ decision to split their order across rounds. b is increasing in signal precision tau_eta. Under full opacity b = 0 because hedgers cannot predict the direction of the period-1 imbalance, so only dealers absorb the imbalance and risk-bearing capacity collapses.

Q6. What heterogeneity across equilibria and cohorts is documented?

At fragile (multiple) equilibria, trading costs are heterogeneous across cohorts: Lambda_2 and Lambda_21 are negatively correlated (one high, the other low). The cohort facing the HIGHEST market impact demands MORE liquidity (hedging intensity is increasing in the cost of trading it induces). Dealers speculate (consume liquidity) more aggressively in the most illiquid equilibrium — consistent with HFTs stepping up liquidity demand during extreme moves (Brogaard et al. 2018; Bellia et al. 2022). The persistence parameter beta = Lambda_21/Lambda_2 equals 1 at unique/intermediate equilibria (random walk noise), and beta>1 is an indicator of multiple equilibria and fragility.

Q7. What are the welfare results and their scope conditions?

Restricted to the UNIQUE-equilibrium case (because with multiplicity hedger payoffs are complex-valued and cannot be ranked), and computed numerically with gamma = gamma_H = 1, tau_v = 1, tau_u = 2: total welfare TW(mu; tau_eta) is increasing in both transparency tau_eta and dealer mass mu. The gain is driven by higher hedger certainty equivalents (CEH_1, CEH_2); restricted dealers’ CE falls with tau_eta, and D-dealers’ CE falls with mu and (when tau_eta is not too small) with tau_eta. So transparency/dealer-presence policies raise welfare via a transfer from liquidity providers to consumers. A well-defined-payoffs condition is gamma_H^2tau_utau_v > 1 (which, when tau_eta=0 and mu=1, also implies a unique equilibrium).

Q8. What is the transparency-versus-dealer-participation trade-off?

More transparency spurs second-period hedgers’ speculation, eroding dealers’ profits, which in a free-entry sense raises effective entry costs and induces some dealer exit (lower mu). Keeping total welfare constant against rising tau_eta requires a smaller mu cut for riskier securities (tau_v = 1) than for safer ones (tau_v = 3). Hence moderate transparency increases can reduce always-present dealer mass and may hurt welfare, especially for risky securities. With low transparency, raising mu has a NON-MONOTONIC effect on fragility (can move from multiple to unique and back), so enhancing transparency — not just dealer presence — is the key tool to eliminate fragility.

Q9. How does the paper relate to and differ from prior fragility literature?

It departs on three dimensions: (i) the disruptive strategic complementarity is on the liquidity DEMAND side, not the supply side (unlike Brunnermeier-Pedersen 2009, Gromb-Vayanos 2002 funding constraints, Cespa-Foucault 2014, Cespa-Vives 2015); (ii) fragility relies on NO irrationality, noise trading, or exogenous demand/supply (unlike crash models of Gennotte-Leland 1990, Jacklin et al. 1992, Madrigal-Scheinkman 1997); (iii) asymmetric information is about the order flow, not payoffs. It also endogenizes an AR(1) noise-trading process whose persistence beta is determined in equilibrium. It supersedes the authors’ earlier working paper Cespa-Vives (2019).

Q10. How does the model map to fragmentation and OTC markets?

Trading rounds 1 and 2 can be reinterpreted as separate venues; opacity then captures the limited flow of order information across venues, and mu (always-present dealers) is a reduced-form proxy for fragmentation-related dealer presence. Results should hold a fortiori in fragmented OTC markets, which are more opaque than centralized ones. Unlike Chen-Duffie (2021), Malamud-Rostek (2017), and Manzano-Vives (2021) — where fragmentation can raise welfare via traders’ price impact — here traders are competitive, so those advantages do not arise.

Q11. What robustness and extension checks are reported?

The partially-opaque case (finite tau_eta) is studied numerically: one or three equilibria can arise, with multiplicity when transparency is low; b>0 and increasing in tau_eta dampens complementarity. The general model with restricted dealers and partial opacity is simulated (Figure 9 partitions (mu, tau_eta) into unique vs. multiple-equilibria regions). Remark 1 allows period-specific endowment variances (tau_u1, tau_u2) and confirms the substitutes logic; as tau_u1 to infinity the transparent solution is recovered. Internet Appendices cover a partially informative signal, comparative statics for tau_v and gamma_H, the AR(1) noise process, the case where first-period hedgers observe u2, and a ranking of hedging aggressiveness across regimes (Corollary 11).

Q12. What real-world episodes does the model claim to rationalize, and how is the empirical case made?

It is consistent with the May 6, 2010 flash crash, the 2015 ETF freeze (where uncertainty over ETF constituents sidelined arbitrageurs and the SPY-RSP spread reached 21 dollars at one point), and the COVID-19 US Treasury dislocation around March 12, 2020 (spreads up roughly tenfold and depth virtually disappearing, per Duffie 2023). Empirical support for non-standard liquidity provision via contrarian marketable orders is drawn from Brogaard et al., Biais et al. (2017), Anand et al. (2013, 2021). The paper itself runs calibrated simulations (normal-volatility tau_v=1,tau_u=2 giving ~30% return volatility per Yuan 2005; and a liquidity-crisis tau_v=tau_u=0.1 case) rather than original econometric estimation.

Key Concepts

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Monetary Policy without Commitment

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: Post-pandemic inflation across advanced economies rose to levels not seen since the early 1980s, reviving interest in central bank credibility. The standard quantitative macro models used to interpret this episode assume exogenous central bank reaction functions and inflation targets, which limits their usefulness. This paper instead makes monetary policy endogenous: a welfare-maximizing central bank that lacks the ability to commit re-optimizes every period. The goal is to characterize how lack of commitment shapes long-run inflation and transition dynamics, questions that prior credibility work (Barro-Gordon 1983; Rogoff 1985) could not address because it used static or log-linearized settings.

Model setup: The authors embed central bank lack of commitment into a standard fully non-linear New Keynesian model (not log-linearized around zero-inflation steady state). Monopolistically competitive firms set prices under Calvo rigidity: a random fraction 1-theta resets prices each period, the rest keep last period’s price. Wages are flexible; households choose consumption, labor, savings. The environment is deterministic with permanent unanticipated shocks. An exogenous proportional labor wedge tau (payroll tax capturing taxes, regulation, unionization) is assumed large enough (Assumption 1: tau > -1/sigma) that monopoly distortions persist. Two distortions operate: monopoly power (underproduction) and price dispersion from sticky prices (labor misallocation). The solution concept is Markov Perfect Competitive Equilibrium. Crucially, firms set prices BEFORE the central bank sets the interest rate, so the central bank takes the price distribution (hence dispersion D_t) as predetermined and optimally sets static welfare-maximizing policy: it eliminates monopoly distortions by setting the labor share to 1 (Y_t = D_t^{-1}). Equilibrium reduces to two difference equations: a forward-looking non-linear Phillips curve and a backward-looking price-dispersion law of motion, yielding a unique steady state. The analysis is conducted in a continuous-time limit for transition dynamics.

Main findings (with magnitudes and scope): (1) Long-run inflation is determined by the interaction of lack of commitment and the environment; steady-state inflation and price dispersion are strictly increasing in the labor wedge tau and strictly decreasing in the elasticity of substitution sigma (the dispersion comparative static in sigma holds for tau below a threshold tau-bar(sigma); the inflation comparative static is unambiguous). (2) Transitions to a higher-inflation steady state feature inflation OVERSHOOTING: inflation jumps on impact then gradually declines, because the central bank’s incentive to stimulate is largest early when dispersion/misallocation are low. (3) Quantitative magnitudes are large. Calibration (monthly): beta=(1.02)^{-1/12}, theta=0.86 (7-month price duration, Nakamura-Steinsson 2008), sigma=7 (Coibion et al. 2012), psi=2.5 (Chetty et al. 2011), tau=-0.1427 to target 2% annual inflation. A permanent 0.5% increase in the labor wedge raises steady-state inflation from 2% to 8.76%, with inflation overshooting to 10.11% on impact; it takes 12 months to decline within 25 basis points of the new steady state. A 0.5% decrease in sigma yields similarly large effects.

Implications: Welfare under inflation targeting strictly exceeds that under no-commitment in both shock scenarios; the welfare gain is about 6% in consumption-equivalent terms (targeting 0.981 vs no-commitment 0.922/0.921). The large magnitudes stem from a nearly vertical long-run Phillips curve (the labor share is insensitive to inflation when beta is near 1). Post-pandemic shocks (lower immigration raising the labor wedge; reduced globalization/supply-chain disruption lowering sigma) do not raise inflation on their own but do so through their interaction with central bank lack of commitment, and may make returning inflation to historic norms unlikely absent strict commitment to inflation targeting.

In depth

Q1. What is the identification/solution strategy, and what makes the model tractable?

This is a theory paper, so ‘identification’ is the equilibrium characterization rather than econometric identification. The authors solve for Markov Perfect Competitive Equilibria of a fully non-linear (not log-linearized) New Keynesian model. Tractability comes from the timing assumption: flexible-price firms set prices BEFORE the central bank chooses the interest rate. Because the equilibrium is Markov, the central bank at date t takes the price distribution (and hence future dispersion D_{t+1} and continuation value V(D_{t+1})) as predetermined; it cannot change future welfare off the equilibrium path. So it optimally maximizes STATIC welfare conditional on current dispersion, yielding the simple first-order condition Y_t = D_t^{-1} (labor share = 1). Equilibrium then reduces to two difference equations in inflation (forward-looking Phillips curve) and dispersion (backward-looking), giving a unique steady state. A key technical innovation is an auxiliary variable delta_t (the inverse of a discounted sum of future relative prices) capturing the passthrough of real wages to current inflation holding future inflation fixed, which itself has a recursive representation and is related to the slope of the Phillips curve.

Q2. What is the core economic mechanism generating higher long-run inflation under lack of commitment?

Starting from a steady state, a permanent rise in tau (or fall in sigma) increases monopoly distortions and would, under commitment, lower the labor share while keeping inflation fixed. But a no-commitment central bank wants to undo the rise in monopoly distortions by cutting interest rates and stimulating output to push the labor share back to 1. Flexible-price firms rationally anticipate this future stimulus, higher future labor demand, and higher future real wages, so they raise prices today to offset expected future costs. Sequential price increases raise price dispersion. The economy converges to a new steady state once rising dispersion reduces aggregate productivity (labor misallocation) enough that the central bank’s marginal benefit from cutting rates vanishes. Hence both long-run dispersion and inflation are permanently higher.

Q3. Why does inflation overshoot in the transition rather than monotonically rise?

Overshooting arises from the evolution of central bank incentives as dispersion rises along the transition. Early in the transition, dispersion and labor misallocation are low, so stimulating output to boost consumption is relatively beneficial; later, once dispersion/misallocation are high, the productivity cost of stimulation is high and the benefit falls. Flexible-price firms anticipate that monetary stimulus is front-loaded, so they front-load their price increases. The result is high inflation early that declines toward the new (lower but still elevated) steady-state level. In the phase diagram (dispersion-inflation plane, holding delta fixed), the dispersion-zero locus is upward sloping and the inflation-zero locus is downward sloping; the saddle path has negative slope, so along it inflation and dispersion move in opposite directions. A labor-wedge shock shifts the inflation-zero locus up (leaving the dispersion locus unchanged); inflation jumps to the new saddle path then declines as dispersion rises.

Q4. Why are the quantitative magnitudes so large?

The steady-state labor share is relatively insensitive to inflation because the positive effect of inflation on the labor share (via overhiring sticky-price firms) is largely offset by the negative effect via forward-looking flexible-price firms that raise prices to protect against future overhiring. Standard New Keynesian calibrations use high beta and low theta, so there is a large fraction (1-theta) of flexible-price firms that raise prices substantially, putting downward pressure on the labor share. Formally, the long-run Phillips curve linking labor share mu and inflation Pi (equation 33) becomes almost vertical when beta is near 1. A nearly vertical long-run Phillips curve means small changes in tau or sigma require large changes in inflation to keep mu unchanged. Implication: any change that flattens the long-run Phillips curve would shrink the magnitudes, lower the value of commitment, and imply meaningful benefits from positive long-run inflation.

Q5. What is the central bank’s reaction function and how does it compare to a Taylor rule?

Substituting the FOC Y_t = D_t^{-1} into the Euler equation gives 1 + i_t = (1/beta) * Pi_{t+1} * Y_{t+1} * D_t. This endogenously-derived rule resembles exogenous Taylor rules: the interest rate is increasing in expected future inflation and expected future output, and it also reacts to current price dispersion. Higher dispersion reduces labor productivity via misallocation, lowering the benefit of stimulating the economy, so the central bank raises rates. Like Atkeson, Chari, and Kehoe (2010), the central bank responds to off-equilibrium increases in inflation/dispersion by raising rates enough that an individual flexible-price firm would actually want lower price increases off the equilibrium path.

Q6. How does the comparative static differ between the labor-wedge shock and the elasticity-of-substitution shock?

Both raise long-run inflation and (generally) dispersion and produce overshooting. For inflation the comparative static is unambiguous in both cases. For dispersion, the tau result is clean (Dss strictly increasing in tau), but the sigma result requires a bound: Dss is strictly decreasing in sigma only for tau < tau-bar(sigma) (where tau-bar(sigma)=infinity if sigma<=2, else 1/(sigma^2-2sigma)), because sigma also enters the dispersion law of motion and could in principle make dispersion increase with sigma when tau is large. A second difference appears in the comparison with inflation targeting: under a tau shock, an inflation-targeting central bank keeps rates fixed, output falls permanently, and dispersion is unchanged. Under a sigma shock, sigma directly affects the dispersion-inflation relationship, so even under inflation targeting steady-state dispersion would decline (greater differentiation makes relative price differences a less important source of misallocation) and rates would adjust to facilitate the transition.

Q7. What is the welfare comparison and how is welfare measured?

Welfare is expressed in consumption-equivalent terms relative to an otherwise-identical flexible-price economy: how much consumption a household would require, right after the shock, to be indifferent between the sticky-price economy (under targeting or no-commitment) and a flexible-price economy with constant consumption and implied labor. For the labor-wedge shock: welfare under targeting 0.981 vs no-commitment 0.922 (difference 0.059). For the elasticity shock: targeting 0.981 vs no-commitment 0.921 (difference 0.060). In both cases targeting strictly dominates, with gains of about 6% consumption-equivalent. The intuition: targeting reduces the misallocation cost of long-run price dispersion, while no-commitment reduces the cost of rising monopoly distortions; the dispersion costs dominate, especially because high beta makes long-run costs weigh heavily.

Q8. How does this paper relate to and differ from prior work on credibility and non-linear monetary policy?

It extends the Barro-Gordon (1983) and Rogoff (1985) credibility tradition, which used static or linearized settings that cannot speak to long-run inflation or transition dynamics. It differs from Markovian linearized approaches (e.g., Halac and Yared 2022) which feature no transition dynamics and significantly OVERESTIMATE the effect of permanent shocks on long-run inflation (because linearization underestimates the welfare cost of rising dispersion). It departs from fiscal-commitment models (Alvarez-Kehoe-Neumeyer 2004; Aguiar et al. 2015) and from Davila-Schaab (2023, which uses quadratic adjustment costs and thus has no price dispersion) by emphasizing the Calvo dispersion cost and its dynamic feedback on the inflation-output tradeoff. Relative to the discretionary-multiplicity literature (Albanesi-Chari-Christiano 2003; King-Wolman 2004; Zandweghe-Wolman 2019), this model obtains a UNIQUE equilibrium and provides an analytical (not numerical) characterization of the steady state and transition. It also contributes a novel recursive representation of the non-linear Phillips curve via the auxiliary variable delta_t.

Q9. What are the transition dynamics of the macro variables in the calibrated exercise?

Following the permanent labor-wedge increase: inflation jumps up from 2% and gradually declines toward its higher steady state (overshooting). The nominal interest rate jumps up and continues rising throughout the transition (the higher steady-state nominal rate reflects the Fisherian effect present in the non-linear model). The real interest rate jumps DOWN initially (the central bank stimulates to weather the shock) then gradually returns to its original level. Output falls gradually as price dispersion and labor misallocation increase. Nominal wage inflation jumps up with price inflation but stays below it, converging from below; this gap underpins a permanent long-run decline in the real wage.

Q10. What are the policy implications and their scope conditions?

Permanent changes in the global economy (e.g., lower immigration shifting labor toward more regulated/higher-wedge sources; slower globalization or supply-chain disruptions raising domestic firms’ market power, i.e., lower sigma) can raise long-run inflation, but only through their interaction with central bank lack of commitment, not on their own. The post-pandemic inflation spike, and its overshooting, can be partly understood as the private sector rationally anticipating accommodative policy. Scope condition: this holds as long as the central bank operates with FULL DISCRETION; a strict commitment to inflation targeting would prevent it. There can therefore be significant benefits to institutions that enhance commitment. A caveat from the model’s own logic: if structural changes flatten the long-run Phillips curve, magnitudes shrink, the value of commitment falls, and there are real benefits to positive long-run inflation (so targeting too low an inflation rate would be costly).

Q11. What are the main caveats and directions for future research the authors flag?

The model is deterministic with permanent shocks and abstracts from monetary-fiscal interactions by assuming lump-sum taxes and Ricardian equivalence (debt is payoff-irrelevant, set to zero). It focuses on the stable steady state, setting aside equilibrium implementation and off-equilibrium inflation stability. The discretionary policy (labor share = 1) is invariant to the price-setting model, so the approach extends to menu-cost or rational-inattention models. Future work: relax Ricardian equivalence to study interactions between central bank and fiscal lack of commitment (facilitated by the framework not assuming a long-run debt level since it is not linearized), and examine off-equilibrium inflation stability.

Key Concepts

Remote Work and City Structure

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Monte, Porcher, and Rossi-Hansberg ask why remote work surged abruptly and permanently after COVID-19 despite information-technology advances raising it only marginally between 1980 and 2019, why the change was so heterogeneous across cities, and what the welfare consequences are. Their answer is a coordination mechanism: working downtown (the CBD) yields productive interactions with other in-office workers but entails commuting/congestion costs, while remote work avoids those costs but forgoes agglomeration benefits. Because workers do not internalize the spillovers they confer, a worker prefers the office only if others commute too — generating, in a dynamic discrete-choice model with idiosyncratic preferences and fixed switching costs, the possibility of MULTIPLE stationary equilibria with different permanent commuter shares. A temporary shock (the pandemic) that drives commuters near zero can then select the low-commuting equilibrium permanently.

The model is a dynamic monocentric city (disk-shaped, radially symmetric CBD, absentee landlords, Cobb-Douglas utility, Gumbel idiosyncratic shocks). Multiplicity arises (Proposition 4.3) when agglomeration forces are strong enough — the net strength delta + xi exceeds a threshold above theta + gamma/(2mu) — AND remote-work productivity relative to office productivity z/A lies in an intermediate “cone of multiplicity” (neither too low nor too high). The authors quantify city-specific parameters for U.S. CBSAs using pre-2019 data (Census/ACS 1980-2023, NLSY79 panel of 4,147 individuals 1998-2022, SafeGraph cell-phone mobility, Zillow ZHVI zip-code house prices). Estimation: transition elasticity s = 0.30 (elasticity of transitions into remote work = 3.09), fixed switching cost F = 1.78 (equivalent to giving up 83% of a year’s earnings); agglomeration externality delta with mean 0.067 (SD 0.022, 619 CBSAs); the amenity-vs-congestion difference xi - theta is statistically insignificant and set to zero.

Stylized facts. Predicted remote-work share (controlling for composition) rose in the ACS from under 1% (1980) to 2.6% (2019), jumped to 12% (2020), peaked at 15% (2021), and fell to 11% (2023); NLSY shows a parallel path (1.4% in 1998 to 3.7% in 2018, 9.2% in 2020, 7.8% in 2022). The remote-work wage premium rose steadily but did NOT jump post-2018: ACS discount of 44.5% in 1980 became a 6.5% premium by 2022; NLSY discount fell from 18.5% (2000) to 3.1% (2022). A stable premium alongside a sudden quantity jump argues against pure productivity/preference shocks.

Mobility/housing facts. All cities dropped to ~20% of pre-pandemic CBD trips in spring 2020 (about a 75% drop, unrelated to city size). Recoveries diverged: the 25 largest CBSAs (employment > 1.5M) stabilized at ~60% of January-2020 trips, while the 663 smallest (< 150K) returned fully to pre-pandemic levels by early 2021. New York and San Francisco stabilized near 40%; Madison, WI recovered fully. House-price distance gradients flattened ~0.01 everywhere by January 2021; the flattening persisted and stabilized around 0.095 by end-2024 in large cities but reversed in small ones.

Results and welfare. Of 278 estimated CBSAs, 208 were inside their cone of multiplicity pre-pandemic; larger cities are systematically more likely to be inside (probit on log employment significant). The cone indicator predicts trip shortfalls (R-squared 0.144 alone, retaining significance with controls) and gradient flattening. Welfare: comparing high- vs low-commuting stationary equilibria for the 208 cone cities, the loss from switching is positive but modest — mean 2.3%, median 2.2%, range 1.2% to 4.0% (Table 3). Average wages fall sharply (15-35%) but option-value and commuting-cost savings offset most of it; net strength delta - gamma/(2mu) predicts the loss with R-squared 0.85. Cities with trips at 60% or less of pre-pandemic levels have an average welfare loss of 2.7%.

In depth

Q1. What is the core economic mechanism, and how does it generate multiple equilibria?

Office work confers productivity spillovers and CBD amenity value that rise with the mass of in-office workers (L-tilde-c), but workers do not internalize these external benefits. So each worker prefers the office only if enough others commute. In a dynamic setting with idiosyncratic Gumbel preference shocks and fixed switching costs F, this coordination can produce multiple stationary equilibria: a high-commuting and a low-commuting one (with an unstable equilibrium E2 between them). Multiplicity requires (Prop 4.3) static agglomeration forces (delta + xi) above a threshold eta_min > theta + gamma/(2mu), AND relative remote productivity z/A in an intermediate interval Z — the ‘cone of multiplicity.’ If z/A is too low, the high-commuting equilibrium is unique; if too high, only the remote equilibrium survives.

Q2. What is the identification/quantification strategy and its main threats?

To avoid taking a stand on which equilibrium generated the data, the authors rely ENTIRELY on pre-2019 data (when every city was plausibly in the high-commuting equilibrium) and on model relationships that hold in any equilibrium. Four steps: (1) transition elasticity s and cost F from NLSY79 transition probabilities via a CCP/log-linear regression (eq. 21), using past wage ratios as an instrument for future ratios to address measurement error / forward-looking expectations (IV eta0 = -0.47, eta1 = 3.09); (2) agglomeration externality delta_j from commuter-wage changes instrumented by 1980 occupational composition interacted with economy-wide occupation-specific commuter-share changes (shift-share IV, eq. 26-28), with five industry groups; (3) remote/office productivity z_j, A_j from occupation-level remote-work premia (NLSY, 22 occupation groups) reweighted by city occupation shares; (4) transport-cost elasticity gamma_j from CBSA-specific housing rent-distance gradients (ACS block-group rents 2015-2019). Main threats: selection of workers into remote work on unobservables (addressed by NLSY individual fixed effects), endogeneity of commuter shares to local productivity shocks (addressed by the shift-share IV), and the assumption that all cities were in the high-commuting equilibrium in 2019; tau_j is calibrated to match each city’s 2019 Lc/L.

Q3. How do the authors rule out competing explanations (pure productivity/preference shocks, congestion, establishment size, occupational shift)?

National productivity/preference shocks: would be expected to leave some lasting imprint even in small cities, but small CBSAs reverted fully, and at least 34% of jobs remain teleworkable even in fully-reverting cities (Dingel-Neiman teleworkable share ranges 25-55% across CBSAs), so low telework capacity cannot explain reversion; cities with permanent 40%+ trip declines have only a modestly higher 43% teleworkable share. The wage premium shows no differential evolution across high- vs low-teleworkable occupations over the pandemic. Congestion: if congestion drove the shift, large cities should show lower CBD propensity pre-pandemic, but the opposite holds (30.6% of trips to CBD in large vs 15.6% in small CBSAs in late 2019). Establishment concentration: employment is LESS concentrated in smaller cities, so big-employer return-to-office decisions cannot explain reversion. Occupational shift: teleworkable employment share rose only ~5% post-pandemic, and rose MORE in smaller CBSAs (7.9%) than larger (5.8%) by end-2023, the wrong direction to explain the heterogeneity.

Q4. What heterogeneity across cities is documented and how does it map to the theory?

Large cities (high agglomeration, high net strength delta - gamma/(2mu), which rises with size: doubling size raises net strength ~0.004 off a mean 0.049) are disproportionately inside the cone of multiplicity (208 of 278 estimated cities in-cone; probit on log employment positive and significant). These cities show permanent CBD-trip declines (stabilizing ~60% for the 25 largest) and persistent gradient flattening (~0.095 by 2024). Small cities are mostly outside the cone, with unique equilibria, and revert fully. The cone indicator is also positively associated with delta_j and z_j/A_j and negatively with gamma_j, as the theory predicts.

Q5. What robustness checks are run?

Estimates of s and F are similar using restricted-use county-geocoded NLSY and under an alternative city-partition definition (two days/week remote). Main results are robust to lower delta_j and higher gamma_j calibrations (Appendix A.17). A CES production function in remote/in-person labor yields very large substitution elasticities, motivating the linear specification. An endogenous-housing-supply model yields a nearly identical rent gradient (because commuters were a high share of employment pre-2020). Office-trip-only versions of the mobility figures (workplace visits) show similar patterns. The cone indicator retains significance in Table 2 after adding teleworkable share, pre-pandemic CBD-trip share, industry value-added shares, and total employment; results hold for an alternative binary ‘returned to office’ indicator 1back(5,20). Multiple DYNAMIC equilibria were not found in numerical exercises (Appendix B.6).

Unlike Davis, Ghent & Gregory (2024) (remote productivity via adoption externalities), Parkhomenko & Delventhal (2024) (amenity value of remote work), and Duranton & Handbury (2023) (exogenous changes in who may work remotely), this paper does NOT rely on exogenous productivity or amenity/preference shocks to explain the large persistent jump. Instead a temporary commuter shock SELECTS among pre-existing multiple equilibria. Liu & Su (2023) document a falling urban wage premium for remote-amenable occupations (consistent with weaker agglomeration). The paper’s documented divergence of residential rent-distance gradients between large and small cities is, to the authors’ knowledge, a new fact, interpreted structurally. Owens, Rossi-Hansberg & Sarte (2020) similarly use coordination/residential externalities (Detroit neighborhoods).

Q7. What are the policy implications and their scope conditions?

Because the coordination failure operates partly OUTSIDE firm boundaries, individual firms’ return-to-office mandates may be insufficient to restore the high-commuting equilibrium. City-level interventions — taxing remote work or subsidizing commuting — could in principle move a city back, since the only active externality in the quantification is a positive agglomeration externality (implying too little commuting relative to the efficient benchmark in all equilibria). However, the authors stress these welfare effects and the effectiveness of policy remain open questions; their welfare numbers depend on estimation details and the abstraction from a system-of-cities with migration.

Q8. What are the main caveats and abstractions?

The model treats each city as a CLOSED economy: no inter-city migration, trade, or investment links, though the authors note large cities show a small differential population drop (Appendix A.9), attributed to low migration elasticities. Remote work is ‘partial’ with a FIXED fraction mu = 3/5 of days at home, not chosen. Occupational heterogeneity is abstracted from (justified by rare occupation transitions). The amenity (xi) vs congestion (theta) externalities are not separately identified and set to zero (difference insignificant). Spillovers are not internalized by firms in the model. The welfare ranking (high-commuting preferred) is intuited from the single positive externality rather than formally proven.

Q9. Why is there a discrepancy between the abstract’s welfare figures and per-city numbers?

The abstract and revised Table 3 report a mean welfare loss of 2.3% (median 2.2%, range 1.2%-4.0%) across the 208 cone cities, and state cities with permanently low commuting (60% or less of pre-pandemic trips) experience average losses of 2.3% (2.7% in the text). The introduction additionally quotes specific city losses (about 3.7% for Los Angeles and San Jose, 3.2% for New York, 2.8% for San Francisco, 2% for Phoenix); these are the largest cities and lie within or near the upper part of the distribution, consistent with welfare loss rising in net agglomeration strength (R-squared 0.85 of loss on delta - gamma/(2mu)).

Key Concepts

Self-Fulfilling Fluctuations in HANK Economies

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: A central tenet of monetary policy is that aggressively raising nominal rates more than one-for-one with inflation (the Taylor principle) nips self-fulfilling inflationary beliefs in the bud. That logic is built on Representative-Agent New Keynesian (RANK) models that abstract from inequality and incomplete markets. Acharya and Benhabib ask whether this central tenet survives in Heterogeneous-Agent New Keynesian (HANK) economies where idiosyncratic income risk is countercyclical, and they answer in the negative: no matter how aggressively monetary policy responds to inflation, such economies remain susceptible to self-fulfilling fluctuations (“endogenous demand shocks”).

Model setup: The paper builds an analytically tractable continuous-time HANK model. Tractability comes from quasi-linear preferences (linear in labor), which makes the economy block-recursive — aggregate output and inflation dynamics can be characterized independently of the wealth distribution. Households face a 2-state Poisson idiosyncratic productivity process (high ξh / low ξl, treating ξl loosely as “unemployment”), with the transition rate into the low state given by λl,t = λl·y^(−Θ); Θ > 0 makes risk countercyclical (Θ = 0 is acyclical). Firms are monopolistically competitive with a forward-looking (Rotemberg-type) Phillips curve. The baseline monetary rule is a simple inflation-targeting Taylor rule it = r + φπ·πt with φπ > 1, and crucially the model imposes NO effective lower bound, to distinguish the mechanism from liquidity-trap multiplicity (Benhabib-Schmitt-Grohé-Uribe 2001).

Key mechanism: With countercyclical risk, the “natural rate” r*(y) = ρ − σ·y^(−Θ) (defined Keynes-style as the real rate consistent with constant output, not the flexible-price rate) is endogenous and co-moves with output: dr*/dy = σΘy^(−(1+Θ)) > 0. A belief that output will fall raises perceived future risk, raises desired precautionary saving, and lowers the natural rate; if policy does not cut rates enough, real rate exceeds natural rate, spending falls, and the pessimistic belief is self-fulfilling.

Main results (with magnitudes/scope): (1) Local determinacy requires a cyclical-risk-augmented Taylor principle φπ > φ(Θ) = 1 + ρσγΘ/κ, valid only if risk is not too countercyclical, Θ < Θ* ≡ ρ/(σγ); if Θ > Θ* the targeted equilibrium is locally indeterminate for any finite φπ. (2) GLOBAL indeterminacy holds for ANY Θ > 0 and any finite φπ (Proposition 3): an untargeted steady state always coexists with the target, and depending on cyclicality, fluctuations take the form of a saddle connection (mildly countercyclical, Θ < Θ⋄), a stable limit cycle around the target (moderately countercyclical, Θ⋄ < Θ < Θ*), or local indeterminacy (highly countercyclical, Θ > Θ*). (3) Calibration (real rate 4%, γ⁻¹ = 2, λl = 0.013, ch/cl = 1.1 implying ξh/ξl = 1.23, φπ = 1.5) yields Θ⋄ ≈ 15.8 and Θ* = 31.08; empirical estimates from Bilbiie-Primiceri-Tambalotti (2023) put Θ in [21.98, 29.9] with mode 28.1 — comfortably in the moderately countercyclical region. At Θ = 28.1 the untargeted steady state has output about 6.5% below target, and the stable cycle has output-gap amplitude of roughly ±2.5% — magnitudes comparable to U.S./Euro-area post-Great-Recession gaps and U.S. business cycle fluctuations. (4) Policy fixes: a monetary rule that responds to the endogenous natural rate, it = r + φπ·πt + φr·(r*(xt) − r) with φπ > 1 and φr ≥ 1 (a “Taylor principle for natural rates”), delivers global determinacy (Proposition 4). Alternatively, a passive-monetary/active-fiscal regime (φπ < 1, φb ∈ [0,1)) eliminates all manifestations of indeterminacy via the Fiscal Theory of the Price Level (Proposition 5). Rules responding only to output, inertial rules, or escape clauses that merely remove the untargeted steady state (e.g., switching to strict inflation targeting if output falls below x̃ = −0.1) fail because the stable cycle survives.

In depth

Q1. What is the central claim and how does it overturn the RANK benchmark?

In RANK (or HANK with acyclical risk), the Taylor principle φπ > 1 delivers both local AND global determinacy because the IS curve has no higher-order terms. In HANK with countercyclical risk, the natural rate r*(y) = ρ − σy^(−Θ) co-moves with output. This adds a stabilizing first-order term (−σγΘx) to the IS curve requiring a stronger response for local determinacy (φπ > φ(Θ)), and adds stabilizing higher-order terms that no finite φπ can overwhelm — producing global indeterminacy for any Θ > 0. So aggressive inflation-fighting alone cannot anchor the economy.

Q2. How is the ’natural rate’ defined here, and how does it differ from standard usage?

The authors follow Keynes (1936): r*(y) is the real interest rate consistent with output remaining constant at level y. This differs from the standard New Keynesian definition (the flexible-price real rate r = ρ − σ). The two coincide in RANK, in HANK with acyclical risk, and at the steady state y = 1 (r = r*(1)), but DIVERGE when risk is countercyclical: there are many natural rates r*(y) — one per output level — while there is a single flexible-price rate r = ρ − σ. The flexible-price rate never depends on endogenous output; r*(y) does.

Q3. What distinguishes this source of multiplicity from prior determinacy literature?

Three distinctions. (1) Versus Benhabib-Schmitt-Grohé-Uribe (2001b) liquidity-trap multiplicity: the paper purposely imposes NO effective lower bound, so the ELB is not the driver — countercyclical risk is. (2) Versus the local-determinacy HANK literature (Acharya-Dogra 2020, Bilbiie 2024, Auclert et al. 2023, Ravn-Sterk 2021): those papers show a stronger ‘cyclical-risk-augmented Taylor principle’ restores LOCAL determinacy; this paper shows that same condition cannot rule out GLOBAL indeterminacy. (3) Versus Benhabib-Eusepi (2005) / older RANK global-indeterminacy work that relied on money-in-utility, money-in-production, or capital: this model is cashless and capital is not a factor of production, so the mechanism is genuinely the countercyclical risk.

Q4. How does the paper relate to Ravn and Sterk (2021), the only other HANK global-indeterminacy paper?

Ravn-Sterk (2021) study a HANK economy with search frictions and find an additional ‘unemployment trap’ steady state (100% unemployment) alongside the target. This paper’s characterization (two steady states) is complementary, but goes further by providing a COMPLETE analytical characterization of the dynamics through which countercyclical risk generates indeterminacy, and by analyzing which policy designs eliminate it. A key novel point: indeterminacy manifests not only as a second steady state but also as a stable cycle around the target, so policies that only kill the untargeted steady state can fail.

Q5. Why isn’t eliminating the untargeted steady state sufficient for global determinacy?

Because under moderately countercyclical risk a stable limit cycle surrounds the targeted steady state independently of the untargeted steady state. The paper shows an escape-clause rule that switches to strict inflation targeting (π = 0) when output falls below x̃ = −0.1 (i.e., more than 5% below target) does eliminate the untargeted steady state, yet trajectories near the target still diverge locally and then converge to the surviving stable cycle, remaining bounded. Hence only policies that neutralize ALL non-fundamental equilibria — not just the untargeted steady state — guarantee global determinacy.

Q6. What is the proposed monetary-policy fix and its scope conditions?

A rule it = r + φπ·πt + φr·(r*(xt) − r) with φπ > 1 and φr ≥ 1 (Proposition 4) delivers global determinacy for any Θ > 0. The intuition is a ‘Taylor principle for natural rates’: by committing off-equilibrium to move the nominal rate at least one-for-one with endogenous natural-rate fluctuations, policy undoes the precautionary-saving impulse so pessimistic/optimistic beliefs cannot be confirmed. Setting φr = 1 makes the nominal rate perfectly track r*(xt), analogous to the optimal RANK response to exogenous demand shocks. It is also related to Holden’s (2024) robust real-interest-rate rule.

Q7. What is the fiscal-policy alternative and the mechanism?

A passive-monetary/active-fiscal regime (φπ < 1, φb ∈ [0,1), Proposition 5) eliminates the untargeted steady state and the stable cycle for any Θ > 0, yielding a unique globally determinate equilibrium converging to x = π = 0, b = b*. Mechanism is the Fiscal Theory of the Price Level: with active fiscal policy, taxes do not rise enough to stabilize debt, so the price level must adjust to keep the real value of debt equal to the present value of future primary surpluses. A permanent-recession (deflationary) belief would raise real debt and eventually violate the government budget constraint, so such beliefs cannot be self-fulfilling. Importantly, the paper assumes b* > 0 (positive steady-state primary surplus), distinguishing it from Kaplan et al. (2023), where multiplicity arises under persistent deficits.

Q8. Do other standard monetary rules rescue determinacy?

No. Appendices E.1 and E.2 show that adding an output-gap response (it = φπ·πt + φx·xt) or making the rule inertial/backward-looking can make LOCAL determinacy easier but cannot eliminate global indeterminacy: for any finite (φπ, φx) however large, or any degree of backward-lookingness (any α), the equilibrium remains globally indeterminate as long as risk is countercyclical. The reason is that none of these rules respond to the endogenous natural-rate fluctuations directly.

Q9. How robust are the results to the functional form of countercyclical risk?

Robust. Appendix E.4 generalizes λl,t = λl·Λ(γxt) for any non-negative, weakly decreasing analytic Λ. The untargeted steady state exists whenever risk is countercyclical locally (−Λ’(0) = Θ > 0), even if Λ is linear. The stable cycle exists if Λ is sufficiently convex locally (Λ’’(0) sufficiently positive). Crucially the conditions depend only on local behavior at x = 0, which is reassuring given the thin empirical evidence on how risk varies far from steady state. The authors argue convexity is plausible: the inflow rate into unemployment rises sharply in recessions but does not fall as sharply in expansions (Crump et al. 2019), and labor-flow asymmetries exceed GDP asymmetries (McKay-Reis 2008).

Q10. Does the multiplicity survive introducing predetermined variables?

Yes, with a caveat about jumps. The baseline has no predetermined variables, so the economy can instantaneously jump between steady states/onto the cycle. Appendix E.5 lets the fraction of ξl households vary (a predetermined state), Appendix E.2 uses a backward-looking rule (lagged inflation predetermined), and Section 4.2/Appendix D.1 add government debt. In all cases instantaneous jumps are ruled out, but global indeterminacy persists: transitions to the untargeted steady state or the stable cycle become GRADUAL (e.g., a slow rise in the ξl fraction alongside falling output and inflation) rather than instantaneous.

Q11. What are the headline calibrated magnitudes and how credible are they?

Calibration: real rate 4%, relative risk aversion γ⁻¹ = 2, transition rate λl = 0.013 (from Bilbiie-Primiceri-Tambalotti 2023), consumption drop at job loss ch/cl = 1.1 implying ξh/ξl = 1.23, and φπ = 1.5. This gives regime boundaries Θ⋄ ≈ 15.8 and Θ* = 31.08. The empirically estimated Θ lies in [21.98, 29.9] (mode 28.1), squarely in the moderately countercyclical region. At Θ = 28.1, the untargeted steady state has output ~6.5% below target (comparable to post-Great-Recession U.S./Euro-area gaps) and the stable cycle has output-gap amplitude ~±2.5% (comparable to U.S. business cycle fluctuations). The 10% consumption drop is within empirical estimates (Cochrane 1991: 24–27% lower growth; Ganong-Noel 2019: ~11%; Gruber 1997: 6.8% for food).

Q12. What are the policy implications and their caveats?

Central banks should monitor and react to private-sector beliefs about REAL activity (consumer confidence, perceived job-loss probability) as vigilantly as they monitor inflation expectations — ignoring real-activity beliefs can leave even inflation expectations unanchored. Because multiplicity does not stem from the ELB, it can afflict the economy even during a tightening cycle, and large rate hikes against inflation do NOT by themselves guarantee anchored expectations. Caveat/scope: the prescriptions hold in this stylized cashless, quasi-linear, no-aggregate-risk model; the precise cycle magnitude/periodicity and depth of the untargeted steady state depend on the full shape of Λ away from steady state, even though their existence depends only on local behavior.

Q13. What is the broader methodological lesson?

Local stability/determinacy analysis can be misleading: even when the targeted equilibrium is locally determinate, multiple bounded global equilibria can exist. Researchers using HANK models should check global, not just local, determinacy. Because linear models have no higher-order terms, local determinacy implies global determinacy there; but HANK with countercyclical risk is genuinely nonlinear, so the implication breaks.

Key Concepts

Natural rate of interest r(y)*: Defined Keynes-style (1936) as the real interest rate consistent with output remaining constant at level y; given by r*(y) = ρ − σy^(−Θ). Distinct from the flexible-price real rate. With countercyclical risk it is endogenous and rises with output (dr*/dy > 0), and there is one natural rate per output level.

Neutral rate of interest: The single flexible-price real interest rate r = ρ − σ in the model — the natural rate consistent with full-employment output y = 1, i.e., r = r*(1). It depends only on exogenous parameters, never on endogenous output.

Countercyclical risk (parameter Θ): Idiosyncratic income risk that rises when output falls, modeled via transition rate λl,t = λl·y^(−Θ). Θ > 0 means a ξh household is more likely to fall to the low-productivity (loosely ‘unemployment’) state when output is low; Θ = 0 is acyclical. Θ governs the strength of this cyclicality.

Endogenous demand shock: A self-fulfilling, non-fundamental fluctuation arising because a belief about future activity shifts desired precautionary saving, moves the endogenous natural rate, and — if policy does not offset it — confirms the original belief. Functions like an exogenous demand shock but is generated internally by countercyclical risk.

Global vs local determinacy: Local determinacy: the targeted steady state is the only bounded equilibrium in a small neighborhood (governed by first-order/eigenvalue terms). Global determinacy: it is the only bounded equilibrium starting from ANY point (governed also by higher-order terms). In this nonlinear HANK model local determinacy does NOT imply global determinacy.

Taylor principle for natural rates: The proposed fix: monetary policy must move the nominal rate at least one-for-one (φr ≥ 1) with endogenous fluctuations in the natural rate r*(x), in addition to responding to inflation (φπ > 1). This off-equilibrium commitment prevents beliefs about real activity from becoming self-fulfilling.

Risk-cyclicality regimes (mild / moderate / high): Mildly countercyclical (Θ ∈ (0, Θ⋄)): indeterminacy via a saddle connection to the untargeted steady state. Moderately countercyclical (Θ⋄ < Θ < Θ*): a stable limit cycle surrounds the target. Highly countercyclical (Θ > Θ* = ρ/(σγ)): the target is locally indeterminate for any finite φπ. Calibrated thresholds Θ⋄ ≈ 15.8, Θ* = 31.08.

Taxing Top Wealth: Migration Responses and their Aggregate Economic Implications

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: Proposals to tax top wealth (e.g., Saez and Zucman, 2019) face a recurring objection in public debate: that the wealthy will emigrate en masse and, because many are entrepreneurs, their departure will inflict large negative spillovers (“trickle-down”) on the broader economy, making wealth taxes self-defeating. Credible evidence on international migration responses to wealth taxes has been scarce due to data limitations and a lack of clean identifying variation. This paper provides such evidence and quantifies the aggregate economic implications.

Data and setting: The authors use exhaustive administrative data from Sweden (wealth tax register Förmögenhetsregistret 1993-2007, LISA, matched employer-employee RAMS, K10 closely-held-business filings, and the Serrano ownership-network data that maps indirect ownership) and Denmark (used for out-of-sample validation). A key strength is observing all wealth components without top-coding and linking individuals to firms they control directly and indirectly. They exploit three large reforms: the unexpected 2007 repeal of the Swedish wealth tax (statutory top marginal rate fell from 1.5% to 0%; effective average rate on the top 2% was ~0.5%), and Danish reforms of 1989 (rate cut from 2.2% to 1%) and 1996/1997 (abolition). Business assets were exempt in Sweden but fully taxed in Denmark.

Empirical strategy: A two-step procedure. Step 1 estimates migration elasticities using difference-in-differences around the reforms (treated = top 2% of net wealth; baseline control = top 20% to top 10%), with treatment assigned on predicted wealth to avoid endogeneity post-2007. Step 2 estimates the effect of migration on individual-, firm-, and market-level outcomes via event studies (never-movers with placebo dates as controls), independent of the tax reforms. The two are combined, weighted by the wealthy’s share of aggregate activity (decomposition in equation 1).

Main quantitative findings: A 1pp increase in the top wealth tax rate raises the out-migration rate by 0.17pp and reduces in-migration by 0.05pp; the 2007 repeal cut wealthy out-migration propensity by ~30% (about one-third of top-2% expatriations were tax-induced). Danish elasticities are statistically indistinguishable. Net flow semi-elasticity is -0.22pp per 1pp. Flow effects cumulate to a modest stock elasticity: the elasticity of the wealthy population w.r.t. the net-of-tax rate is 1.77 (s.e. 0.47) — a 1% rise in the net-of-tax rate raises the stock by under 2%. The implied income-net-of-tax migration elasticity is ~0.05, comparable to top-income cross-border elasticities. Firms controlled by the top 2% account for ~9% of Swedish employment, 15% of value added, 12% of investment, 19% of tax payments (and ~10% employment / 15% value added per the intro). When a top-2% owner out-migrates, directly-controlled firms see employment fall ~33%, gross investment ~22%, value added ~34%, and tax payments ~51%, driven almost entirely by the extensive margin of firm disappearance (effects near zero conditional on survival). But 45% of “closed” firms are absorbed via mergers/acquisitions; displaced workers lose only 4.3% in earnings and face a 0.6pp higher unemployment probability; market-level spillovers are small and insignificant even for granular firms.

Aggregate and policy implications: Combining steps, a 1pp rise in the top wealth tax rate reduces aggregate employment by 0.022%, investment by 0.065%, and value added by 0.103% in the long run — modest despite the wealthy’s large economic footprint, because migration flows are small. Fiscally, each $1 raised loses only $0.22 to migration responses vs. $0.54 to intensive-margin responses (savings/avoidance/evasion, using Jakobsen et al. 2020), so $0.76 total. Migration responses are far from the Laffer bound but, because the MCPF is highly nonlinear, they nearly double it from ~2.2 to ~4.2. Migration threats, while salient in debate, matter less for welfare and policy than intensive-margin responses.

In depth

Q1. What is the identification strategy for the migration elasticity and what are the main threats?

A difference-in-differences design around the 2007 Swedish wealth tax repeal, comparing out-migration of the treated top-2% group to a control group in the top 20% to top 10%. The non-contiguous control avoids contamination bias (households near the threshold anticipating future liability; less than 1% of controls reach the top 2% by 2006). The main threat is the parallel-trends assumption given a control group lower in the distribution; the authors show no differential pre-trends in out-migration and that effective capital-income and labor-income tax rates evolved similarly across groups (only wealth-inclusive tax rates diverged). The 2007 inheritance tax abolition is ruled out as a confounder because inheritance tax had little bite and strict residency rules made it hard to avoid by migrating (10-year non-residence required at death). Treatment is assigned on predicted wealth (from pre-reform variables) to avoid endogenous post-2007 wealth measurement. 2SLS specification (4) instruments the log net-of-tax rate with the treatment-by-post interaction.

Q2. How is the aggregate effect identified separately from the migration channel, and why not use the reform directly?

National wealth tax reforms cannot identify general-equilibrium/aggregate effects because treatment and control groups share the same aggregate economy, the exclusion restriction fails (wealth taxes also affect savings, capital accumulation, avoidance/evasion), and they are underpowered (small stock changes are hard to detect). The two-step procedure circumvents this: event studies of migration events (specification 7, with randomly-assigned placebo dates for never-movers, no matching) give the effect of migration on outcomes independent of the tax reform, and these are combined with the reform-based migration elasticity, weighted by the wealthy’s share of each aggregate outcome (equation 1).

Q3. What is the role of the LATE / marginal-mover correction?

The two-step procedure requires the population whose migration impact is measured (event studies) to match the population whose migration responds to the tax (compliers). Using methods from the insurance-selection literature (Hendren et al., 2021) and the fact that 30% of pre-reform wealthy migrants were tax compliers, they recover the characteristics and treatment effects of marginal movers. Tax-induced movers (compliers) are slightly younger, slightly more likely entrepreneurs, slightly wealthier, around the 65th-70th skill percentile, but their firms are not selected. Event-study estimates pre vs post reform are similar (not statistically different), so treatment-effect heterogeneity is limited; column (5) double-difference LATE estimates for compliers are the preferred inputs.

Q4. What is the firm-level evidence and how is reallocation distinguished from genuine destruction?

Owner out-migration causes a ~30pp drop in firm survival (firm-identifier disappearance) and large declines in employment (~33%), value added (~34%), investment (~22%), turnover, and tax payments (~51%), almost entirely extensive-margin. The authors distinguish destruction from reallocation using Bolagsverket merger/closure-reason data: 45% of closures are linked to mergers (the firm is absorbed), 55% are liquidations/bankruptcies. Accounting for buy-outs cuts the firm-existence and employment effects by ~40%. Worker-level event studies show displaced employees lose only 4.3% in earnings and 0.6pp higher unemployment, indicating workers reallocate. Including indirectly-held firms, five-year effects are employment -19%, value added -33%, turnover -28%, investment -19%, tax payments -45%.

Q5. What heterogeneity is documented?

Migration semi-elasticities do not vary much by age or education; entrepreneurs’ out-migration semi-elasticity is larger but less precisely estimated (their effective tax rate dropped less because business assets were exempt; their out-migration fell ~0.14pp, roughly 50%, within a year). Firm-level migration effects show limited heterogeneity by owner age or children; effects are smaller for larger firms and especially for the top-10 largest moves (multi-billion-SEK businesses), where effects are considerably below average. In-migration effects mirror out-migration with opposite sign but are smaller for value added, turnover, investment, and tax payments.

Q6. What robustness checks are run?

Estimates are robust to alternative control groups closer to the treatment group; to assumptions on the regeneration/replacement rate of the wealthy population and to dynastic effects (detectable but small); and to tax evasion — using Alstadsæter et al. (2019) and Boas et al. (2024) bounds, the stock elasticity ranges 1.85 (lower) to 1.92 (upper) vs. 1.77 baseline. Firm outcomes are robust to winsorization choices (Appendix Table IV.3); with no winsorization, value added/investment/tax effects turn positive-insignificant due to one outlier firm. Market-level spillovers are insignificant across alternative market definitions. Alternative aggregate calibrations (including accounting for buy-outs) imply smaller effects, so the baseline is a conservative upper bound.

Q7. How does the paper relate to and differ from prior work?

It builds on the wealth-tax behavioral-response literature (Seim 2017; Jakobsen et al. 2020; Brülhart et al. 2022) which is largely silent on international migration, and on the tax-migration literature (Kleven et al. 2013/2014/2020; Akcigit et al. 2016) which focuses on income taxes and within-country mobility. It is the first systematic evidence on international migration responses to wealth taxes and their trickle-down. Versus the CEO/owner death-and-retirement literature (Smith et al. 2019: -26pp firm survival, -82% profits per worker, -45% even conditional on survival; Jäger and Heining 2022), migration effects are much smaller and nearly zero conditional on survival, because owners often retain control or restructure rather than shut down. Findings echo Bach et al. (2023) for France.

Q8. What are the policy implications and their scope conditions?

Migration-driven fiscal externality is $0.22 per $1 raised, vs. $0.54 for intensive-margin responses, $0.76 combined — below the Laffer bound. Because the MCPF is nonlinear, migration roughly doubles it from ~2.2 to ~4.2; wealth taxation would be welfare-improving if revenue funds projects with MVPF above 4.2 (e.g., programs for low-income children, often above 5 per Hendren and Sprung-Keyser 2020). Scope conditions: estimates come from reforms that only cut rates, so asymmetric responses to increases cannot be ruled out; the elasticity depends on destination-country taxes (Swedish movers went to low-tax UK non-dom, Switzerland, Austria), so responses could be more muted if all neighbors taxed wealth heavily; results are for small open economies with low wealth inequality and weaker agglomeration than the US, suggesting the estimates are upper bounds; computations reflect 1990s-2000s Scandinavia where offshoring/evasion mattered, and depend on tax base, enforcement, and exit-tax design.

Q9. How is the stock elasticity derived from flow elasticities?

Using a simple OLG framework, the population stock elasticity ≈ net-flow semi-elasticity times (T+1)/2, where T is the average ’lifespan’ of wealthy individuals (the inverse of the regeneration/birth rate into the wealthy population). Longer lifespan means slower regeneration, so lost migrants are harder to replace and the stock effect is larger. This yields a stock elasticity of 1.77 (s.e. 0.47); the effect stays modest because top-of-distribution migration flow rates are very small.

Q10. What are the magnitudes of migration flows and tax-payment effects, and any caveats on persistence?

Top-decile out-migration is ~0.2% per year in Sweden (vs. ~0.65% in the bottom half) and ~0.1% in Denmark, rising in the extreme tail; taxable wealth of wealth-tax-liable out-migrants is only 0.09% of total taxable wealth; net migration is small and slightly positive. One year after out-migration, total tax payments fall ~66% (wealth tax -59%, income tax -68%; income taxes are ~90% of the wealthy’s payments, implying large fiscal externalities on income tax). Effects attenuate over time: ~40% reduction at five years because ~40% of out-migrants return within five years (migration is persistent but return migration is common). Taxable wealth in Sweden falls 94% one year out; real estate is typically sold, and financial wealth falls at extensive (-21%) and intensive (-15%) margins, confirming real rather than purely fiscal-residence responses.

Key Concepts

The Aggregate Costs of Uninsurable Business Risk

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation. A large literature argues that credit constraints are the dominant financial friction holding private businesses below their optimal scale, so that easing credit access would yield large aggregate efficiency gains. This paper challenges that view. Private businesses are also poorly diversified — their owners bear undiversifiable business-income risk — and the authors argue the macroeconomic costs of this lack of diversification are far larger than those of credit constraints. The crux is that entrepreneurs can limit risk exposure by operating at a smaller scale, so productive-but-poor entrepreneurs choose an inefficiently low scale and are unwilling to borrow to expand. Firm size is thus limited by risk, not by credit availability.

Data and setup. The empirical analysis uses the historical Orbis dataset (Moody’s Bureau van Dijk), 1995–2019, focusing on Spain (best coverage; results extend to Italy, France, Norway, Portugal, Slovakia in the appendix). Output is value added; the sample is partnerships and private limited companies, excluding FIRE, public administration, defense, education. The final sample is 622,883 firms (6,298,358 firm-year observations), observed on average 10 years; the mean (median) firm has 12 (5) workers and 486 (151) thousand EUR value added. The Spanish Survey of Household Finances (EFF, 2008–2020) provides entrepreneur wealth/prevalence and consumption data. The model is a small-open-economy model of entrepreneurial dynamics (à la Quadrini 2000; Cagetti–De Nardi 2006) with two frictions: each firm is owned by a single (undiversified) entrepreneur, and a collateral constraint k’ ≤ a’/(1−ξ). Key modeling choices: capital AND labor are chosen before productivity is observed (time-to-build), and productivity has persistent and transitory shocks drawn from fat-tailed mixtures of normals. Parameters are estimated by simulated method of moments (9 parameters, 16 moments; objective 0.013, ~1.3% average deviation).

Main quantitative findings. Profit shares fluctuate sharply: 5% of firms have losses exceeding 20% of output, against an average profit share of 0.13; the 5th percentile of profit-share deviations is −0.33 and the 95th is +0.47. Output growth is fat-tailed (s.d. 0.48, IQR/s.d. ratio 0.65 vs 1.35 Gaussian; excess kurtosis 10.7). Inputs do not track output: regressing wage-bill growth on output growth gives 0.40 (capital 0.16); restricting to |Δlog y|<0.5 gives 0.58 and 0.31. A change in profit share on output growth has slope 1.56 (0.46 in the restricted sample). The headline result: eliminating both frictions would raise output by 15.8%; eliminating the risk wedge alone raises output by 15.4%, while eliminating the credit wedge alone raises output by only 0.4%. Misallocation losses are 10.8% (11.0% due to risk, 0.2% due to credit). Aggregate wedges are equivalent to a 12.8% tax on labor and 14.9% on capital. Wage losses are 27.8% (26.4% risk, 0.4% credit).

Mechanisms and implications. Two wedges distort choices: a risk wedge (from the covariance of consumption and productivity) that distorts both labor and capital, and a credit wedge (from the binding collateral constraint) that distorts only capital. The credit wedge falls quickly with wealth (vanishing once unconstrained), but the risk wedge declines only gradually and persists even for wealthy entrepreneurs. Aggregate losses are governed by the distribution of wedges weighted by efficient firm size (Hopenhayn 2014): risk wedges are large precisely for high-ability entrepreneurs who would be large under efficiency, whereas credit-constrained firms are mostly unproductive with small efficient size. Policy implication: improving credit access has limited impact unless it also improves risk sharing. The findings also imply firm profits largely reflect compensation for risk (75% of the aggregate profit share), and dispersion in returns to business wealth largely reflects risk compensation.

In depth

Q1. What is the identification strategy for the model, and how are parameters pinned down?

Parameters ϑ=(β,α,η,ρ,σu,σε,s,p,ϕ) are estimated by simulated method of moments, minimizing a weighted distance between 16 empirical and model moments scaled by 1+empirical moment (objective = 0.013, ~1.3% average deviation). Intuitively: β is pinned by the entrepreneur wealth-to-income ratio (12.5 in data and model); α and η by the capital-output ratio (1.22 vs 1.21), labor share (0.72 vs 0.71) and profit share (0.13 vs 0.14); ρ, σu, σε by output autocorrelations at horizons 1–3, the cross-sectional s.d. of output, and the s.d. of output growth at horizons 1–3; the tail parameters s and p by the IQR of output growth relative to its s.d.; and ϕ by the entrepreneurship rate. Three assigned parameters: δ=0.10, r=0.02, θ=2, with ξ=0.408 set to match the aggregate debt-to-capital ratio of 0.408. Standard errors (bootstrapped) are small because the firm sample is very large.

Q2. What is the main mechanism, and how are the risk wedge and credit wedge distinguished?

Because labor and capital are chosen before productivity is realized and risk is undiversified, the entrepreneur weights future states by their own stochastic discount factor. The risk wedge τ (>1) arises from the negative covariance between marginal utility of consumption and productivity and distorts both labor and capital equally. The credit wedge ω (>1 when the collateral constraint binds) distorts only capital. As wealth rises, the credit wedge falls rapidly and vanishes once the firm is unconstrained, but the risk wedge declines only gradually and never disappears. The two are isolated quantitatively by setting ω=1 (to get the role of risk) or τ=1 (to get the role of credit) in the productivity-loss mapping (eq. 13).

Q3. Why does risk dominate credit in the aggregate even though most firms are credit-constrained?

Aggregate outcomes depend on the distribution of wedges weighted by efficient firm size n_it (Hopenhayn 2014). Weighted by efficient size, the risk wedge ranges from 1.27 (10th pct) to 1.61 (90th pct), while the credit wedge is essentially 1 except at the very top (1.02 at the 90th pct). Unweighted, the risk wedge is only 1.12 at the 90th pct and the credit wedge is positive for more than half of firms — but those constrained firms are unproductive with small efficient size. Risk wedges are large precisely for high-ability entrepreneurs who would be large under the efficient allocation, so they drive the aggregate.

Q4. Why is the result robust to the form of the collateral constraint?

The authors consider two extremes: no borrowing at all (ξ=0) and unlimited borrowing (ξ=1, no credit limit). With no borrowing, misallocation losses rise only from 10.8% to 11.7%, still mostly risk-driven (8.3% risk vs 1.4% credit). With no credit limit, risk wedges remain nearly as large as baseline and removing credit frictions has negligible effects. Intuitively, risk leads entrepreneurs to operate small and accumulate precautionary wealth, so they self-finance most desired capital and credit wedges stay small even without credit.

Q5. Which three ingredients are essential to the risk-dominates result, and what happens without each?

(1) Fat-tailed productivity shocks, (2) transitory productivity shocks, and (3) labor chosen before productivity is realized. Removing each in isolation (with re-estimation) reverses the conclusion so that credit becomes the primary driver: without fat tails, misallocation losses fall to 2.1% (credit 1.5%, risk 0.3%); without transitory shocks, losses are 12.1% (credit 10.9%, risk 0.4%); with flexible labor, losses fall to 3.3% (credit 2.4%, risk 0.1%). The flexible-labor case matters because risk then distorts only capital, whose share is smaller than labor’s, reducing income volatility and pushing firms to expand and hit the credit constraint. In all three counterfactuals, the 1st percentile of profit-share deviations ranges −0.21 to −0.43, far smaller in magnitude than the data (−1.66) or baseline model (−1.92).

Q6. Is the result driven by high risk aversion?

No. The baseline uses relative risk aversion θ=2. Re-estimating with θ=0.5 (low end of usual values) still yields sizable, risk-dominated losses: productivity losses 6.4%, output losses 9.2%, wage losses 16.7% — roughly three-fifths of the baseline — and again primarily driven by risk rather than credit.

Q7. What untargeted moments does the model match (model validation)?

The model reproduces the distribution of profit-share deviations (10th pct −0.17 data vs −0.16 model; 1st pct −1.66 data vs −1.92 model), the full distribution of output growth rates, the low wage-bill/output comovement (0.58 data vs 0.55 model in the restricted sample), the profit-share/output comovement (0.46 vs 0.42; falling to 0.10 vs 0.06 when holding the labor share constant), and the persistence/volatility of capital and labor (e.g., wage-bill growth s.d. 0.36 vs 0.32). Critically, it matches the low comovement of entrepreneur consumption with profits: regressing Δc on Δπ gives a slope of 0.02 in both data and model (data based on 799 EFF observations, three-year changes).

Q8. What heterogeneity and external validity does the paper document?

The motivating facts hold for Italy, France, Norway, Portugal and Slovakia, and for Spanish public firms; for young (age≤5) and old firms; for small and large firms (top decile of value added vs rest); and across the five largest sectors (manufacturing, construction, wholesale/retail, accommodation/food, professional activities). Output-growth kurtosis ranges roughly 11–18 across countries. On diversification: 12% of households are entrepreneurs; 93% of entrepreneurs own exactly one business; multi-business owners hold 71% of their business wealth in their main business; the average ownership share is 83%, and 71% own 100% of their main business.

Q9. What are the extensive-margin and unconstrained-firm results?

Extensive margin: when the planner can also choose who becomes an entrepreneur, it cuts the entrepreneurship rate from 13.2% to 1.2%, but because marginal entrepreneurs are low-ability the gains are small — productivity, output and wage losses relative to the unconstrained planner are 10.8%, 16% and 27.8%, very close to the intensive-margin numbers. Unconstrained firms: adding a frictionless sector calibrated to match the 58.7% output share of public firms in Orbis leaves misallocation losses at 10.5% (vs 10.8% baseline), still mostly risk-driven (risk 10.1%, credit 0.1%); wage losses fall to about three-fifths of baseline because the unconstrained sector reduces the aggregate labor wedge.

Q10. What are the implications for profits and returns to wealth?

Decomposing the profit share into span-of-control, risk and credit components: risk accounts for 75% of the aggregate profit share (0.11/0.146), with the rest from span of control; credit contributes little. Risk also drives most of the profit-share dispersion (s.d. 5.5%, essentially all from risk; credit contributes only 1%). For excess returns to wealth, the mean of 2.2% is almost entirely accounted for by risk, and risk drives most of the dispersion (s.d. 5.5%). This implies dispersion in returns to private business wealth — a driver of wealth inequality — largely reflects compensation for risk rather than credit constraints.

Q11. What is the working-capital robustness check?

Adding a working-capital constraint where a fraction ϑ=0.25 of the wage bill is paid in advance (à la Mendoza 2010), evaluated at baseline parameters, gives misallocation losses of 11.1% (vs 10.8% baseline), with risk still accounting for the bulk (9.4%) and credit less important (1.3%); risk accounts for 13.4% of the 16.3% total output losses. So even when credit frictions can also distort labor, risk remains dominant.

Q12. What are the policy implications and their scope conditions?

The central implication is that policies expanding firms’ access to credit will have limited aggregate impact unless they also improve risk sharing. This holds within the scope of the model — undiversified private businesses with single owners, where risk exposure is endogenously chosen via scale and can be partly self-insured through wealth, labor income, and occupational switching. The authors note their framework assumes (rather than micro-founds) the lack of diversification, and suggest future work should model the moral-hazard or informational frictions preventing diversification, and broaden redistributive tax analysis to incorporate uninsurable-risk distortions (as in Di Tella et al. 2024).

It contributes to the misallocation literature (Hsieh-Klenow 2009; Buera et al. 2011; Moll 2014; Midrigan-Xu 2014; Gopinath et al. 2017). Prior work on risk and investment (Tan 2018; Robinson 2021; David et al. 2022a) studies how risk distorts investment; this paper instead emphasizes how risk distorts LABOR choices, relating it to Arellano et al. (2019) and David et al. (2022b). It differs from the credit-constraint-centric tradition by showing credit matters little once undiversified risk and the three key ingredients are present. Di Tella et al. (2024), partly motivated by these findings, study optimal policy under uninsurable risk and show it is the opposite of optimal policy when misallocation stems from markups.

Key Concepts

Risk wedge (τ): In the paper’s sense, the gap between the expected marginal product of an input and its price arising from undiversifiable business risk. It equals [1 + COV(c^{-θ}, zε)/(E c^{-θ} · E zε)]^{-1}, generally >1 because of the negative covariance between the entrepreneur’s marginal utility of consumption and productivity. It distorts both labor and capital, declines only gradually with wealth, and persists even for wealthy entrepreneurs.

Credit wedge (ω): The distortion from a binding collateral constraint, ω=1+(1−ξ)μ/R, where μ is the multiplier on the constraint k’≤a’/(1−ξ). It exceeds one only when the constraint binds, distorts only capital, falls rapidly with wealth, and vanishes once the entrepreneur is unconstrained.

Profit share: In this paper, the ratio of profits to output (value added), π_it/y_it, where profit is output net of the wage bill and the user cost of capital. Its average is 0.13; the paper studies its large transitory firm-level fluctuations as the empirical signature of uninsurable risk.

Time-to-build (inputs chosen before productivity): The assumption that both capital and labor are chosen before the firm observes its productivity shock. This parsimoniously generates the imperfect high-frequency comovement between inputs and output and makes wealth affect employment as well as investment.

Efficient-size-weighted wedge distribution: The paper’s organizing device (following Hopenhayn 2014): aggregate productivity losses depend on the distribution of risk and credit wedges weighted by each firm’s efficient size n_it. Because high-ability firms have large efficient size and large risk wedges, risk dominates the aggregate even though most firms are credit-constrained.

Self-financing: The mechanism by which entrepreneurs, operating at small scale and saving for precautionary reasons because of risk, accumulate enough wealth to finance most of their desired capital — so credit wedges stay small even in an economy with no credit, rendering the borrowing limit nearly irrelevant for aggregates.

The Efficiency-Equity Tradeoff of the Corporate Income Tax: Evidence from the Tax Cuts and Jobs Act

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

This paper estimates the firm- and worker-level effects of the corporate income tax cuts in the 2017 Tax Cuts and Jobs Act (TCJA) — the largest corporate tax cut in U.S. history — to inform the long-running efficiency-versus-equity debate over corporate taxation. The question matters because federal corporate tax reforms are rare, prior credible evidence comes mostly from subnational or small-economy variation (where factors are more mobile and the tax base smaller), and theory predicts alternate instruments behave differently, so existing estimates may not extrapolate to a major reform in a large advanced economy.

Identification exploits that TCJA cut the top C-corporation rate from 35% to 21% (a 40% reduction) while cutting the implied top rate for S corporations far less — from 39.6% to 37%, and to 29.6% for many via the new 20% Qualified Business Income deduction (a cumulative ~25% reduction). The authors use employer-employee matched federal tax records (corporate SOI files merged with W-2 and individual returns), tax years 2013-2019, on a balanced panel of large firms (>=50 employees and >=$1M sales each pre-period year): 15,490 firms and 108,430 firm-year observations. The main design is an event study / 2SLS comparing similarly sized C and S corps in the same industry-size bin, with firm and industry-size-year fixed effects and standard errors clustered by firm; entity-switchers are dropped. The identifying assumption is parallel trends absent the tax change (as in Yagan 2015), not random C/S assignment.

First stage: C corps’ marginal tax rate fell ~5.0 pp (s.e.=0.2) relative to S corps, raising the log net-of-tax rate ~6.6% (s.e.=0.2); C corps paid ~$2,100 (s.e.=341) less tax per worker. Real effects: C-corp sales rose 3.9 pp (s.e.=1.2) relative to S corps; pre-tax profits +3.0 pp (s.e.=0.7); after-tax profits +4.0 pp (s.e.=0.7); total payouts +21.9% intensive (s.e.=2.9) and +3.0 pp extensive (s.e.=0.5); employment +2.3% (s.e.=0.8); payrolls +3.4% (s.e.=0.8); net investment +2.9% (s.e.=0.4). The benchmark corporate elasticity of taxable income (pre-tax profits) is 0.46 (s.e.=0.11); after-tax-profit elasticity 0.61 (s.e.=0.11); investment elasticity 0.45 (s.e.=0.07). Worker earnings are flat for the bottom 90% (median wp50 coefficient -0.001, s.e.=0.004) but rise for the top 10%: +1.3% at the 95th percentile (s.e.=0.4), +4.8% at the 99th, and +4.8% for executives (top-5 paid; s.e.=0.7, earnings elasticity 0.73). Executive-pay gains barely shrink when controlling for firm performance (4.8% to 4.5%) and are concentrated among incumbents, consistent with rent-sharing rather than productivity.

Responses concentrate in capital-intensive industries and are not larger for cash-constrained firms, pointing to a cost-of-capital channel rather than liquidity. Via a stylized model, a $1 marginal cut in corporate tax revenue generates $0.44 in additional output; revenue falls $0.85 per $1 mechanical loss (total -$86 billion, 0.40% of GDP). Factor incidence: 51% of gains to firm owners, 10% to executives, 38% to high-paid workers, 0% to low-paid workers. Across the income distribution, 80% of gains accrue to the top 10% and 20% to the bottom 90%, with gains concentrated in the Northeast/West and large high-income cities. The corporate tax is ~twice as inefficient as the personal income tax but similarly progressive, suggesting margin-of-efficiency gains from shifting toward personal income taxation. Results are short-run and abstract from public-goods provision and deficit financing.

In depth

Q1. What is the identification strategy and what are the main threats to it?

The strategy is a difference-in-differences/event study (and 2SLS) comparing C corporations to S corporations in the same industry-size bin before and after TCJA, instrumenting the change in the log net-of-tax rate with pre-existing C/S entity status, with firm and industry-size-year fixed effects and firm-clustered standard errors. The identifying assumption is parallel trends in outcomes absent the tax change (not random C/S assignment), supported by (a) flat pre-trends in the event studies, (b) Yagan (2015) showing C and S trends were statistically indistinguishable 1996-2008, (c) the unexpected nature of TCJA before the 2016 elections limiting anticipation, and (d) industry-size-year fixed effects matching firms in similar product markets. Main threats: anticipatory/intertemporal tax shifting (some rate decline already in 2017; executive pay also trends up in 2017); other concurrent TCJA provisions (bonus depreciation, DPAD repeal, NOL/interest limitation, international); endogenous entity switching; differential industry-size composition; and general-equilibrium/SUTVA violations where C-corp gains could be S-corp mirror-image losses or where common wage effects are absorbed by time fixed effects.

Q2. What are the main mechanisms and how are they distinguished empirically?

The authors argue the dominant mechanism is a reduction in the cost of capital from the permanent rate cut, not liquidity relief and not primarily bonus depreciation. Evidence: (1) responses are larger in capital-intensive industries (profits and investment), consistent with the cost-of-capital first-order condition; (2) high-cash firms are if anything more responsive than low-cash firms, ruling out liquidity constraints (and thus income effects); (3) bonus depreciation is downweighted because many eligible firms do not claim it, much capital (intangibles, structures) is never fully expensed, C and S corps had near-identical expensing exposure (so the design differences them out), and the investment response is driven almost entirely by short-lived assets rather than the long-lived assets where accelerated depreciation is most valuable. A complementary dynamic-adjustment-cost model (Auerbach-Hassett 1992 with Foertsch 2018 cost-of-capital inputs) yields elasticities very similar to the benchmark.

Q3. What heterogeneity is documented?

By capital intensity: C corps in capital-intensive industries show significantly larger profit and investment responses (supporting the cost-of-capital channel). By liquidity: high-cash firms are no less (if anything more) responsive than low-cash firms, contrasting with Zwick and Mahon (2017). By firm size: no clear pattern in profits, median earnings, or investment, with only suggestive evidence that high-income-worker gains are larger in smaller firms. By worker position: earnings gains are concentrated entirely in the top 10% of the within-firm distribution and especially in executives, with zero gains below the 90th percentile. By worker tenure: gains are driven by incumbents, not new hires (consistent with rent-sharing). Geographically: gains concentrate in the Northeast and West and in large high-income commuting zones (e.g., ~3x the median CZ gain in New York City, ~5x in the San Francisco Bay Area).

Q4. What robustness checks are run?

Alternate specifications (Table 7): cohort(age)-by-year FE, state-by-year FE, firm-specific pretrend controls, 6-digit NAICS industries, reweighting S to match the C industry-size distribution, inverse-propensity-weighting, log-transformed outcomes, winsorizing at 5th/95th percentiles, and 2016-sales/payroll weighting — elasticities are stable. Alternate samples (Table 8): excluding firms with >$1B sales or >10,000 employees, excluding mismatched industries (C share >80% or <20%), excluding manufacturing (trade-war exposure), unbalanced panel, excluding public firms, excluding industries most exposed to DPAD/NOL/interest-limitation/bonus-depreciation provisions, excluding multinationals, dropping tax years 2017-2018 (anticipation/shifting), and dropping single-owner S corps (wage/profit reclassification). Entity switching rose only from ~0.1% to ~0.3% (profit-weighted) and is negligible. Most estimates stay within the benchmark confidence intervals.

It builds on the C-vs-S comparison design of Yagan (2015) but studies marginal corporate rate cuts rather than the 2003 dividend tax cut. It obtains an investment elasticity (0.45) very close to Chodorow-Reich et al. (2023)’s 0.52 despite a different identification strategy and sample. Its corporate ETI (0.46) is below state/local estimates (Giroud-Rauh ~0.50; Suarez Serrato-Zidar ~0.9; Bachas-Soto 3.0-5.0 in Costa Rica) but above typical personal-income ETIs (Saez et al. central 0.25), consistent with distortions scaling with factor mobility. Its incidence finding — that the corporate tax falls on capital and high-income workers — differs from Fuest et al. (2018), who find German municipal corporate tax hikes fall on low-skilled/marginally-attached workers (the authors note possible asymmetry between hikes and cuts and small-firm effects), and aligns with Risch (2024). It uses directly observed owner returns and the full earnings distribution, requiring weaker assumptions than Suarez Serrato-Zidar (2016, who infer owner returns structurally) and Fuest et al. (who assume negligible rental-rate changes).

Q6. What are the policy implications and their scope conditions?

On efficiency: a $1 cut in corporate tax revenue yields $0.44 of additional output, and current U.S. top corporate rates appear below the revenue-maximizing rate (revenue falls only $0.85 per $1 mechanical loss). The corporate tax is ~twice as inefficient as the personal income tax but similarly progressive, and 3-4x more progressive than the payroll tax while being 2-3x as inefficient — implying that shifting the federal revenue mix toward personal income taxes could raise efficiency without much loss of progressivity. On equity: the cuts are regressive in the short run, with 80% of gains to the top 10% (24% to the top 1%, 56% to the 90-99th percentiles), 0% to low-paid workers, and 17% flowing to foreign equity holders. Scope conditions: estimates are short-run (through 2019, pre-COVID); they hold welfare equal to output (ignoring utility curvature); they assume a representative consumer (no consumer-price channel) and equal redistribution of revenue; they abstract from deficit financing, public-goods provision, and long-run productivity/wage effects; and the very largest C corps have no S-corp analogue, so their responses are not well identified.

Q7. What other significant findings, extensions, or caveats appear?

Employment increases reflect predominantly reallocation of workers across sectors rather than net new hiring, which the authors account for in the aggregate analysis (and is why incidence focuses on wages, not employment). New investment gains are in short-life assets (e.g., computers), with no change in long-life machinery or structures. Firms returned excess profits via dividends and buybacks but did not increase equity or debt issuance, and shareholder-payout results are robust to excluding multinationals (so the repatriation holiday is not the driver). Executive pay shifted forward into 2017 (bonuses) to be deducted at the higher pre-cut rate. Caveats flagged by the authors: rent-sharing tests are suggestive not dispositive (conditioning on post-treatment outcomes; unobserved hours/effort; short two-year horizon); private-income components are precisely estimated but the welfare confidence interval includes zero (up to ~0.4% of GDP); and long-run channels (productivity, lower prices, real wages) and offsetting cuts to public services/transfers are outside the analysis.

Key Concepts

C corporation vs. S corporation: The two legal entity types whose divergent TCJA tax treatment provides identification. C corps pay corporate income tax directly (rate cut 35% to 21%) and their dividends are taxed at the shareholder level; S corps pass income through to up to 100 individual U.S. shareholders who pay ordinary income tax (top rate cut 39.6% to 37%, or 29.6% with QBI), with no corporate-level or dividend tax.

Implied marginal tax rate (for S corps): Because S corps pay no entity-level tax, their firm marginal rate is constructed as the ownership-share-weighted average of the individual marginal income tax rates of the firm’s owners, computed from linked personal returns (e.g., two equal owners at 25% and 35% imply 30%).

Corporate elasticity of taxable income (ETI): The percent change in the corporate tax base (pre-tax profits) per percent change in the net-of-tax rate; the paper’s benchmark is 0.46. Following Feldstein (1999), it summarizes the deadweight loss / efficiency cost of the tax under negligible income shifting and income effects.

Net-of-tax rate: One minus the marginal tax rate, ln(1-tau); the object firms optimize against, used to scale reduced-form effects into elasticities. TCJA raised C corps’ log net-of-tax rate by ~6.6% relative to S corps.

Cost-of-capital channel: The mechanism by which a lower tax rate (or higher expensing parameter theta) reduces the user cost of capital phi = r(1-theta*tau)/(1-tau), raising capital demand, labor demand, and firm scale — the paper’s preferred interpretation, distinguished from liquidity effects.

Marginal excess burden: dW/dT, the change in welfare (output, defined as private income plus tax revenue) per dollar of corporate tax revenue; estimated so that $1 of foregone corporate revenue generates $0.44 of additional output.

Incidence across the income distribution: An extension of factor incidence that assigns owners’ capital gains back to workers using the Distributional Financial Accounts (since many workers hold equity and many owners work), yielding the result that 80% of tax-cut gains accrue to the top 10% of earners.

Rent-sharing: The channel whereby earnings gains accrue to incumbent high-paid workers and executives rather than to new hires (the marginal unit of labor), with executive pay only weakly tied to firm performance — interpreted as workers/executives capturing a share of excess after-tax profits.

Uncertainty and Change: Survey Evidence of Firms' Subjective Beliefs

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: A large literature shows that firms perceiving more uncertainty make more cautious intertemporal decisions (investment, hiring, price setting), but it is far less clear what makes firms uncertain in the first place. Macro models typically impose rational expectations and treat uncertainty as exogenous shocks to the conditional volatility of fundamentals. The paper asks how subjective uncertainty arises and evolves, and whether it is the same object as conditional volatility.

Data and design: The authors build a new panel from a quantitative module they added in 2012 to the ifo Business Survey of German manufacturing firms. At the start of each quarter, top managers report (i) last quarter’s realized sales (“Umsatz”) growth, (ii) a one-quarter-ahead point forecast, and (iii) best- and worst-case scenarios. The “span” between best and worst case is their quantitative measure of subjective uncertainty; the forecast error is realized growth minus the point forecast. The baseline sample is 1,005 firms and 8,889 firm-quarter observations over 27 waves, 2013:Q2–2019:Q4 — a calm period with no German recession. A simple scenario-analysis model (Proposition 1) shows that under a quadratic loss and a location-scale shock family, span is proportional to subjective standard deviation, justifying span as an index of subjective conditional volatility. An organizing framework contrasts rational expectations (Example R: subjective uncertainty equals conditional volatility, forecasts unbiased) with learning about signal quality (Example L: managers are unsure of signal precision, so unfamiliar signals raise perceived uncertainty even when true volatility is constant, and generate forecast bias).

Main findings with magnitudes: (1) Subjective uncertainty reflects experienced change, in both cross section and time series, following an asymmetric V-shape in growth (steeper negative branch, flatter positive branch, minimum near zero). Mean span is 12.4 pp, larger than mean absolute forecast error of 9.0 pp; cross-firm SD of time-averaged span is 7.4 pp and within-firm time-series SD of span is 6.3 pp. Cross-sectional V: a 1 pp lower (more negative) average growth goes with about 0.6 pp higher span; a 1 pp higher positive average growth with about 0.2 pp higher span. Time-series V (firm fixed effects removed): a 1 pp lower negative quarterly growth is followed by 0.2 pp higher span next quarter; a 1 pp higher positive growth by 0.1 pp (0.118 positive, -0.204 negative branch coefficients in Table 4). (2) Uncertainty is more than conditional volatility. Volatility explains about a quarter of cross-sectional variation in uncertainty; turbulence quartile dummies alone explain 30%, with span rising from 7 pp (lowest) to 18 pp (highest quartile). But controlling for turbulence, shrinking firms remain more uncertain (bottom-trend dummy ~2 pp) and make systematically too-conservative (toward-zero) forecasts, while large firms (>250 employees) report ~5 pp lower span holding trend/turbulence fixed (9 pp unconditionally). In the time series, after positive growth uncertainty rises but absolute forecast errors do not — inconsistent with rational expectations (Proposition R2), consistent with learning (Example L). Within-firm forecast-error/forecast correlation is -0.27 (overreaction); larger in magnitude (-0.31 vs -0.24) for low-excess-span firms. (3) Uncertainty is mostly idiosyncratic (time/industry fixed effects give R-squared ~1%, rising to ~5-7% with time-industry effects) yet matters for plans: a one-SD rise in span raises the probability of planned employment decrease by 2.4 pp (vs 4.2 pp for a one-SD forecast decline; baseline ~11%), raises planned price decreases by 0.9 pp and lowers planned price increases by 0.8 pp. Because employment (a quantity) and prices move the same direction, uncertainty acts like a negative demand shifter / “pessimism,” not a freezer of actions.

Implications: Understanding subjective uncertainty requires going beyond rational-expectations models where uncertainty equals conditional volatility; learning is a promising alternative even for mature firms (median age 45 years). Decoupling of uncertainty from volatility matters for welfare and policy evaluation (misallocation, optimal policy under idiosyncratic risk).

In depth

Q1. What is the core measurement strategy, and why is span a valid index of subjective uncertainty?

The ifo module elicits best- and worst-case sales-growth scenarios; span (best minus worst) is the uncertainty measure, and the separate point forecast (answer 2b) is the subjective conditional mean. The authors model managers who think through a finite number n of scenarios to minimize expected quadratic loss based on distance from the closest scenario. Proposition 1 shows that if growth g = mu + sigma*epsilon belongs to a location-scale family, optimal span is linear in sigma (independent of mu), so span is proportional to subjective conditional standard deviation. Quadratic cost is a second-order approximation to general loss, making the link broad. Span is also robust/low-cognitive-load: it depends only on adjacent scenarios’ first-order conditions, so it is insensitive to interior reshaping or tail-shape changes managers cannot confidently distinguish.

Q2. What is the identification strategy for distinguishing uncertainty from conditional volatility, and what are the threats?

Identification rests on contrasting two observable implications. Under rational expectations (Example R), a cross-sectional uncertainty V must be accompanied by a cross-sectional volatility V in mean absolute forecast errors (Proposition R1), and a time-series uncertainty V must coincide with a ‘conditional-volatility V’ in absolute forecast errors (Proposition R2). Under learning (Example L), uncertainty can move with growth while debiased forecast-error volatility does not (Proposition L2). The authors test these by comparing span responses to forecast-error responses. The main threat is that span is only an index of subjective volatility (level not identified), so for the negative branch — where both uncertainty and volatility rise — they cannot fully rule out that higher uncertainty merely reflects higher conditional volatility. They argue against this because the implied span-to-volatility ratio (up to 4 in Table 4) would far exceed the roughly one-for-one cross-sectional relationship for most firms. For positive growth, the absence of any forecast-error response makes the rational-expectations explanation clean to reject.

Q3. What are the two competing mechanisms and how are they distinguished empirically?

Mechanism 1 (Example R, rational expectations): subjective uncertainty equals true conditional volatility, driven by heteroskedastic fundamentals; forecasts are unbiased. Mechanism 2 (Example L, learning about signal precision): growth is homoskedastic but managers observe a noisy signal of unknown information content gamma; using a Normal-Gamma prior with confidence parameter nu, an unfamiliar signal (far from prior mean, either sign) leads managers to infer lower precision and remain more uncertain, and generates forecast bias toward zero. Distinguishing tests: (a) cross section — shrinking firms are more uncertain AND biased holding volatility fixed (supports learning, Proposition L1b); large firms are less uncertain but unbiased (supports a confidence/nu channel, L1c); (b) time series — after positive growth, uncertainty rises but absolute forecast errors do not (rejects R2, supports L2); (c) the within-firm negative correlation between forecast and forecast error (-0.27) indicates overreaction from overprecision (Proposition L3). The preferred reading is a hybrid: a known volatility component generating the negative branch (R) plus a symmetric learning V (L).

Q4. What heterogeneity is documented across firms?

Three dimensions. Turbulence (time-series SD of growth): strongly raises uncertainty — top vs bottom quartile span 18 vs 7 pp, ~1.5 cross-sectional SDs, dummies explain 30%. Trend growth: asymmetric V — both fast-growing and fast-shrinking firms are more uncertain, but after controlling for turbulence only the bottom (shrinking) trend quartile retains a significant ~2 pp effect, and shrinking firms also have biased (too-conservative) forecasts, whereas fast-growing firms lose significance once volatility is controlled. Size: larger firms perceive less uncertainty — large (>250 employees) firms ~9 pp lower span unconditionally, ~5 pp lower controlling for trend and turbulence, but show no significant difference in average forecast errors (so the size effect is a confidence/nu channel, not bias). Time-series heteroskedasticity of span also rises with turbulence and trend and is larger for smaller firms, consistent with smaller firms having lower nu. Employment effects of uncertainty are similar across size classes (if anything slightly stronger for large firms).

Q5. What robustness checks are run?

Industry dummies (14 sectors) added to the cross-sectional span regression leave the turbulence/trend/size coefficients essentially unchanged and raise R-squared by only 2 pp, showing the effects are within-industry. Time and time-industry fixed effects confirm variation is overwhelmingly idiosyncratic (R-squared ~1% rising to ~5-7%). The within-firm uncertainty results are robust to requiring at least 5 span observations per firm (Table I4), as are the employment/price-plan results (Tables I6). Deseasonalization is corroborated at macro and micro level (Appendix B). Forecast-error analyses use a debiased absolute forecast error (residual from regressing forecast error on past growth and firm fixed effects) to separate volatility from bias, and a ‘statistical forecast error’ (deviation of growth from firm mean) as an econometrician benchmark, both giving the same V/no-V patterns. Data quality is documented: ~73-86% of respondents are top management, the responder is the same person in ~98% of firms, ~80% of firms use in-house quantitative planning, and a majority rely on scenario analysis.

It builds on survey-based ‘micro uncertainty’ work (Guiso and Parigi 1999; Bontempi et al. 2010; Bachmann, Elstner and Sims 2013). Several papers found V-shapes between subjective uncertainty and lagged sales growth (Altig et al. 2022 Atlanta Fed SBU; Bloom et al. 2020 MOPS; Kumar, Gorodnichenko and Coibion 2023 New Zealand), but those use single cross sections or short pooled samples and cannot separate cross-sectional from time-series Vs. The contribution is decomposing the V into between- and within-firm components and constructing volatility Vs to contrast against the uncertainty Vs, showing uncertainty is more than volatility. It also connects to the behavioral/miscalibration literature (Ben-David, Graham and Harvey 2013; Barrero 2022) by linking forecast bias to the gap between subjective uncertainty and conditional volatility via endogenous perceived precision. Uniquely, it studies subjective idiosyncratic uncertainty jointly with both a quantity (employment) and prices in normal (non-recession) times; Kumar et al. (2023) found ‘uncertainty as pessimism’ but for a macro variable (GDP).

Q7. What are the policy and modeling implications, and their scope conditions?

The decoupling of uncertainty from volatility matters for welfare and policy because the standard approach (regress absolute forecast errors on conditioning information and use the fitted value as uncertainty) measures ’too little’ uncertainty — it ignores uncertainty about features the econometrician sees only with hindsight. Heterogeneous-firm models of misallocation and optimal policy under idiosyncratic risk (e.g., Boar et al. 2025; Di Tella et al. 2025) should incorporate uncertainty distinct from volatility. Models of firm dynamics need either heteroskedastic innovations or sufficient nonlinearity, plus feedback from past growth to uncertainty (learning), and should treat idiosyncratic demand uncertainty as a driver of employment churn and price dispersion even in steady state. Scope conditions: the evidence is German manufacturing, 2013-2019, a calm idiosyncratic-shock-dominated period (so results speak to idiosyncratic, not aggregate, uncertainty); span identifies relative not absolute uncertainty; for idiosyncratic uncertainty to affect actions, firm decisions must depend on it (manager career concerns, closely-held ownership, or ambiguity/Knightian uncertainty defeating diversification). The authors note the decoupling principle extends to policy uncertainty (e.g., tariffs) even when realized paths are not volatile.

Q8. What does the ‘uncertainty as a negative demand shifter’ result tell us about the type of shocks managers fear?

Because higher span lowers BOTH planned employment (a quantity) and planned prices in the same direction, the comovement indicates that managers primarily worry about demand shortfalls rather than cost shocks. A firm fearing a demand shortfall scales down production (sheds workers) and lowers prices; a firm fearing input-cost increases would still cut employment but RAISE prices. The observed pattern therefore points to idiosyncratic, subjective demand uncertainty as the relevant primitive, and (with financial frictions or risk/ambiguity-averse decision-makers placing more weight on low-payoff states) explains why uncertainty ‘acts like pessimism’ rather than freezing actions.

Q9. What are the key caveats and limitations?

Span is an index of subjective volatility, so levels and the exact span-to-volatility ratio are not point-identified, leaving residual ambiguity on the negative branch where uncertainty and volatility both rise. The sample is non-recessionary German manufacturing, so results characterize idiosyncratic (not aggregate) uncertainty; the authors explicitly note variation is essentially all idiosyncratic. The learning examples abstract from explicit dynamics (the prior is held fixed each period), serving as stark illustrations rather than a fully dynamic structural model; the data are interpreted through a hybrid of R and L. The plan outcomes are qualitative (up/down/same) and ifo does not elicit realized outcomes suitable for the authors’ purposes, so the link to realized employment/prices relies on external evidence that ifo indicators forecast those variables.

Key Concepts

Understanding High-Wage Firms: Monopoly, Monopsony, and Bargaining Power

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: Why do some firms pay persistently higher wages for observably similar workers, and what role do firms’ product-market power (monopoly/markups), labor-market power (monopsony/markdowns), and workers’ collective bargaining power play in shaping wages and welfare? Prior literature studies labor-market power as a driver of wages/profits but abstracts from product-market power and bargaining, while the markups literature abstracts from imperfect labor competition and bargaining. The paper unifies all three in one structural framework.

Central theoretical insight: A firm’s wage equals its marginal revenue product of labor (MRPL) times a “labor wedge” (the share of MRPL workers receive). The labor wedge decomposes into three components — price-cost markups, monopsony markdowns, and bargaining power — via equation (3): Lambda = kappa*(product market rents term) + (1-kappa)*lambda. With positive bargaining power (kappa>0) workers capture a share of markup-generated rents, so the labor wedge rises with markups (rent-sharing); this nests pure monopsony as the kappa=0 special case.

Data and setting: French administrative micro-data. Firm balance sheets (FARE, 2008-2019, DGFiP); firm-product output prices (EAP survey, 2009-2019, INSEE, manufacturing firms >=20 employees or sales >5m euros); matched employer-employee data (DADS, 1995-2018) which crucially includes hours worked. Firm wage premia estimated via a k-means/BLM grouped AKM regression (Bonhomme, Lamadon, Manresa 2019). Markups and labor wedges estimated with the production-function/production approach (De Loecker-Warzynski 2012; Yeh et al. 2022) using translog functions and an Ackerberg-Frazer-Caves control function, separating the two by noting markups distort all input demands while labor wedges distort only labor demand.

Two key empirical facts a standard monopsony model cannot explain: (i) high-wage firms charge higher output prices and markups; (ii) high-wage firms pay a larger share of MRPL as wages (higher labor wedges). Both persist within narrow industries and conditional on TFP, pointing to product quality and positive bargaining power.

Main quantitative findings (French manufacturing, 2016 unless noted): Median markup 1.32 (IQR 1.14-1.60). Median labor wedge 0.62 (median monopsony markdown 0.46) — the gap is due to bargaining power and markups. Workers capture about 12% of firm profits (bargaining power kappa ~ 0.12-0.14; falls to ~0.05-0.13 under IV correction). Median markdown 0.46 implies a median firm-specific labor supply elasticity of 0.85. Accounting for hours matters: median labor wedge is 0.62 with effective hours, 0.65/0.68/0.71 across specifications, rising to 0.71 when labor is measured by employment (near Yeh et al.’s 0.70-0.73 US figures) — so omitting hours upward-biases labor wedges.

Quantitative GE model (oligopoly/oligopsony, nested-CES, Atkeson-Burstein/Berger et al.): A 1% productivity shock has wage passthrough 0.97-0.99 versus 0.23 for an equal quality shock (because varieties are close substitutes, sigma=5.17), though quality still generates more wage-premium dispersion. Markups and markdowns reduce welfare by 46% in consumption-equivalent terms, with markups alone accounting for over 80%; misallocation explains about 63% of the markup welfare cost. Equalizing markups raises average wages 39% and wage variance 99% and welfare 24% (output-restriction effect dominates rent-sharing, so equalizing markups raises wage dispersion). Raising bargaining power from 0.12 to 0.50 matches the wage gains of removing markups but yields only 10% welfare gain (vs 38%); full bargaining power (kappa=1) raises welfare 13%, under one-third of the planner’s 46% gain. Bargaining power offsets the uniform-tax and misallocation distortions on labor demand but cannot fix markup distortions to capital/material demand.

In depth

Q1. What is the core identification strategy for separating markups from labor wedges, and what are its main assumptions/threats?

The author applies the production approach: estimate translog production functions per 2-digit manufacturing sector (via two-step GMM with an Ackerberg-Frazer-Caves control function for unobserved productivity) to recover firm-specific output elasticities. Markups distort the demand for ALL inputs while labor wedges distort ONLY labor demand, so choosing materials as a flexible, price-taken input lets markups be identified from the material cost share (mu = alpha_m * PY/(Pm*M)) and labor wedges from the wage-bill-to-materials ratio scaled by elasticity ratios (eq. 4). Key assumptions/threats: materials must be a flexible input firms take prices for (examined in Appendix B.7-B.8); unobserved productivity must satisfy scalar unobservability and monotonicity in material demand; unobserved output and input prices bias elasticities — addressed using observed EAP output prices (measuring output in quantities) plus the De Loecker et al. (2016) input-price control function, and additionally controlling for firm wage premia because monopsony markdowns create unobserved labor-price variation. Markup variation driven by idiosyncratic demand uncorrelated with TFP is controlled via export status, market shares, firm age, and a 3rd-order price polynomial. Gandhi-Navarro-Rivers concerns about identifying material elasticities are addressed in Appendix B.9.

Q2. What is the new identification challenge for estimating bargaining power, and how is it solved?

The rent-sharing literature estimates bargaining power kappa by regressing wages on quasi-rents using instruments (export demand, patent shocks) assumed orthogonal to the worker’s reservation wage. But in this model, when kappa=0 workers earn an endogenous monopsony wage (lambda*MRPL) that moves with the SAME firm-specific shocks (productivity, quality, amenities) that shift quasi-rents — so standard instruments violate the exclusion restriction. The solution: instead of the wage equation, exploit the labor-wedge equation (3), which relates labor wedges to markups and avoids unobserved monopsony wages. Conditional on markdowns, variation in product-market rents identifies kappa (when kappa=0 product-market rents do not affect the labor wedge). This shifts the core challenge from unobserved monopsony wages to unobserved amenities (mirroring IC3 in the rent-sharing literature), handled by a theory-consistent control function in which employment and the wage bill jointly proxy for amenities under a monotonicity assumption (labor supply increasing in amenities). Under multiplicative separability of wages and amenities, markdowns do not depend directly on amenities, so unobserved amenities do not bias kappa at all.

Q3. What are the bargaining-power estimates across specifications?

Pooled OLS gives ~0.135; adding firm fixed effects ~0.124; adding the amenity control function (columns 3-4) ~0.124-0.135, indicating amenities have little direct effect on markdowns; instrumenting product-market rents with their lags to correct correlated measurement error (columns 5-6) gives 0.130 and 0.059. Baseline kappa is taken as ~0.12 (specification 4). All 2-digit sectors have kappa below 0.3. These align with the rent-sharing literature’s typical 0.05-0.15, though external innovation-based instruments tend to find ~0.30.

Q4. How does the paper measure firm wage premia and why not use standard AKM?

Standard AKM firm effects assume time-invariant firm effects and rely on worker mobility; short panels yield noisy estimates with upward-biased variance. The author needs time-varying premia (to measure effective labor over time). He uses the BLM (Bonhomme, Lamadon, Manresa 2019) k-means approach: cluster firms by the similarity of their internal wage distributions (by 2-digit sector over overlapping 2-year windows), then run an AKM-style regression with firm-GROUP effects that vary by year, identified by workers switching between firm-groups — greatly increasing the number of switchers. DADS-Postes is used for clustering (broad coverage) and DADS-Panel for the wage-premium regression.

Q5. What heterogeneity is documented across firms?

Firm wage premia dispersion accounts for 5.2% of wage dispersion; the 90-10 premium gap is ~30% (about 4 euros/hour, 25% of the median worker’s hourly wage), IQR 15%. Markdowns increase with firm wage premia (flat gradient) but DECREASE with firm size — larger firms have more monopsony power, consistent with oligopsony models. Firm-specific labor supply elasticities are 0.54/0.85/1.33 at the 25th/50th/75th percentiles. About 7% of firms have labor wedges above 1, and these tend to have much higher markups (rationalized by kappa>0). In the GE model, top-decile high-wage firms are ~15% more productive but have over 100% greater product quality than bottom-decile firms; amenities rise slightly more steeply with premia than productivity. Passthrough is substantially smaller for 90th-percentile firms (0.74 productivity, 0.18 quality) than for median/10th-percentile firms (~1.06/~0.26).

Q6. How is the dispersion of wage premia decomposed across sources of firm heterogeneity?

Introducing one source at a time into the GE model and comparing variance to baseline (Table 6): varying only product quality reproduces 161.5% of baseline variance, only TFP 153.3%, and only amenities 40.8%. Product quality is the largest single contributor to wage-premium dispersion, closely followed by productivity, then amenities.

Q7. Why does the productivity passthrough differ so much from the quality passthrough?

Total passthrough is 0.97 for a 1% productivity shock vs 0.23 for an equal quality shock (~4x). The decomposition (Table 5) attributes most of the gap to the direct effect (1.07 vs 0.26): with high within-market substitutability (sigma=5.17), consumers are very price-sensitive, so productivity (which lowers price) moves sales and labor demand far more than quality. Higher sigma raises productivity passthrough but lowers quality passthrough. For sufficiently low sigma the ranking can reverse. The variable-market-power channel also matters: higher productivity raises markups, increasing rent-sharing (+0.06 via labor wedge) but also output restriction (-0.09 via markup), with output restriction dominating; firm-size effects (sectoral price -0.10, sectoral wage +0.03) further adjust passthrough. Amenity shocks have direct effect -0.26 (mirror of quality) but total -0.28, amplified because better amenities lower hiring costs and expand the firm.

Q8. How does worker bargaining power affect welfare, and what are the limits?

Bargaining power offsets two distortions firm market power imposes on aggregate labor demand: a uniform tax (Lambda/mu, lowering labor demand proportionally) and a misallocation tax (Theta, from dispersion in wedges). There exists a kappa-bar that exactly cancels the uniform tax, and kappa-bar falls as markups rise (high markups make bargaining more effective). With full bargaining power and common markups, the markdown-driven misallocation tax is fully neutralized. BUT bargaining only acts through labor demand; markups also distort capital and material demand, which bargaining cannot fix. Quantitatively: raising kappa from 0.12 to 0.50 matches the wage gain of removing markups but yields only 10% welfare gain (vs 38%) and far less dispersion increase; full kappa=1 raises welfare 13%, under one-third of the planner’s 46% gain. So bargaining power is a partial, not full, remedy for firm market power.

Q9. What is the welfare accounting for markups vs markdowns?

Comparing the decentralized economy to the social planner’s (Table 7, column 3): eliminating both markups and markdowns raises wage-premium dispersion 113%, average wages 303%, and welfare 46% (consumption-equivalent). Over 80% of the welfare gain comes from removing markups. Equalizing markups alone (column 4) gives 24% welfare, +39% wages, +99% wage variance, implying ~63% of the markup welfare cost is misallocation. Equalizing markdowns alone (column 5) has little welfare effect (2%), though a wide markdown level reduces welfare significantly (column 2).

Q10. What robustness checks and caveats does the author flag?

Caveats: (1) Multiplication bias — mismeasured output elasticities enter both labor wedges and product-market rents multiplicatively, mechanically biasing kappa upward (Appendix B.10); IV with lags only fixes classical, not serially-correlated, measurement error. (2) Labor adjustment costs get absorbed into the labor wedge and bias kappa; firm fixed effects do not fully fix this (Appendix B.11). (3) The markdown estimation imposes that all markdown variation reflects firm size and amenities — more general than kappa=0 approaches but restrictive in this dimension. (4) The model uses collective (not individual) bargaining and abstracts from sequential-auction wage-setting (Cahuc-Postel-Vinay-Robin); robustness to hiring-wages-only following Di Addario et al. (2020) is shown (Appendix B). (5) Worker types assumed perfect substitutes; an Appendix E two-skill extension gives similar results. (6) Empirical patterns hold without TFPQ controls (Figure D.3) and by firm size (Figure D.4).

Versus the labor-market-power literature (Berger et al. 2022; Lamadon et al. 2022) it adds product-market power and bargaining, showing their pure-monopsony labor wedge is a kappa=0 special case. Versus the markups/welfare literature (De Loecker et al. 2020; Edmond et al. 2023) it adds imperfect labor competition and bargaining. Versus recent integrated product+labor power models that use wage-posting and no bargaining (Kroft et al. 2024; Deb et al. 2024), it adds the rent-sharing channel where markups raise (not just lower) the labor wedge. Versus production-approach markdown estimation (Yeh et al. 2022; Mertens 2020), it shows their estimates are labor wedges (not markdowns) once kappa>0, and that omitting hours upward-biases them. Versus the rent-sharing literature (Card et al. 2018; Kline et al. 2019; Van Reenen 1996), it shows their instruments violate exclusion under endogenous monopsony wages and proposes the labor-wedge-equation alternative. The closest exception incorporating unions is Azkarate-Askasua and Zerecero (2025).

Q12. What are the policy implications and their scope conditions?

Strengthening worker collective bargaining power can raise welfare mainly by offsetting markup-induced distortions to labor demand and redistributing rents, but it raises between-firm wage inequality and cannot restore full efficiency because it leaves markup distortions to capital/material untouched (full kappa closes under one-third of the planner gap). The wage effects of innovation depend on whether it improves productivity or quality and on the degree of product differentiation. Scope conditions: estimates are for French manufacturing under firm-level collective bargaining institutions (firms >=50 employees legally bargain annually); results rely on the production-approach assumptions (flexible/price-taken materials, scalar unobservability) and on data including hours and output prices that many countries lack — researchers should interpret labor-wedge/markup moments cautiously without hours data.

Key Concepts

A Goldilocks Theory of Fiscal Deficits

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

This paper develops a tractable continuous-time model to study the fiscal sustainability of government deficits and the joint dynamics of public debt, with two main ingredients: an endogenous interest rate R that rises with the debt level through a convenience yield mechanism (savers value holding government bonds), and a potentially binding zero lower bound (ZLB) on the nominal interest rate. The paper’s central theoretical contribution is deriving the correct free-lunch condition: not the commonly cited $R < G$, but the stricter condition $R < G - \varphi$, where $\varphi$ captures the sensitivity of $R - G$ to debt. Even when $R < G$, accumulating more debt raises R through reduced convenience yields, and this endogenous feedback tightens fiscal sustainability. The paper maps the full deficit-debt space with a hump-shaped locus, analyzes ZLB dynamics where the deficit-debt relationship can invert, and studies the role of income inequality and tax policy. Calibrating to U.S. and Japan as of December 2019, the paper finds little room for free-lunch policies in the U.S. — a maximum permanent deficit of just over 2% of GDP at a stable debt-to-GDP ratio of 110% — while Japan is in the “inverted” ZLB regime where deficit increases can reduce debt through higher nominal growth.

Summary of a published paper based on the NBER working paper full text (w29707), AI-assisted, pending human review. See the linked original for the authoritative claims and full conditions.

Layer 1: Overview

Mian, Straub, and Sufi construct a tractable deterministic continuous-time model with savers who derive convenience utility from holding government bonds, hand-to-mouth spenders, and a monetary authority that targets inflation (except at the ZLB), to systematically analyze when deficits can be “free lunches.” The core insight is that the standard r < g analysis treats interest rates as exogenous to the debt level, but if R rises as debt accumulates — through the declining marginal convenience yield of bonds — then the condition for a free-lunch policy is not R < G but R < G − φ. This matters empirically: the paper estimates φ (the debt-to-interest-rate sensitivity) from empirical estimates of the convenience yield elasticity, and calibrates the model to U.S. and Japan December 2019 conditions. The U.S. calibration finds a maximum free-lunch deficit of just over 2% of GDP at a stable debt ratio of 110%, implying the U.S. was barely inside the free-lunch region pre-Covid. By contrast, the paper finds ample free-lunch space for Japan and an “inverted” ZLB regime in which higher deficits can reduce the debt-to-GDP ratio by stimulating nominal growth. The analysis is extended to incorporate aggregate risk, capital, debt maturity structure, and inequality — each with distinct implications for the size and location of fiscal space.

In depth

Q1. What is the deficit-debt diagram, and what is the free-lunch condition?

The deficit-debt diagram is the locus of steady-state combinations of the primary deficit z and the debt-to-GDP ratio b, derived from the government budget constraint $\dot{b} = -(G^ - R^(b))b + z$ at steady state; this locus is hump-shaped, with the maximum sustainable permanent deficit z occurring at the debt level b where $R^(b^) = G^* - \varphi(b^)$.** The hump shape arises because at low debt levels the convenience yield is high (R is low relative to G, allowing large deficits), while at high debt levels the convenience yield is saturated (R rises toward G, leaving little deficit room). The left branch of the locus — where debt levels are below b — is the free-lunch region: any permanent increase in the deficit to a value below z* raises the steady-state debt level but requires no future tax increases. The right branch — debt above b* — is the conventional region: any deficit increase must eventually be accompanied by higher taxes. The key departure from the standard r < g analysis is that R is endogenous; Proposition 1 and Corollary 1 formally establish that the correct free-lunch threshold is $R^(b_0) < G^ - \varphi(b_0)$, not simply R < G.

Q2. Why is R < G insufficient as a free-lunch condition, and what does φ capture?

The condition R < G fails as a free-lunch criterion because, when the government borrows an additional dollar and rolls it over forever, it faces two opposing budget effects: a positive cash flow of G − R from rolling over the existing debt, and a tightening of the budget constraint from the endogenous rise in R on all infra-marginal outstanding debt; the parameter φ measures the magnitude of this second effect as the semi-elasticity of R − G with respect to the log of debt. When φ is positive — as it is empirically because convenience yields are declining in debt supply — the net fiscal benefit of rolling over additional debt is G − R − φ, not G − R. An economy can exhibit R < G yet be in the conventional debt region if φ is sufficiently large that R > G − φ at the current debt level. The U.S. calibration illustrates this: the traditional R < G condition holds up to a debt ratio of 220% of GDP, but the stricter R < G − φ condition breaks down already at 110%, which is the actual boundary of the free-lunch region for the U.S.

Q3. How does the analysis change at the zero lower bound, and what is the “inverted” fiscal regime?

At the ZLB, the direction of causality reverses: instead of the debt level determining the interest rate, the debt level determines the nominal growth rate G (via aggregate demand and the Phillips curve), creating an “inverted” regime in which higher deficits can reduce rather than increase debt by stimulating nominal growth and inflating away the debt. The mechanism is: when the nominal rate is constrained at zero, fiscal expansion raises aggregate demand, which via the Phillips curve (slope κ) raises inflation, which raises nominal growth G, which accelerates the inflation of the debt ratio. If the fiscal multiplier times κ times the debt level exceeds one — a sufficient statistic condition — then higher deficits reduce the debt ratio. The paper finds this condition plausible for Japan (debt ratio ~225%, estimated κ = 0.1-0.3, multipliers of 1.5-2) but not for the U.S. in 2019. The deficit-debt locus in this regime is “backward-bending”: as the ZLB binds more tightly (lower debt), the locus can curve back and eventually allow the inverted relationship between deficits and debt.

Q4. How does income inequality affect fiscal space, and why does the ZLB reverse the sign?

Outside the ZLB, greater income inequality (a larger income share of savers relative to hand-to-mouth spenders) expands fiscal space, because savers have a higher propensity to save, which reduces the natural interest rate R and thus raises G − R and allows larger sustainable deficits; at the ZLB, greater inequality shrinks fiscal space, because it reduces aggregate demand and hence nominal growth G rather than R.* Formally, outside the ZLB: $z(b) = (v’(b)(1-x-\mu) - \rho)b$, which increases as the spender share μ falls (Corollary 3). At the ZLB, nominal growth G becomes demand-determined via equation (20), and lower μ reduces demand, lowering G and hence z(b). The policy implication is a potential conflict between redistributive policies and deficit finance: redistribution (raising μ) reduces fiscal space outside the ZLB but expands it at the ZLB. The paper notes that roughly 69% of U.S. government debt held by households is directly or indirectly held by the top 10% of the wealth distribution, making savers’ saving propensity the primary driver of the convenience yield.

Q5. What are the U.S. and Japan calibration results for fiscal space as of December 2019?

For the U.S. in December 2019, the model calibrates a maximum permanent primary deficit z of just over 2% of GDP at a stable debt-to-GDP ratio of b ≈ 110%, implying the U.S. was just inside the free-lunch region; for Japan, the model finds the economy in the inverted ZLB regime where higher deficits reduce debt by raising nominal growth.** The calibration uses empirical estimates of φ from the literature on convenience yield demand elasticities (Krishnamurthy and Vissing-Jorgensen 2012, Laubach 2009, Presbitero and Wiriadinata 2020). For the U.S., the standard r < g condition holds up to a debt ratio of 220% (the upper bound), but the binding free-lunch condition R < G − φ limits fiscal space to 110%. Deficits beyond the 2%-of-GDP limit must be financed by future tax increases or spending cuts, even though R < G throughout the range. The Japan calibration illustrates the ZLB regime: with a debt ratio already above 200%, the fiscal multiplier effect on inflation is large enough that the backward-bending locus applies, and Japan’s economy lies in the inverted region.

Q6. How does the analysis extend to aggregate risk, capital crowding-out, and debt maturity?

With aggregate risk, the free-lunch condition R < G − φ remains informative: when the condition holds on average, free-lunch policies can be designed with probability approaching one; when it fails on average, no free lunch is possible. The risk extension follows Mehrotra and Sergeyev (2020) and confirms numerically that the deterministic condition provides a valid signal for the stochastic case. Adding capital and crowding-out (Section 7.2) yields a counterintuitive finding: greater crowding-out of capital actually increases fiscal space by reducing the sensitivity of interest rates to debt (lower φ), because each additional unit of government debt displaces private capital rather than reducing convenience yields as sharply. Regarding debt maturity: issuing long-term debt reduces fiscal space at low debt levels (locking in higher interest costs), but increases it at high debt levels; this suggests that QE-style maturity shortening may constrain fiscal space as debt rises. These extensions confirm that the φ parameter — and the R < G − φ condition — is robust to a range of model ingredients, making it a practically useful criterion beyond the baseline model.

Key Concepts

free-lunch fiscal policy : a permanent increase in the primary deficit that raises steady-state debt to a new higher level without requiring any future tax increases or spending cuts; feasible only when $R^(b_0) < G^ - \varphi(b_0)$, which is strictly tighter than the standard r < g condition when φ > 0.

debt-rate sensitivity (φ) : the semi-elasticity of R − G with respect to the log of debt, capturing how much the endogenous convenience yield on government bonds falls (and hence interest rates rise) as the debt supply increases; the paper’s addition to the standard r < g framework that tightens the sustainability condition from R < G to R < G − φ; estimated empirically from convenience yield demand curves.

deficit-debt diagram : the hump-shaped locus of sustainable steady-state combinations of the primary deficit and the debt-to-GDP ratio; the left (increasing) branch is the free-lunch region where fiscal expansion is self-sustaining, and the right (decreasing) branch is the conventional region where fiscal expansion requires future tax increases.

inverted ZLB fiscal regime : the case where the nominal interest rate is zero and the deficit-debt locus bends backward, so that higher deficits reduce rather than increase the debt ratio; occurs when the fiscal multiplier is large enough that deficit-induced nominal growth more than offsets the direct debt accumulation effect; found to apply to Japan as of December 2019 but not the U.S.

convenience yield : the non-pecuniary benefit savers derive from holding government bonds (capturing liquidity, safety, and regulatory premia), modeled as the utility function v(b) for savers; the mechanism making R endogenous to debt: as debt supply rises, the marginal convenience yield v’(b) falls, pushing R toward G and shrinking fiscal space.

A Preferred-Habitat Model of Term Premia, Exchange Rates, and Monetary Policy Spillovers

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

Layer 1 — Core Argument

The paper develops a two-country preferred-habitat model in which currency and bond markets are populated by different investor clienteles — currency traders with price-elastic demand for foreign assets, and bond investors whose preferences are habitat-specific by country and maturity — with segmentation partly overcome by global arbitrageurs who have limited capital and bear mean-variance risk. Risk premia in the model are time-varying, connected across markets, and consistent with the empirical violations of Uncovered Interest Parity (UIP) and the Expectations Hypothesis (EH): in particular, currency carry trade (CCT) and bond carry trade (BCT) strategies earn abnormally high expected returns in ways that co-vary across the two markets in a manner the standard frictionless model cannot generate. Through these time-varying, connected risk premia, large-scale bond purchases (QE) lower domestic bond yields, lower foreign bond yields, and depreciate the purchasing country’s currency; short-rate cuts also lower foreign yields, but with smaller effects than bond purchases. A key structural finding, quantified in the estimated model calibrated to US and Eurozone data, is that currency returns are nearly uncorrelated with long-maturity bond returns — an exchange-rate disconnect — yet the currency market is instrumental in transmitting bond demand shocks across countries, because arbitrageurs hedge their cross-currency positions in bond markets and vice versa. Sterilized foreign-exchange interventions have strong effects on the exchange rate but weak effects on bond yields, while QE/QT has weak effects on the exchange rate but sizeable effects on foreign bond yields — a sharp asymmetry that follows directly from the disconnect.

In depth

Q1. Why do UIP and EH fail in the standard model, and what changes in this model?

In the standard model with perfect capital mobility, risk premia are constant, so the yield curve depends only on expectations of the domestic short rate and the exchange rate absorbs short-rate differentials exactly. In this model, arbitrageurs bear the residual risk when currency traders and bond clienteles are unwilling to absorb excess supply or demand at prevailing prices. Because arbitrageurs have limited capital (captured by a risk-aversion parameter a ≥ 0 that can also represent capital or Value-at-Risk constraints in reduced form), they demand compensation — time-varying risk premia — for holding currency and maturity risk. When a = 0, arbitrageurs are risk-neutral, UIP and EH both hold, and the model collapses to the standard frictionless benchmark.

Q2. What are the three types of agents and what does each do?

Currency traders hold foreign assets and have a demand that is downward-sloping (price-elastic, with slope coefficient αe ≥ 0) in the log exchange rate; their demand also shifts with a stochastic currency demand factor γt. They can be interpreted as households engaged in expenditure switching or central banks managing reserve levels. Bond investors form clienteles, each with a preferred-habitat demand for bonds of a specific country and maturity that is downward-sloping in the log bond price (slope αj(τ)) and shifts with a country-specific bond demand factor βjt; examples are pension funds and insurance companies whose liabilities are long-dated and denominated in their home currency. Global arbitrageurs trade the currency and all bonds of both countries, maximizing mean-variance utility over instantaneous wealth changes; they bridge the segmented markets and their positions pin down equilibrium risk premia.

Q3. What is the equilibrium structure and which factors drive prices?

The equilibrium exchange rate and bond prices are log-affine functions of five stochastic factors: the home short rate iHt, the foreign short rate iFt, the currency demand factor γt, and the two bond demand factors βHt and βFt. These factors follow a mean-reverting (Ornstein-Uhlenbeck) system. The equilibrium is characterized by a scalar nonlinear system (25 equations in the general case) whose solution pins down the loadings of prices on each factor. This affine structure means each asset’s risk premium is the product of the arbitrageur’s risk-aversion coefficient, the factor covariance matrix, and arbitrageur net positions, which are themselves determined by market-clearing.

Q4. How does a conventional short-rate cut transmit domestically and internationally in the model?

Following a home short-rate cut, arbitrageurs find it attractive to enter the CCT — borrow home currency, invest in foreign currency. If currency traders’ demand is price-elastic (αe > 0), arbitrageurs’ equilibrium foreign-currency holdings rise, and the expected return on the CCT rises too (arbitrageurs must be compensated for the increased risk). This attenuation effect means the foreign currency appreciates less than implied by UIP: the exchange rate response is dampened. Simultaneously, arbitrageurs enter the home BCT (borrow at the home short rate, invest in long home bonds); if home bond investors’ demand is price-elastic (αH(τ) > 0), arbitrageurs’ long-bond holdings rise and the BCT’s expected return rises, attenuating the transmission to domestic long-maturity yields (which fall less than EH would imply). A propagation effect to foreign bond yields arises through arbitrageur hedging: by taking long positions in foreign currency (CCT), arbitrageurs become exposed to the risk that the foreign short rate drops and the foreign currency depreciates; long-maturity foreign bonds provide a natural hedge (their price rises when the foreign short rate drops), so arbitrageurs increase foreign bond demand, depressing foreign yields. This international transmission of conventional policy is absent from the standard model.

Q5. How does unconventional policy (QE/QT) transmit domestically and to the exchange rate and foreign yields?

Following QE purchases of home bonds, their prices rise; arbitrageurs accommodate by holding fewer home bonds, which reduces their exposure to home short-rate risk. With less home-rate risk, arbitrageurs become more willing to hold foreign currency (which depreciates when the home short rate rises, offering a natural hedge against the home rate risk they have shed). The increased foreign-currency position in turn makes arbitrageurs more willing to hold foreign bonds (which hedge the foreign-currency position against foreign rate changes). The net result in the model is: QE lowers domestic bond yields, lowers foreign bond yields, and depreciates the home currency. The quantitative finding from the estimated model is that QE/QT effects on foreign bond yields are sizeable and stronger than those of conventional short-rate policy.

Q6. What explains the exchange-rate disconnect, and how can the currency market still transmit bond demand shocks?

In the estimated model, variance decompositions reveal that long-maturity bond yields in each country are driven primarily by bond demand factors (βHt and βFt), while the exchange rate is driven primarily by the currency demand factor (γt); short rates account for a small fraction of movements in both, and each factor type accounts for negligible variation in the other asset class’s price. The disconnect between bond yields and the exchange rate arises because bond demand shocks in the two countries move the exchange rate in opposite directions — a home bond demand shock that lowers home yields also raises the exchange rate via arbitrageur hedging, while a foreign bond demand shock moves the exchange rate in the opposite direction. These offsetting effects make the exchange rate nearly uncorrelated with long-maturity bond yields. However, bond demand shocks in one country are transmitted to bond yields in the other country through the currency market: arbitrageurs hedge their bond positions using the currency, so a shock to home bond demand moves arbitrageurs’ currency positions, which in turn affects their willingness to hold foreign bonds. Cross-country bond yield comovement is therefore positive and sizeable, despite the exchange-rate disconnect.

Q7. What are the model’s implications for foreign exchange intervention?

A sterilized purchase of foreign currency by the home or foreign central bank — which shifts the currency demand factor — has strong effects on the exchange rate but weak effects on bond yields. This follows directly from the variance decomposition: the exchange rate loads heavily on the currency demand factor and bond yields load lightly on it. The asymmetry mirrors the QE result in reverse: QE shifts bond demand factors, which load heavily onto bond yields and lightly onto the exchange rate; FX intervention shifts the currency demand factor, which loads heavily onto the exchange rate and lightly onto bond yields. The model thus delivers a sharp policy instrument separation between QE/QT (primarily a bond yield tool) and FX intervention (primarily an exchange-rate tool), with each having spillovers in the other dimension that are quantitatively weaker.

Q8. How is the relationship between currency risk premia and bond risk premia captured, and what empirical regularities does the model match?

The model’s risk premia are linked through the shared arbitrageur portfolio: the price of each risk factor is proportional to the covariance between that factor and the arbitrageur’s overall portfolio return, so a shock that changes arbitrageurs’ currency positions also changes the compensation required for bond positions, and vice versa. The estimated model is reported to match closely the violations of UIP (CCT profitability) and EH (BCT profitability) documented in the literature, and the ways in which these violations are connected — including findings that yield-curve slope differentials predict CCT profitability, and that CCT profitability declines when carried out with long-maturity rather than short-maturity bonds. These matches are described as consistent with the empirical regularities, not structural identification of the underlying causes.

Q9. What is the role of segmented versus global arbitrage, and why does the distinction matter?

The paper considers both cases. Under segmented arbitrage, separate arbitrageur pools operate in the currency market (risk aversion ae), home bond market (aH), and foreign bond market (aF); first-order conditions for each pool reflect only their own portfolio risk, so the prices of risk factors differ across markets. Under global arbitrage, a single pool of arbitrageurs trades all assets, and their shared portfolio means the price of each risk factor is the same across currency and bond markets — this is the mechanism through which bond demand shocks in one country propagate through the currency market to bond yields in the other. Global arbitrage is the primary specification; segmented arbitrage serves as a benchmark to isolate the hedging-based transmission channel that requires global positions.

Q10. How does the model relate to and extend predecessor frameworks?

The model extends Vayanos and Vila (2021) — a closed-economy preferred-habitat yield curve model — to two countries by adding a currency market and a second country’s bond market, with arbitrageurs who are global rather than country-specific. In the currency dimension, the attenuation of UIP deviations parallels Gabaix and Maggiori (2015), which models exchange-rate dynamics with financially constrained intermediaries but without a yield curve. The two-country structure allows the paper to simultaneously study term premia (EH violations), exchange rate dynamics (UIP violations), and their connection, and to quantify the effects of QE, conventional monetary policy, and FX intervention within a single internally consistent framework estimated on US-Eurozone data.

Key Concepts

Preferred-habitat demand: A bond investor’s demand for bonds of a specific country and maturity that does not arise from portfolio optimization over the full menu of available assets, but rather from institutional constraints or liability-matching motives (e.g., pension funds matching long-dated domestic liabilities). In the model, preferred-habitat demand is price-elastic with slope αj(τ) and shifts with a country-specific bond demand factor βjt; the elastic component means that as bond prices rise, clientele demand falls, so arbitrageurs must absorb the residual supply and require a risk premium to do so.

Global arbitrageur: An investor who trades the currency and bonds of both countries simultaneously, bridging the segmented currency and bond markets. In the model, global arbitrageurs maximize mean-variance utility over instantaneous wealth changes; their shared portfolio across all asset classes is the mechanism through which shocks in one market create hedging-driven demand in other markets, generating the cross-market linkages in risk premia and monetary policy transmission.

Currency carry trade (CCT): A strategy that borrows at the home short rate and invests at the foreign short rate, profiting when the foreign currency does not depreciate enough to offset the interest rate differential. Under UIP, the CCT earns zero expected return; the model generates a positive expected CCT return — a currency risk premium — when arbitrageurs are risk-averse and currency traders’ demand is price-elastic. In the paper’s notation, the CCT return is det/et + (iFt − iHt)dt.

Bond carry trade (BCT): A strategy that borrows at the short rate and invests in long-maturity bonds of the same country, profiting when long yields fall or when expected short rates are below current long yields. Under EH, the BCT earns zero expected return; the model generates a positive expected BCT return — a term premium — when arbitrageurs are risk-averse and bond clientele demand is price-elastic.

Exchange-rate disconnect: The empirical and model finding that movements in the exchange rate are nearly uncorrelated with movements in long-maturity bond yields, even though both are endogenously determined in the same model. The disconnect arises in the estimated model because long bond yields are driven primarily by bond demand factors, while the exchange rate is driven primarily by the currency demand factor, and the two sets of factors move the exchange rate in offsetting directions so that their net effect on bond yield-exchange rate covariance is approximately zero.

Attenuation effect: The dampening of monetary policy transmission to asset prices caused by the need to compensate risk-averse arbitrageurs for the increased risk they bear when accommodating the policy-induced excess demand. In the currency market, a home short-rate cut causes the CCT’s expected return to rise (arbitrageurs must be paid more to hold foreign currency), which means the foreign currency appreciates less than UIP predicts. In the bond market, a short-rate cut causes the BCT’s expected return to rise (term premia increase), so long yields fall less than EH predicts.

Propagation effect: The international transmission of a domestic monetary policy shock to foreign asset prices through arbitrageur hedging. A home short-rate cut causes arbitrageurs to increase their foreign-currency position (CCT); this exposes them to the risk of foreign short-rate declines (which depreciate the foreign currency), and long-maturity foreign bonds hedge this risk; so arbitrageurs increase foreign bond demand, depressing foreign yields. This channel is absent from the standard model where risk premia are constant.

Log-affine equilibrium: The conjectured and verified form of the equilibrium in which the log exchange rate and log bond prices are affine (linear plus constant) functions of the five state factors (iHt, iFt, γt, βHt, βFt). This structure allows the model to be solved as a system of ordinary differential equations and scalar equations, and enables closed-form or numerically tractable characterization of risk premia, variance decompositions, and policy effects.

Bond demand factor (βjt): A stochastic variable that shifts the intercept of bond clientele demand in country j, independent of maturity τ. A positive shock to βjt increases desired bond holdings of country-j clienteles at any given price, forcing arbitrageurs to shed country-j bonds, which lowers bond yields. The factor follows a mean-reverting process and in the estimated model is found to be the primary driver of long-maturity yields in both countries.

Currency demand factor (γt): A stochastic variable that shifts the intercept of currency traders’ demand for foreign assets, independent of the exchange rate level. A positive shock to γt increases desired foreign asset holdings of currency traders, so arbitrageurs reduce their foreign-currency position, which affects their bond positions through hedging. In the estimated model, γt is the primary driver of exchange-rate movements.

Summary based on LSE Research Online accepted version (accepted manuscript). AI-assisted, human review pending.

A Theory of Supply Function Choice and Aggregate Supply

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

Research Question

Modern macroeconomic models of aggregate supply universally restrict firms to price-setting — committing to a price and supplying whatever quantity the market demands. Flynn, Nikolakoudis, and Sastry ask: what happens if instead firms choose any supply function, a mapping that describes the price charged at each quantity of production? The paper develops the first general-equilibrium, macroeconomic theory of supply function choice and characterizes its implications for the slope of aggregate supply, monetary non-neutrality, and time-varying inflation-output tradeoffs.

Methodology

The paper proceeds in two stages. In partial equilibrium, a single monopolistic firm with constant-returns-to-scale technology and constant-elasticity demand faces log-normal uncertainty about demand shifters, the aggregate price level, real marginal costs, and the stochastic discount factor. The firm chooses a non-parametric supply function — any implicit mapping f(p,q) = 0 — to maximize expected real profits. The paper shows that supply function choice is equivalent to conditioning price-quantity decisions on the realized nominal demand state z = ΨP^η. The authors prove (Theorem 1) that the optimal supply function is endogenously log-linear: log p = α₀ + α₁ log q, where the inverse supply elasticity α₁ is characterized in closed form.

In general equilibrium, the authors embed supply function choice in an otherwise standard monetary business cycle model (in the tradition of Woodford 2003a and Hellwig and Venkateswaran 2009), featuring a representative household demanding differentiated goods, a money supply following a random walk with time-varying volatility, and idiosyncratic shocks to productivity, wages, and demand. They guess and verify a log-linear equilibrium and derive a scalar fixed-point equation for the equilibrium supply elasticity (Theorem 3).

For quantification, the authors calibrate structural parameters (η = 8 from Hottman et al. 2016 scanner data; γ = 0.11 from Gagliardone et al. 2023 Belgian firm data; κ^M = 0.29 calibrated to match an average aggregate supply slope of 0.11 from Hazell et al. 2022) and estimate time-varying uncertainty via a GARCH model of quarterly US data on GDP growth, inflation, and real marginal cost growth from 1960 Q1 to 2024 Q4. Idiosyncratic demand uncertainty is set proportional to aggregate TFP uncertainty using the proportionality factor R = 6.5 from Bloom et al. (2018).

Main Findings

Optimal supply function. The optimal firm-level supply function is log-linear with inverse supply elasticity α₁ determined by the relative variances and covariances of demand, the price level, and real marginal costs. Three comparative statics drive the macroeconomic results: (1) higher idiosyncratic demand uncertainty (σ²_Ψ) flattens the supply function toward price-setting, because a fixed price insulates profit markups against demand variation; (2) higher price-level uncertainty (σ²_P) steepens the supply function toward quantity-setting, because setting a fixed quantity allows relative prices to adjust; (3) lower price elasticity of demand (less elastic demand, more market power) flattens the supply function, conditional on a sufficient condition that holds in US data whenever η > 2.5.

From micro supply to aggregate supply. With fixed log-linear supply functions, the economy has a unique log-linear equilibrium with an AD/AS representation (Theorem 2). The slope of aggregate supply ε^S_t depends on ω₁ (the transformed inverse supply elasticity), κ^M (firms’ signal precision about the money supply), γ (income effects), and η (demand elasticity). Aggregate supply is maximally elastic — money is as non-neutral as possible — if and only if firms are pure price-setters (ω₁ = 0). Aggregate supply is perfectly inelastic — money is neutral — if and only if firms are quantity-setters (ω₁ = 1/η). A lower elasticity of demand flattens aggregate supply through general equilibrium strategic complementarities, a prediction opposite to the New Keynesian model.

Equilibrium supply slope and its determinants. The equilibrium ω₁ solves a fixed-point equation (Theorem 3) in which macroeconomic uncertainty shapes firms’ optimal supply functions, which in turn shape macroeconomic dynamics. Under the special case of balanced strategic interactions (ηγ = 1), the slope of aggregate supply has a clean closed form depending only on the ratio ρ_t = σ_{ϑ,t}/σ^M_{t|s} (idiosyncratic demand uncertainty relative to posterior monetary uncertainty). Critically, the equilibrium supply slope is invariant to the overall level of uncertainty — only the composition of uncertainty matters (Proposition 3). Even vanishingly small uncertainty can generate any level of monetary non-neutrality depending on uncertainty composition.

Quantitative results — United States over time. The model’s estimated slope of aggregate supply shows sharp variation since 1960. The slope is relatively flat and stable during the 1960s, the Great Moderation (1991–2007), the Great Recession (2008–2019), and the recovery from the Great Recession. It spikes dramatically during the 1970s oil crisis and the post-Covid inflation of the 2020s. Compared to Ball and Mazumder (2011), the model qualitatively matches the steepening during 1973–1984 (+58% in the model) vs. the data’s +175%, and a subsequent flattening of −25% vs. −32% in the data during 1985–2007. Compared to Cerrato and Gitti (2022), the model accounts for approximately 4/5 of the steepening between the pre-Covid and post-Covid periods (+112% model vs. +145% data). For the Hazell et al. (2022) comparison, the model accounts for approximately 1/2 of the estimated flattening from 1978–1990 to 1991–2018.

Quantitative results — Cross-country. Using OECD annual data from 1960–2019, the model’s predicted slope of aggregate supply is not positively correlated with the average level of inflation across countries. For countries with the highest inflation rates, the model predicts a negative slope of aggregate supply, driven by very high correlation between price-level uncertainty and real marginal cost uncertainty. The model-predicted slope correlates positively with the reduced-form regression coefficient of inflation on real output growth across countries, even after instrumenting for demand. This predictive power is over and above what can be explained by the level or volatility of inflation alone.

Scope Conditions

All results are derived under log-normality of uncertainty, which ensures the log-linear structure of optimal supply functions. The quantification relies on GARCH-estimated uncertainty and treats idiosyncratic demand uncertainty as proportional to aggregate TFP uncertainty. The model abstracts from microeconomic nominal price stickiness (though the authors show in Appendix B that Calvo-style sticky prices can be incorporated). The baseline model requires the equilibrium condition on firm beliefs to be consistent (rational expectations). Multiple equilibria of the scalar fixed-point are possible in principle, bounded by at most five log-linear equilibria (Proposition 2).

In depth

Q1. What is wrong with assuming price-setting or quantity-setting as a primitive restriction on firm behavior?

A: Price-setting and quantity-setting are two isolated, generically non-optimal points in the larger space of supply functions. Corollary 2 establishes that price-setting is optimal only in the limit as idiosyncratic demand uncertainty becomes unboundedly large (σ²_Ψ → ∞), while quantity-setting is optimal only in the limit as price-level uncertainty becomes unboundedly large (σ²_P → ∞). In a macroeconomic environment where both sources of uncertainty are present in comparable magnitudes, both extreme policies perform poorly and the analyst who imposes either inadvertently restricts firms’ strategies in ways that have large macroeconomic consequences — for example, making money neutral under quantity-setting even when information frictions are present, or making the slope of aggregate supply invariant to demand elasticity under price-setting.

Q2. What is the formal equivalence between supply function choice and conditioning on realized demand?

A: The firm’s problem of choosing a supply function f(p,q) = 0 ex ante is mathematically equivalent to choosing a price-quantity plan (p(z), q(z)) indexed by the nominal demand state z = ΨP^η (Equation 4 in the paper). After the supply function is set, the firm produces where the supply function intersects the demand curve, which pins down the market-clearing outcome as a function of z. Choosing the supply function ex ante is therefore the same as choosing z-contingent prices and quantities without any parametric constraint. This links the model to rational expectations equilibrium in the spirit of Lucas (1972): firms use the demand for their product as a noisy signal to update beliefs and set their optimal price and quantity in response to realized demand conditions.

Q3. How is the optimal inverse supply elasticity α₁ derived, and what is the 2SLS interpretation?

A: Because the optimal supply function allows the firm to set a z-contingent price, the first-order condition at each realized demand state z = t equates expected marginal revenue and expected marginal cost (Equation 7). Under log-normality, this yields a log-linear relationship log p = α₀ + α₁ log q. The elasticity α₁ equals the ratio (d log p / d log z) / (d log q / d log z) = Cov[log z, log p**] / Cov[log z, log q**], where p** and q** are the full-information optimal price and quantity (Equation 9). This is formally equivalent to a 2SLS regression: the firm estimates how its optimal price should change with its optimal quantity, using the nominal demand state z as an instrument for the optimal quantity. The supply function is steep if nominal demand strongly predicts movements in the full-information optimal price (large reduced-form coefficient); it is flat if nominal demand primarily predicts movements in the full-information optimal quantity (large first-stage coefficient).

Q4. How do uncertainty and demand elasticity shape the firm’s optimal supply function in partial equilibrium?

A: Three key comparative statics apply when the supply function is upward-sloping. (1) Greater price-level uncertainty (σ²_P increases) steepens α₁ toward quantity-setting: not knowing competitors’ prices makes aggressive dynamic pricing attractive because it allows the firm’s relative price to adjust ex post. (2) Greater idiosyncratic demand uncertainty (σ²_Ψ increases) flattens α₁ toward price-setting: demand uncertainty favors a fixed price to keep the markup over real marginal costs constant, accommodating demand with quantity variation. (3) A lower price elasticity of demand (more market power, lower η) flattens α₁: more market power reduces the cost of setting the “wrong” price, reducing the benefit of dynamic pricing. Corollary 1 provides a sufficient condition — σ_{M,P} ≥ 0, 2ησ_{M,P} + σ_{M,Ψ} ≥ σ_{P,Ψ}, and α₁ ≥ 0 — under which ∂α₁/∂η > 0, implying greater market power flattens supply; the paper verifies this condition holds in US data whenever η > 2.5.

Q5. How does the model generate an aggregate supply and demand representation from supply function choices?

A: Theorem 2 establishes that, given any fixed log-linear supply functions with slope ω₁,t, there is a unique log-linear equilibrium. In this equilibrium, the price level and real output are jointly determined by an aggregate demand curve — shifting with the money supply but not productivity — and an aggregate supply curve — shifting with productivity but not the money supply. The inverse elasticity of aggregate supply is ε^S_t = γ(κ^M_t + ω₁,t(η − 1/γ)(1 − κ^M_t)) / ((1 − ω₁,t η)(1 − κ^M_t)), derived from aggregating firm-level pricing decisions. The slope depends on ω₁,t (micro supply), κ^M_t (signal precision about money), γ (income effects), and η (demand elasticity). An aggregate demand shock of ∆ log M raises the price level by ε^S_t ∆ log M / (ε^D_t + ε^S_t) and raises real output by ∆ log M / (ε^D_t + ε^S_t), where ε^D_t = γ is the inverse elasticity of aggregate demand.

Q6. What is the equilibrium fixed-point equation and why can there be multiple equilibria?

A: Theorem 3 shows that the equilibrium transformed inverse supply elasticity ω₁,t solves a quintic polynomial fixed-point equation (Equation 29) that depends on the variances of idiosyncratic demand shocks (σ²_ϑ,t), posterior uncertainty about productivity (σ^A_{t|s}), and posterior uncertainty about money (σ^M_{t|s}). Multiple equilibria can arise because of a self-reinforcing feedback: if firms set steep supply functions, prices respond more to demand, which raises price-level volatility, which in turn makes quantity-setting more attractive, further steepening supply functions. Proposition 2 establishes existence of at least one log-linear equilibrium and at most five. Idiosyncratic productivity and factor price uncertainty do not enter the fixed-point equation because the variance of real marginal costs per se does not affect optimal supply function choice — only the covariance of marginal costs with demand and the price level matters.

Q7. What determines the slope of aggregate supply in the special case of balanced strategic interactions (ηγ = 1)?

A: Under ηγ = 1 — where strategic complementarities from relative price effects exactly offset strategic substitutabilities from aggregate consumption effects — the slope of aggregate supply has the closed-form expression ε^S_t = γ(κ^M_t / (1 − κ^M_t))(1 + 1/(γ²ρ²_t κ^M_t)) where ρ_t = σ_{ϑ,t}/σ^M_{t|s} is the ratio of idiosyncratic demand uncertainty to posterior monetary uncertainty (Corollary 5). Aggregate productivity uncertainty drops out entirely because firms do not use the demand state to infer aggregate productivity when strategic interactions are balanced. As ρ_t → ∞ (idiosyncratic demand dominates), the slope converges to the price-setting value γκ^M_t/(1 − κ^M_t). As ρ_t → 0 (monetary uncertainty dominates), the slope goes to infinity, corresponding to quantity-setting and monetary neutrality.

Q8. What is the role of total uncertainty versus the composition of uncertainty?

A: Proposition 3 establishes a striking invariance result: if all standard deviations in the economy are scaled by a common factor λ > 0, the equilibrium supply elasticity and slope of aggregate supply are unchanged. The equilibrium outcomes depend only on the ratios of different sources of uncertainty, not their absolute magnitudes. This sharply distinguishes the model from menu-cost models, in which any increase in uncertainty unambiguously raises the benefit of price adjustment and steepens aggregate supply. A corollary is that idiosyncratic productivity uncertainty has no effect on the slope of aggregate supply in the supply function model, whereas it would steepen aggregate supply in Golosov-Lucas menu-cost models. Moreover, even a vanishingly small level of uncertainty can generate any level of monetary non-neutrality, because the equilibrium supply elasticity is discontinuous at zero uncertainty (ε^S_t (0) = {∞} while ε^S_t (λ) is bounded for any λ > 0).

Q9. How does market power (demand elasticity) affect the slope of aggregate supply, and why does this differ from the New Keynesian prediction?

A: In the supply function model, a lower elasticity of demand (more market power, lower η) flattens aggregate supply by reducing general-equilibrium strategic complementarities. When other firms raise their prices following a demand shock, a given firm faces higher relative demand; the strength of this effect is parameterized by η. With supply functions (ω₁,t ≠ 0), this relative demand increase generates an additional price response, so higher η steepens aggregate supply. Crucially, this effect is exactly zero if and only if firms are pure price-setters (ω₁,t = 0) — meaning the prediction that market power affects aggregate supply is absent from price-setting models. This is the opposite of the New Keynesian prediction: in Woodford (2003b) with decreasing returns to scale, a higher elasticity of demand (less market power) steepens the Phillips curve, because more elastic demand amplifies the quantity response to price changes and thereby the marginal cost response to nominal cost shocks.

Q10. How does the model rationalize the steepening of aggregate supply in the 1970s and 2020s?

A: The GARCH estimates of macroeconomic uncertainty show abrupt increases in inflation uncertainty during the 1970s oil crisis period and after the Covid-19 shock in the 2020s. In the model, a spike in aggregate price-level uncertainty (σ²_P increases) causes firms to choose steeper supply functions — closer to quantity-setting — endogenously. This steepens the aggregate supply curve so that demand shocks have larger nominal effects and smaller real effects. Quantitatively, relative to the base period, the model predicts a steepening of +58% during 1973–1984 and +112% during 2021–2023. The empirical comparisons are +175% (Ball and Mazumder 2011, 1973–1984) and +145% (Cerrato and Gitti 2022, 2021–2023). The model thus accounts for the direction and rough order of magnitude of both episodes but not their full extent. The quarterly time series of model-implied ε^S_t has a correlation of 0.93 with one-quarter-ahead inflation uncertainty and 0.62 with the quarterly level of inflation.

Q11. How does the cross-country evidence help distinguish the model from alternatives based on the level of inflation?

A: The cross-country analysis uses OECD data from 1960–2019 to construct country-level model-implied slopes of aggregate supply using the same structural parameters (η = 8, γ = 0.11, κ^M = 0.29) and country-specific GARCH uncertainty estimates from a one-lag VAR. The key finding is that the model-implied slope is not positively predicted by average inflation across countries (Panel A of Figure 5) — in fact, for the highest-inflation countries such as Chile, Israel, and Mexico, the model predicts a negative slope of aggregate supply, reflecting high correlation between price-level uncertainty and real marginal cost uncertainty. By contrast, the model-implied slope correlates positively with the reduced-form regression coefficient of inflation on real output growth (Panel B), and this positive correlation is also found using a model-derived instrument isolating exogenous monetary variation. This implies that relative uncertainties, not the mean or volatility of inflation per se, help account for cross-country heterogeneity in inflation-output tradeoffs beyond the predictions of Ball et al. (1988).

Q12. How can supply functions be integrated into larger linearized macroeconomic models?

A: Section 4.5 provides a general framework. For any model in which firms face a demand function q_it = d(p_it, z^D_it) and a value function V(p_it, q_it, z^V_it), log-linearization around a deterministic steady state yields an optimal pricing rule ˆp_it = ω₁,it ˆz^D_it (Equation 35) for some scalar ω₁,it determined by the covariance structure of the linearized model. The coefficients ω₁,it enter the standard representation of aggregate dynamics (McKay and Wolf 2023) through the ideal price index ˆP_t = ∫₀¹ ˆp_it di. The additional “rational expectations” restriction is that ω₁,it must be consistent with the equilibrium law of motion for prices. The paper argues that supply functions can thereby be embedded in the broad class of linearized DSGE models used for quantitative work, including models with decreasing returns, monopsony, endogenous markups, sticky prices, investment, and quality choice.

Q13. What are the implications of supply function choice for monetary policy discretion?

A: The model implies a thorny tradeoff for monetary policymakers. If a central bank wishes to maintain discretion — the ability to surprise private agents — this increases firms’ uncertainty about the money supply (higher σ²_M). Under balanced strategic interactions (ηγ = 1), greater posterior monetary uncertainty (σ^M_{t|s}) lowers the ratio ρ_t = σ_{ϑ,t}/σ^M_{t|s}, which flattens the aggregate supply curve (reduces ε^S_t) and thereby increases the real effect of monetary surprises. However, this also endogenously induces firms to set steeper supply functions — closer to quantity-setting — so that the aggregate supply curve steepens in response to the greater price-level uncertainty generated by such an environment. The paper therefore concludes that maintaining monetary policy discretion may be, at least partially, self-defeating.

Inverse supply elasticity (α₁): The percentage by which a firm increases its price in response to a one percent increase in production, characterizing the slope of the firm’s optimal supply function. It is endogenously log-linear and determined by the ratio of covariances relating the nominal demand state to the firm’s optimal price vs. optimal quantity under full information — formally equivalent to a 2SLS coefficient using nominal demand as an instrument.

Supply function: A mapping f(p, q) = 0 describing the locus of prices and quantities a firm commits to, as an implicit function over price-quantity pairs. Unlike price-setting (f depends only on p) or quantity-setting (f depends only on q), the general supply function allows prices to vary with realized demand, nesting both polar cases as limits of extreme uncertainty.

Nominal demand state (z): The composite variable z = ΨP^η that indexes the demand curve. Firms observing their own output market clearing can use z as a noisy signal for inference about the aggregate price level, real marginal costs, and monetary conditions. The supply function is formally equivalent to conditioning price-quantity choices on z.

Slope of aggregate supply (ε^S): The inverse elasticity of the aggregate supply curve in the AD/AS representation, measuring the relative within-period response of the price level versus real output to an aggregate demand shock. It depends on the slope of firm-level supply functions (ω₁) interacted with the information precision about the money supply (κ^M) and income effects (γ).

Transformed inverse supply elasticity (ω₁): The reparameterization ω₁ = α₁/(1 + ηα₁), where α₁ is the firm-level inverse supply elasticity and η is the price elasticity of demand. ω₁ = 0 corresponds to price-setting; ω₁ = 1/η corresponds to quantity-setting. The equilibrium value of ω₁ solves a fixed-point equation that maps macroeconomic uncertainty back into firms’ optimal supply function choices.

Balanced strategic interactions (ηγ = 1): A parametric special case in which strategic complementarities from aggregate demand externalities (parameterized by η) exactly offset strategic substitutabilities from wage pressure (parameterized by 1/γ). Under this condition, the slope of aggregate supply has a closed-form solution that depends only on the relative uncertainty about idiosyncratic demand vs. the money supply.

Relative uncertainty sufficient statistic (ρ_t): The ratio σ_{ϑ,t} / σ^M_{t|s}, measuring firms’ uncertainty about idiosyncratic demand shocks relative to posterior uncertainty about the money supply. Under balanced strategic interactions (ηγ = 1), ρ_t is the single sufficient statistic determining the equilibrium slope of aggregate supply. As ρ_t → ∞ (idiosyncratic demand uncertainty dominates), firms converge to price-setting and aggregate supply flattens; as ρ_t → 0 (monetary uncertainty dominates), firms converge to quantity-setting and aggregate supply becomes vertical.

Invariance to total uncertainty: A key property of the model: the equilibrium slope of aggregate supply is invariant to the overall scale of uncertainty (Proposition 3). Only the composition of uncertainty across idiosyncratic vs. aggregate sources and demand vs. productivity shocks matters. This distinguishes the model from menu-cost models, in which any increase in uncertainty raises the benefit of price flexibility and steepens aggregate supply regardless of uncertainty composition.

A Welfare Analysis of Policies Impacting Climate Change

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

This paper extends and applies the marginal value of public funds (MVPF) framework to evaluate the welfare consequences of 96 climate-related tax and spending policies in the United States. The MVPF is a benefit-cost ratio in which the numerator captures all benefits to individuals (measured by their willingness to pay) and the denominator captures net government costs; policies with higher MVPFs are better spending policies, while those with lower MVPFs are more efficient revenue-raising instruments.

The sample covers policies rigorously evaluated using quasi-experimental or experimental methods drawn from 18 major economics journals between January 1999 and December 2023. Policies fall into three primary categories: subsidies (wind production tax credits, residential solar, electric vehicles, hybrid vehicles, vehicle buybacks, appliance rebates, and weatherization), nudges and marketing, and revenue raisers (gasoline taxes, other fuel taxes, cap-and-trade). A selected set of international aid policies is also analyzed. The analysis applies a harmonized method for translating behavioral changes into emissions changes — using the EPA’s AVERT model for electricity-sector emissions — and a consistent set of externality valuations, including an EPA 2023 social cost of carbon (SCC) of $193 per ton of CO2 in 2020 (rising over time), with robustness checks at $76, $337, and $1,367.

The primary methodological contribution is a new sufficient statistics approach to quantifying learning-by-doing (LBD) externalities. When marginal cost of production is an isoelastic function of cumulative production and demand is an isoelastic function of price, the time path of production satisfies a second-order ordinary differential equation whose solution yields society’s willingness to pay for LBD spillovers. LBD generates two types of externalities: a price externality (lower future consumer prices) and an environmental externality (increased future take-up of clean goods). The approach requires four inputs: price elasticity of demand, elasticity of marginal cost with respect to cumulative production, cumulative production at the time of the subsidy, and product cost at the time of the subsidy.

The three main empirical findings are as follows. First, subsidies for production that directly displaces dirty electricity generation have the highest MVPFs. Wind production tax credits have an MVPF of 3.85 without LBD, rising to 5.87 with LBD. Residential solar subsidies have an MVPF of 1.45 without LBD, rising to 3.86 with LBD. EV subsidies have an MVPF of approximately 1.4 with LBD and approximately 1 without it. Consumer subsidies for appliances, weatherization, vehicle retirement, and hybrid vehicles have MVPFs around 1. Second, conservation nudges targeting electricity consumption can deliver MVPFs exceeding 5 in regions with relatively dirty electric grids, but fall below 1 in cleaner-grid regions such as California and the Northeast — and their effectiveness is expected to decline as grids decarbonize. Third, fuel taxes (gasoline, diesel, jet fuel) and cap-and-trade permit reductions are efficient revenue raisers, with nearly all having MVPFs below 1 and most below 0.7, reflecting the Pigouvian logic that current tax rates fall below the associated environmental externalities. Cap-and-trade permit reductions can produce MVPFs below zero, meaning revenue is raised while providing net positive welfare to individuals.

The paper also constructs three cost-per-ton metrics — resource cost per ton, government cost per ton, and social cost per ton — and shows they can yield substantively different and sometimes opposite rankings relative to each other and to the MVPF. For example, EV subsidies carry a government cost per ton of $1,356 (among the highest in the sample) yet an MVPF above most consumer subsidies, because that metric omits non-CO2 benefits including LBD effects. The scope of the analysis is US historical policy, with the MVPF comparison most informative when social welfare weights across beneficiary groups are treated as roughly equal.

Q: What is the MVPF framework and how does it differ from cost-per-ton analysis? A: The MVPF equals benefits to individuals (sum of willingness to pay) divided by net cost to the government. It is designed for a decision-maker maximizing social welfare subject to a budget constraint, whereas cost-per-ton metrics serve a decision-maker minimizing cost subject to a fixed CO2 reduction target. A higher MVPF means more welfare gain per dollar spent; a lower MVPF means less welfare cost per dollar of revenue raised.

Q: What are the three cost-per-ton definitions the paper distinguishes, and why do they differ? A: Resource cost per ton measures the economic resources consumed per ton of CO2 abated, independent of subsidy incidence; government cost per ton measures net government outlays per ton, omitting all non-CO2 benefits; social cost per ton subtracts non-CO2 benefits from government costs. For appliance rebates, these three values are -$2, $474, and an intermediate figure — a range that reflects whether inframarginal transfers and non-CO2 co-benefits are counted.

Q: What is the new methodological contribution regarding learning by doing? A: The paper derives a sufficient statistics result showing that when marginal production cost is an isoelastic function of cumulative production and demand is isoelastic in price, the time path of production follows a second-order ordinary differential equation. Solving this equation yields society’s willingness to pay for LBD spillovers from four observable parameters: demand price elasticity, the LBD elasticity of marginal cost with respect to cumulative production, cumulative production at the subsidy date, and unit cost at that date. This allows LBD benefits to be incorporated into both MVPF and cost-per-ton calculations without requiring a fully calibrated dynamic model.

Q: What LBD elasticities does the paper use, and where do they come from? A: Drawing on Way et al. (2022), a 1% increase in cumulative solar production is associated with a 0.319% price reduction; for wind the elasticity is 0.194%, and for EV batteries it is 0.421%. These are treated as the isoelastic parameter in the sufficient statistics formula.

Q: How does LBD affect the MVPF estimates for wind, solar, and EVs specifically? A: For wind production tax credits, the MVPF rises from 3.85 to 5.87 when LBD is included. For residential solar, it rises from 1.45 to 3.86. For EV subsidies, the MVPF rises from approximately 1 to approximately 1.4. Without LBD, EV subsidies are in line with other consumer subsidies; LBD is the primary reason EVs outperform that group.

Q: What is the baseline social cost of carbon used, and how sensitive are results to alternative values? A: The baseline SCC is $193 per ton of CO2 in 2020, following EPA 2023 guidance at a 2% discount rate. Robustness checks use $76, $337, and $1,367. Higher SCC values raise the MVPF of all subsidies in the sample, but the relative ordering — with wind PTCs above all other consumer subsidies — remains consistent across the full range.

Q: How are EV subsidies evaluated, and what accounts for their MVPF exceeding other consumer subsidies? A: The analysis uses the California EFMP program studied by Muehlegger and Rapson (2022), which finds a price elasticity of demand of -2.1 and 85% pass-through to consumers (15% captured by dealers). A $1 subsidy generates $0.85 in consumer WTP, $0.15 in dealer WTP, $0.17 in CO2 co-benefits, $0.05 in local pollution and accident co-benefits, offset by $0.10 in damages from increased electricity generation. Most benefits are non-environmental (inframarginal transfers and LBD effects on future vehicle prices), which is why the government cost per ton of $1,356 appears high while the MVPF is approximately 1.4.

Q: What drives the high MVPFs for nudges in dirty-grid regions, and what is the implication for the future? A: Conservation nudges in dirty-grid areas have high MVPFs (exceeding 5) because each kilowatt-hour of reduced consumption displaces generation from high-emission sources, amplifying the environmental benefit per dollar of program cost. In cleaner-grid regions like California and the Northeast, the same nudge displaces lower-emission generation, pushing the MVPF below 1. As grids decarbonize nationwide, the paper notes that nudge MVPFs will decline over time.

Q: How do cap-and-trade permit reductions compare to fuel taxes as revenue-raising instruments? A: Nearly all fuel taxes (gasoline, diesel, jet fuel) have MVPFs below 1, with most below 0.7, meaning they impose a welfare cost of only $0.70 per dollar of revenue raised. Cap-and-trade permit reductions can have MVPFs below zero, meaning they can raise revenue while simultaneously providing net positive welfare gains to individuals because environmental benefits from reduced emissions outweigh the permit costs borne by emitters.

Q: What do the international subsidy findings suggest, and what are their limitations? A: Subsidies for efficient charcoal cookstoves in Kenya (Berkouwer and Dean 2022) generate US-specific gains from CO2 reductions that are 37 times the net cost of the subsidy; including global benefits raises the MVPF to 323. However, the paper flags substantial uncertainty: estimated policy impacts vary widely within similar international categories, and the US-specific MVPF is highly sensitive to assumptions about the incidence of the social cost of carbon on US residents and US government tax revenue.

Q: Why does the social cost per ton metric give opposite rankings within wind, solar, and EVs relative to the MVPF? A: EVs have a social cost per ton of -$415 versus -$32 for wind PTCs, making EVs appear superior on that metric — the reverse of the MVPF ordering. The paper explains that when SCPT values are negative (policies that abate CO2 while also yielding positive non-CO2 net benefits), the metric loses its Lagrange multiplier interpretation: increased non-CO2 benefits make SCPT more negative while increased abatement makes it less negative, preventing meaningful cross-policy comparisons.

Q: What is the overall policy ranking implied by the MVPF analysis? A: From highest to lowest MVPF: international clean energy subsidies > wind production tax credits > residential solar subsidies > energy conservation nudges (dirty grids) > EV subsidies > consumer appliance and weatherization subsidies > hybrid vehicle subsidies > vehicle buyback rebates > energy conservation nudges (clean grids) > revenue raisers (gas taxes, fuel taxes, cap-and-trade). The paper notes that shifting $1 of government revenue from gas taxes (MVPF ~0.67) to wind PTCs (MVPF ~5.87) generates $5.20 in net welfare benefits to individuals, assuming equal social welfare weights across groups.

Marginal Value of Public Funds (MVPF): A benefit-cost ratio equal to the sum of individuals’ willingness to pay for a policy divided by its net cost to the government. Policies with higher MVPFs deliver greater welfare gains per dollar spent; those with lower MVPFs impose lower welfare costs per dollar of revenue raised. Used to compare spending and revenue-raising policies on a common welfare-maximizing basis.

Learning-by-Doing (LBD) Externality: The spillover by which current production of a technology lowers its future marginal cost, generating future consumer surplus (price externality) and additional future uptake with associated environmental benefits (environmental externality). Treated in this paper as an uninternalized external benefit of subsidizing current production.

Sufficient Statistics Approach to LBD: The paper’s methodological contribution — showing that when marginal cost is an isoelastic function of cumulative production and demand is isoelastic in price, the LBD welfare benefit can be computed from four observables: the demand price elasticity, the LBD cost elasticity, cumulative production at subsidy date, and unit cost at subsidy date, without requiring a fully specified dynamic model.

Resource Cost per Ton (RCPT): Economic resources consumed to produce and use a product, divided by tons of CO2 abated. Appropriate for private firms minimizing abatement cost; independent of subsidy take-up rates and inframarginal transfers.

Government Cost per Ton (GCPT): Net government outlay per ton of CO2 abated. The correct metric for a government focused exclusively on CO2 reduction at minimum fiscal cost; omits all non-CO2 welfare impacts, including co-benefits and LBD effects.

Social Cost per Ton (SCPT): Government cost net of all non-CO2 benefits, per ton of CO2 abated. Intended to capture the social cost of abatement, but loses its Lagrange multiplier interpretation when values are negative, preventing valid cross-policy comparisons in that region.

Social Cost of Carbon (SCC): The monetized damage from one additional ton of CO2 emissions. Baseline value of $193 per ton in 2020 from EPA 2023 at a 2% discount rate, rising over time. A key parameter driving MVPF levels across all policy categories; robustness checked at $76, $337, and $1,367.

Pigouvian Efficiency of Environmental Taxes: The paper quantifies that fuel taxes have MVPFs below 0.7 because current tax rates fall below the associated Pigouvian optimum — i.e., taxing polluting goods raises revenue while reducing a pre-existing negative externality, so the welfare cost of the revenue is less than one dollar per dollar raised.

Abundance from Abroad: Migrant Income and Long-Run Economic Development

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

Layer 1 — Overview

Research Question

This paper asks how persistent increases in international migrant income prospects affect long-run economic development in migrant-origin areas. The central question is whether Philippine provinces with persistent access to higher-income migration opportunities develop faster than provinces with less attractive migration opportunities, and through which channels.

Natural Experiment and Identification Strategy

The authors exploit the 1997 Asian Financial Crisis as a large-scale natural experiment. The crisis triggered sharp, heterogeneous, and persistent exchange rate changes across Philippine migrants’ destination countries — ranging from a 4% depreciation against the Philippine peso (Korea) to a 57% appreciation (Libya), with Japan and Saudi Arabia in between (appreciations of 32% and 52%, respectively). Because Philippine provinces differed in the pre-crisis distribution of migrant income across destinations (measured using unusual POEA/OWWA administrative contract data covering all overseas worker contracts, including migrant incomes, origins, and destinations), these exchange rate shocks generated exogenous, province-level variation in a shift-share instrument: the predicted change in province migrant income per capita due to the 1997 shocks. Identification follows the “exogenous shares” framework of Goldsmith-Pinkham et al. (2020). Pre-trend tests across up to 12 years of pre-shock panel data find no evidence of differential trends across provinces. The five destinations with the highest Rotemberg weights — Saudi Arabia, Japan, United States, Taiwan, and Hong Kong — collectively account for 75% of the identifying variation. The exchange rate shocks and the exposure weights both exhibit strong persistence over two decades post-1997.

Data

Philippine government administrative data (POEA/OWWA) on all overseas worker contracts, 1992–2015, matched at 95% rate, providing province-of-origin and destination-specific migrant income.
Philippine Family Income and Expenditure Survey (FIES), up to twelve triennial rounds from 1985–2018 (74 provinces, ~40,000 households per round), for domestic income and expenditure.
Six rounds of the Philippine Census of Population (1990–2015) for education, migration rates, and sectoral employment shares.
Province-level consumer price index data (1994–2017) and firm-level export survey data for robustness checks.
Unit of analysis: 74 Philippine provinces (consistent 1990 borders).

Main Findings with Quantitative Magnitudes

Six-fold magnification of migrant income: Each unit of initial short-run shock (1997–1998) to migrant income per capita is magnified more than six-fold by 2009–2015. A one-standard-deviation shock (0.093) raises long-run migrant income per capita by 14.7% of the baseline mean (PhP 601 per capita, 0.2 standard deviations).
Domestic income gains predominate: A one-standard-deviation shock raises domestic income per capita (excluding migrant income and remittances) by 6.4% of the baseline mean (PhP 1,676, 0.18 standard deviations). Remarkably, 73.6% of the long-run global income increase comes from domestic income and only 26.4% from migrant income.
Global income and expenditure: A one-standard-deviation shock raises global income per capita by PhP 2,277 (0.2 standard deviations, or 7.5% of the baseline mean) in 2009–2015. Expenditure per capita rises by PhP 1,159 (0.13 standard deviations). Effects emerge gradually over two decades.
Education: A one-standard-deviation shock increases the college-educated share of the population by 0.46–0.51 percentage points (0.11–0.12 standard deviations) and secondary completion by 0.63 percentage points. There is no significant effect on primary completion.
Migration rates and skill composition: A one-standard-deviation shock increases the migration rate by 0.19 percentage points (0.22 standard deviations), raises the share of skilled migrants by 1.84 percentage points (0.19 standard deviations), and increases average migrant annual salary by PhP 23,703 (0.16 standard deviations). New migration concentrates in higher-education-quartile occupations.
Structural change: The shock reduces primary sector employment shares by 1.2 percentage points per standard deviation (0.06 standard deviations), with over 70% of that shift absorbed by non-tradable goods and services sectors. Domestic income gains are driven almost entirely by non-agricultural income, and roughly 55% of the increase in entrepreneurial income is from service sectors.
Education’s contribution to income: Model-based calculations assign 19.6% of the global income gain, 17.8% of the migrant income gain, and 20.2% of the domestic income gain to educational investments. Exchange rate persistence plus altered migration flows explain an additional 64.6% of the migrant income increase, so together these mechanisms account for 82.3% of the six-fold magnification. A demand multiplier (assuming 64% of migrant income returns to origin economies and a multiplier of 2.9, consistent with estimates from the literature) accounts for approximately 83.3% of the non-education-related portion of the domestic income increase.

Threats to Identification Ruled Out

Import and export shift-share controls (constructed analogously using bilateral trade data and province-level industry employment shares) are uncorrelated with the migrant income shock and leave coefficient estimates unchanged. Province-level manufactured exports, agricultural income, the CPI, and national-level FDI inflows show no statistically significant response to the shock. Internal migration rates are unaffected. Geographic spillover controls and tourism controls do not alter results. Placebo regressions in the pre-period yield small, statistically insignificant coefficients.

Scope Conditions

The paper studies formal, government-regulated temporary labor migration from the Philippines, where migrants sign contracts through POEA-licensed agencies and typically expect to return after one or more contracts. The findings apply specifically to settings where persistent (not transitory) migrant income shocks occur. Approximately 60% of contract migrants are female. The study period spans 1985–2018, with main long-run outcome analyses comparing 1994 (pre-shock) with 2009–2015 (post-shock).

In depth

Q1. What makes the 1997 Asian Financial Crisis useful as a natural experiment for this paper’s purposes?

A1: The crisis was largely unanticipated by policymakers, international organizations, and financial markets, making it implausible that pre-1997 migration destination choices reflected anticipation of the shocks. Exchange rate changes were heterogeneous across destinations (ranging from a 4% depreciation to a 57% appreciation), and crucially, these changes proved highly persistent over two decades — regression coefficients of long-run exchange rate changes on the initial 1997–1998 shock are close to and statistically indistinguishable from 1 in nearly all post-shock periods. Combined with the province-specific variation in migrant destination exposure, this generates persistent, exogenous, and heterogeneous shocks to migrant income prospects across provinces.

A2: The shift-share variable Shiftshareo equals the sum over destinations d of (ωdo0 × ΔRd), where ωdo0 is province o’s pre-shock migrant income per capita from destination d (the “exposure weight” or “share”), and ΔRd is the fractional change in destination d’s exchange rate from before to after the crisis (the “shift”). It captures the predicted change in province-level migrant income per capita due to the 1997 exchange rate shocks, and is derived directly from a theoretical model of migration. Identification relies on the “exogenous shares” approach of Goldsmith-Pinkham et al. (2020): the pre-1997 exposure weights are treated as as-good-as-randomly assigned conditional on controls, because they reflect historical migration networks formed well before the crisis.

Q3. Why is the six-fold magnification of the initial migrant income shock so striking, and what does the structural model say about its sources?

A3: The coefficient on migrant income per capita (6.463 in Panel D of Table 1) implies that for each unit of initial short-run migrant income shock, migrant income per capita is more than six units higher in 2009–2015 — a far larger response than a one-for-one pass-through would predict. The structural model, which augments a Fréchet-based gravity model of migration with endogenous education investments, accounts for 82.3% of this magnification. Education investments explain 17.8% of the migrant income increase; persistent favorable exchange rates and resulting shifts in migration flows across destinations explain an additional 64.6%. The Fréchet elasticity of migration flows with respect to destination wages is estimated at θ = 3.42 via PPML, implying that even partial reorientation of migrants toward now-higher-wage destinations substantially raises aggregate migrant income.

Q4. What evidence supports the parallel trends assumption in the pre-shock period?

A4: The authors present event study diagrams (Figure 2) showing no differential positive pre-trends in either expenditure per capita or domestic income per capita prior to 1997 — for domestic income, there is a statistically insignificant negative trend from 1985–1991 and no trend in 1991–1994. Placebo regressions estimated on the pre-period only (1985, 1988, 1991 as “pre,” 1994 and 1997 as “post”) yield small, statistically insignificant coefficients on both domestic income and expenditure. Balance tests focusing on the five high-Rotemberg-weight destination shares (Saudi Arabia, Japan, US, Taiwan, Hong Kong) — which collectively account for 75% of the identifying variation — also show no significant pre-trends in key outcomes across provinces with varying levels of exposure.

Q5. How do the authors rule out trade flows as an alternative mechanism for the estimated income effects?

A5: They construct separate import and export shift-share variables, analogous to the “China shock” of Autor et al. (2013), using baseline bilateral trade values (from COMTRADE, disaggregated to 36 ISIC industries), province-level employment shares in import and export industries (from the 1990 Census), and the same destination exchange rate shocks. These trade shift-share variables are uncorrelated with the migrant income shock after conditioning on baseline controls (Appendix Table A5). Including them as additional controls in Panel D of all main regression tables leaves the migrant income coefficient stable. Further, province-level manufactured exports per capita show no large or statistically significant response to the migrant income shock, agricultural income similarly shows no significant response, and consumer price indices are unresponsive — ruling out import price changes as a confound. FDI inflows at the national level also show no significant relationship with destination-country exchange rate shocks.

Q6. What is the composition of the domestic income gains — where do they come from?

A6: Both wage income and entrepreneurial/rental income rise significantly and in similar magnitude, while “other income” (pensions, interest, dividends) shows no robust increase (Table 4). Non-agricultural income drives virtually the entire domestic income gain; agricultural income per capita is statistically insignificant (Table 5, columns 1–2). Within entrepreneurial income, approximately 55% of the increase is from service sectors, with manufacturing and primary sector entrepreneurial income showing insignificant effects at the 10% level (Table 5, columns 3–5). These patterns are consistent with the structural change finding: the shock shifts labor from primary sectors toward non-tradable goods and services rather than toward tradable manufacturing.

A7: Global income per capita is defined as the sum of domestic income per capita (earned within the Philippine economy, excluding all international transfers) and migrant income per capita (the full income earned abroad by a province’s international migrants, calculated from contract data). Of the long-run global income increase, 73.6% comes from domestic income and 26.4% from migrant income. A one-standard-deviation shock raises global income by PhP 2,277 per capita in 2009–2015 (0.2 standard deviations, or 7.5% of the baseline mean).

Q8. How do education effects translate into more and higher-skilled migration?

A8: A one-standard-deviation migrant income shock increases college completion by 0.46 percentage points and secondary completion by 0.63 percentage points (with no significant effect on primary completion), consistent with the shock raising the return to higher education in the broader population. These better-educated workers then migrate at higher rates: the share of migrants who are skilled (college-educated) rises by 1.84 percentage points per standard deviation. Migration increases are concentrated in the two highest-education quartiles of occupations (engineers, medical professionals, teachers in the 4th quartile; caregivers, restaurant workers, performing artists in the 3rd quartile), with no significant effect in the two lowest quartiles. Average annual migrant salary rises by PhP 23,703 per standard deviation (0.16 standard deviations).

Q9. What mechanisms does the structural model invoke to explain the domestic income gains?

A9: The model treats domestic income changes as arising through at least two channels: (1) the education channel, which the model assigns 20.2% of the domestic income increase (using the estimated college completion response of 0.046 per unit shock, baseline skill-migration probabilities, and baseline skill premia for domestic income); and (2) a demand multiplier operating on the portion of migrant income remitted to origin provinces, combined with capital accumulation from sustained migrant income flows. Assuming 64% of migrant income returns to origin economies (estimated indirectly from KNOMAD/ILO and Survey on Overseas Filipinos data) and a multiplier of 2.9 (consistent with estimates from Kenya and India), this demand-plus-investment channel can explain approximately 83.3% of the remaining (non-education-related) domestic income increase of PhP 14.4 per unit shock. Under baseline assumptions (α = 0.64), the stylized dynamic model generates PhP 18.88 of domestic income by 2015 from a PhP 1 initial shock — close to the empirical estimate of PhP 18.02.

Q10. How do the authors assess SUTVA and internal migration?

A10: They test whether the migrant income shock affects net internal migration rates at the provincial level (Appendix Table A6) and find no large or statistically significant impact. There is a small negative effect on outmigration of young adults (aged 16–24) that the authors judge cannot account for the documented income impacts. The Philippines’ archipelago geography (over 7,000 islands) is noted as likely limiting inter-provincial economic spillovers; to the extent spillovers occur, they would be positive (demand spillovers from provinces experiencing income gains to neighboring provinces), making estimates conservative lower bounds. Direct tests controlling for the inverse-distance-weighted migrant income shock in neighboring provinces leave main estimates unchanged.

Q11. Are the exposure weights (migration shares) persistent, and does this support interpreting the shock as persistent?

A11: Yes. Regressions of dyadic migrant income per capita in post-shock years (2009, 2012, 2015) on dyadic migrant income per capita in 1995 yield coefficients ranging from 0.4 to 0.6, each statistically significantly different from zero (and from 1, indicating partial but substantial persistence). The exchange rate shocks ΔRd are even more persistent: regression coefficients on the initial 1997–1998 shock are close to 1 and statistically indistinguishable from 1 in nearly all post-shock periods (with the only exceptions in 2009–2012 during the Great Recession). Both components of the shift-share variable thus show persistence over two decades, supporting interpretation of the long-run effects as responses to a persistent (not transitory) income shock.

Q12. What are the policy implications and how do the authors connect findings to migration policy?

A12: The findings suggest migration policy should be an important part of the development policy toolkit. The results are directly relevant to origin-country policies facilitating formal, contract-based labor migration (e.g., regulation of recruitment agencies, educational investments to raise worker skills and competitiveness for overseas employment) and destination-country policies governing legal immigration opportunities. The authors also note implications for overseas development assistance: development agencies could consider supplementing traditional foreign aid with programs that facilitate international labor migration. The paper’s context — formal, government-regulated migration through POEA and OWWA — is described as highly policy-relevant, with 94% of developing countries with populations exceeding 1 million having a dedicated government migration agency and 78% having policies promoting migrant remittances.

Key Concepts

Shift-share variable (Shiftshareo): The paper’s primary independent variable, equal to the sum over all overseas destinations d of (ωdo0 × ΔRd) — the province’s pre-shock migrant income per capita from each destination (the exposure weight or “share”) multiplied by that destination’s exchange rate shock (the “shift”). It is the predicted change in province migrant income per capita due to the 1997 Asian Financial Crisis exchange rate shocks, and is derived directly from the theoretical model of migration (Equation A9). Identification treats the exposure weights as exogenous following the “exogenous shares” approach of Goldsmith-Pinkham et al. (2020).

Exposure weights (ωdo0): Province o’s pre-shock aggregate migrant income per capita earned in destination d, calculated from administrative POEA/OWWA contract data for 1995. These serve as the “shares” in the shift-share and capture the extent to which a province’s residents are exposed to a given destination’s exchange rate shock. They reflect historically-formed migration networks rather than anticipation of future shocks.

Global income per capita: The sum of domestic income per capita and migrant income per capita. Domestic income is household income earned within the Philippine economy (wages, entrepreneurial, and other sources), explicitly excluding all income from international sources including remittances. Migrant income is the full income earned abroad by all international migrants from the province, calculated from contract data (not remittances sent home). Global income thus captures the full resource gain available to a province from the combination of domestic production and international migration.

Magnification (of migrant income shock): The empirical finding that the long-run coefficient on migrant income per capita (6.463 in Panel D, Table 1) far exceeds 1 — meaning each unit of initial short-run shock becomes more than six units of migrant income per capita in 2009–2015. The paper decomposes this magnification into contributions from persistent exchange rates, educational investments raising skill levels and migration, and shifts in migration flows toward now-higher-wage destinations.

Brain gain: The paper’s term for the process by which improved migrant income prospects raise educational investments among the broader population (not just among migrants), leading to higher skill levels among non-migrants as well. The paper distinguishes this from “brain drain” (where migration of skilled workers reduces origin-area human capital) and provides evidence of a “virtuous cycle”: education raises migration rates and migrant skill levels, which in turn raises migrant and domestic incomes, potentially funding further education.

Rotemberg weights: Province-destination-level weights (following Goldsmith-Pinkham et al. 2020) characterizing which destination-specific exchange rate shocks drive the estimates most. Saudi Arabia (0.20), Japan (0.19), United States (0.18), Taiwan (0.10), and Hong Kong (0.08) together account for 75% of the total Rotemberg weight. These weights guide which destination-specific exposure shares receive the most scrutiny in pre-trend and balance tests.

Fréchet elasticity (θ): The elasticity of migration flows from an origin province to a destination with respect to destination wages (in Philippine pesos), estimated at 3.42 via PPML using the exchange rate shocks. This parameter governs how much migration flows — and thereby migrant income — respond to the persistent exchange rate changes, and is central to the model’s decomposition of the six-fold magnification of migrant income effects.

Domestic income multiplier: The ratio of long-run domestic income increase to the portion of the migrant income shock that returns to origin provinces. Assuming 64% of migrant income returns to origin economies (estimated from multiple administrative data sources), the implicit demand multiplier in the paper’s context ranges from about 2.9 to 3.4, consistent with multipliers found in related literature on cash transfers and credit supply shocks in low-income settings.

Across-Country Wage Compression in Multinationals

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

Layer 1 — Summary

Many multinationals do not fully adjust wages to the local context of their foreign establishments; instead, they partially link the wages of foreign workers in a given position to the wages paid in the same position at headquarters — a practice the authors call “wage anchoring.” Using yearly establishment-level compensation data on roughly 1,200 multinationals operating across 174 cities worldwide (2000–2015) and matched employer-employee administrative data (RAIS) from Brazil, Hjort, Li, and Sarsons document that a 10 percent higher headquarters wage is associated with 1.63–2.8 percent higher wages for workers in the same occupation at foreign establishments, with the within-firm across-country correlation substantially exceeding the correlation between a given establishment’s wages and the local average paid by other multinationals for the same position. To establish a causal link between externally imposed headquarters wage changes and subsequent foreign establishment wage responses, the paper exploits two identification strategies: minimum wage shocks in the headquarters country or U.S. state and exchange rate fluctuations, both of which generate plausibly exogenous variation in headquarters wages that is then partially transmitted to foreign workers in the same position. Wage change transmission appears to be direct and to operate through firm-wide wage-setting procedures rather than through associated changes in technology or employment at foreign establishments, a conclusion the Brazil RAIS data support because total employment at multinationals’ Brazilian establishments shows little change following positive external shocks to headquarters wages. Wage anchoring is strongest for low-skill occupations (cleaners, drivers, security guards), where a 10 percent higher headquarters wage is associated with a 2.8 percent higher foreign establishment wage, versus roughly 1.2 percent for middle- and high-skill occupations; the resulting spatial compression of wages is in line with how many multinationals themselves report setting pay across locations.

In depth

Q1. What is the central phenomenon documented in this paper, and what are the two broad empirical components of the analysis?

The central phenomenon is “wage anchoring”: multinationals link wages at their foreign establishments to the wage level at headquarters for the same narrowly-defined occupation, so that the within-firm across-country wage distribution is more compressed than what local labor-market conditions alone would imply. The first empirical component is descriptive — documenting the high cross-sectional correlation between headquarters and foreign establishment wages within a firm×occupation cell, controlling for city×year effects and local wage benchmarks. The second component is causal — using minimum wage shocks in the headquarters country or U.S. state and exchange rate shocks to generate externally imposed changes in headquarters wages, and tracing whether and how quickly those changes are partially transmitted to foreign establishments.

Q2. What is the primary dataset, what does it cover, and what are its key limitations?

The primary dataset was compiled by an unidentified consulting company that gathers compensation information from client employers and harmonizes positions globally into 309 occupations across 16 skill levels and 26 occupational categories. It covers roughly 1,200 multinationals (private-sector firms and multinational public-sector employers such as NGOs and multilateral organizations), operating in more than 170 cities, with yearly observations spanning 2000–2015. The data report average nominal gross total monthly wages for domestic (non-expat) workers in each establishment-occupation-year cell. Key limitations: the panel is unbalanced because multinationals choose which establishments report each year and often rotate establishments in and out; matching between the headquarters and any given foreign establishment requires observing the same occupation in the same year at both, which reduces the headquarters-matched sample to 80 employers and 611 foreign establishments (Sample 3, the most comparable subsample). The publicly listed U.S. firms in the data account for about one-third of total revenue of all publicly listed U.S. firms, so the sample is skewed toward unusually large employers.

Q3. How do the authors define and measure “wage anchoring” in the descriptive section?

The authors regress log average wages of workers in occupation j at a firm f’s foreign establishment in city c in year t (wjfct) on log average wages for the same occupation at the firm’s headquarters (HQwjft), controlling for firm×occupation fixed effects, city×year fixed effects, and a local market wage benchmark measured either as the average paid by other multinationals in the same city-occupation-year cell or as a city×occupation×year fixed effect. The estimated coefficient on the headquarters wage — around 0.163 using the benchmark-wage control and about 0.09 using the more restrictive city×occupation×year fixed effect — measures how much of a headquarters wage difference is “passed through” to foreign establishment wages within the same firm and occupation. They further document that the within-firm wage slope (the difference between wages in consecutive skill levels within an occupational category) at foreign establishments is similarly anchored to the corresponding slope at headquarters, with a 10 percent greater consecutive-skill wage gap at headquarters associated with about a 1.4 percent greater gap at the foreign establishment.

Q4. What exactly do the minimum wage and exchange rate identification strategies exploit, and what do they identify?

The minimum wage strategy compares multinationals whose headquarters are located in a country or U.S. state that experiences a minimum wage increase (“treated”) against multinationals whose headquarters are not exposed (“control”), conditioning on establishments being in the same foreign city. Within the treated group, it also exploits cross-occupation variation: within a given foreign establishment, workers in positions whose headquarters counterparts are more exposed to the minimum wage increase (because their wages are closer to the new minimum) experience larger foreign wage gains. The exchange rate strategy exploits appreciation of a non-U.S. headquarter country’s currency against the dollar: when the USD-measured headquarters wage of such a multinational increases following an appreciation, this tests whether foreign establishment wages in USD also rise. Because exchange rates increase and decrease, are less stable than minimum wages, and have different underlying drivers, the exchange rate design provides an independent corroboration of the minimum wage findings. Both strategies identify the effect of externally imposed headquarters wage changes on wages at the same firm’s foreign establishments in the same narrowly defined occupation.

Q5. What evidence is marshaled against indirect pathways (technology changes, employment changes, offshoring) as the driver of foreign wage transmission?

The paper presents three types of evidence against indirect pathways. First, including headquarters country×year fixed effects in the descriptive wage regressions — which absorbs any technology shocks originating in the headquarters country that affect all occupations uniformly — leaves the estimated wage anchoring coefficient essentially unchanged. Second, event study and panel regressions using the Brazil RAIS data show little change in total employment at multinationals’ Brazilian establishments following positive external shocks to headquarters wages, which is hard to reconcile with employment-driven or offshoring-driven wage adjustment. Third, a causal forest analysis of the conditional average treatment effect of minimum wage shocks on foreign wages — estimated allowing responses to vary with a wide range of job, employer, sector, and location characteristics — finds that occupation characteristics and sector have little explanatory power for which establishments transmit more, while differences in transmission are more closely related to characteristics of the headquarter-establishment country pair (proximity, similarity, shared language), which are more naturally associated with administrative coordination than with technology or production-style linkages.

Q6. How does occupation skill level moderate wage anchoring, and what does this heterogeneity imply?

Wage anchoring is strongest for low-skill occupations. In the descriptive correlations, a 10 percent higher headquarters wage is associated with 2.8 percent higher foreign wages in low-skill jobs (cleaners, drivers, data entry clerks, security guards) but only about 1.2 percent higher foreign wages in both middle-skill and high-skill jobs. The occupation heterogeneity is visible graphically (Figure 1 Panel C) and holds in regressions interacting the headquarters wage with skill-level indicators. A natural interpretation, consistent with the firm-wide wage-setting procedure explanation, is that firms are most likely to apply standardized pay rules to lower-level positions where local market customization may be seen as less important; higher-skill workers may be more likely to have individually negotiated contracts responsive to local conditions. The heterogeneity also implies that the spatial compression effect — wages in foreign establishments being pulled toward headquarters levels — is particularly pronounced at the lower end of the within-firm wage distribution, affecting positions like cleaners and guards in ways that can result in wages that are, relative to GDP per capita, an order of magnitude higher than what headquarters workers in the same position receive.

Q7. What is the “spatial compression” implication and how does it relate to within-firm wage inequality?

Wage anchoring implies that workers in the same occupation at foreign establishments located in lower-income countries receive wages that are compressed toward headquarters levels rather than fully adjusted to local wages. The paper shows that nominal wages at foreign establishments average about 89 percent of headquarters wages in the same occupation and year — and about 78 percent for establishments in countries poorer than the headquarter country — a ratio that is roughly stable across the within-firm headquarters wage distribution. This partial equalization is what the authors call “across-country wage compression”: it reduces the within-multinational cross-country wage dispersion relative to what would arise from purely market-based, locally responsive wage-setting. The spatial compression is consistent with how many firms self-report setting wages: a survey of primarily North American employers (Culpepper & Associates, 2011) found 29 percent report paying the same nominal wages across locations, and several large employers (Amazon, IKEA, Walmart) have self-imposed country-wide wage floors.

Q8. What role do headquarter-establishment country-pair characteristics play in predicting which establishments exhibit stronger wage transmission?

Using a causal forest algorithm to estimate the conditional average treatment effect of a minimum wage shock at headquarters and then constructing above- versus below-median predicted treatment groups, the paper finds that differences in transmission are “generally not large” but that higher transmission is somewhat associated with characteristics of the headquarter-establishment country pair: pairs that are more closely connected and share more similarities (e.g., common language, closer geographic distance) transmit more. Some foreign-establishment-country characteristics such as inequality and urbanization also appear related. In contrast, occupation characteristics (such as offshorability), the sector the multinational operates in, and characteristics of the headquarter country alone have little explanatory power. The paper notes these findings do not conclusively rule out alternative explanations but are more consistent with administrative coordination channels than with technology- or employment-based ones.

Q9. What role do potential fairness preferences and firm-wide wage norms play in the paper’s interpretation?

The authors suggest several possible mechanisms through which firm-wide wage-setting procedures could operate. Firms may adopt uniform wage-setting to reduce the menu and information costs of localized wage-setting (Lemieux et al., 2012); to increase foreign worker morale, particularly if workers are averse to pay inequality relative to headquarters peers (Card et al., 2012; Dube et al., 2019); or to respond to fairness preferences from headquarters workers or consumers (Harrison & Scorse, 2010). Survey evidence from Alfaro-Urena et al. (2019) explicitly records that multinationals pay high wages abroad in part to “ensure cross-country pay fairness within the MNC.” Alternatively, the authors note that firm-wide wage-setting may represent a form of firm inertia or mistakes — an inability or unwillingness to fully adapt pricing and compensation to local contexts — consistent with DellaVigna & Gentzkow (2019). The paper presents this as an open question for future research rather than definitively adjudicating among the explanations.

Q10. How does the Brazil RAIS data corroborate and extend the global multinationals findings?

The RAIS matched employer-employee administrative data cover all employees at each Brazilian establishment of the 44 multinationals in the global dataset that operate in Brazil, with individual-level information on wages, education, race, gender, age, and tenure. Because RAIS is an administrative census of formal-sector employment rather than a consulting firm’s client dataset, it provides independent corroboration of the main findings. The paper confirms using RAIS that wages of individual workers at multinationals’ Brazilian establishments rise abruptly when their foreign headquarters experience positive external shocks. The RAIS data then enable the additional step of examining employment responses, where event study and panel regressions find little change in total employment at multinationals’ Brazilian establishments following such shocks — evidence against employment- or technology-driven indirect pathways as the primary explanation for wage transmission.

Key Concepts

Wage anchoring: The practice by which a multinational ties wages at its foreign establishments, for workers in a given occupation, to the wage level at its headquarters for the same occupation. In this paper’s usage, anchoring does not mean wages are set identically across locations but that they are partially linked — externally imposed changes in headquarters wages are partially transmitted to foreign establishment wages — rather than being independently set based on local labor-market conditions.

Across-country wage compression: The reduction in the cross-country dispersion of wages within a multinational that results from wage anchoring. Because foreign establishment wages are partially pulled toward headquarters levels rather than fully adjusting to local wages, the multinational’s within-firm wage distribution is more compressed across countries than it would be under purely localized wage-setting. In the paper’s data, this compression is particularly pronounced for low-skill occupations in lower-income host countries.

Firm-wide wage-setting procedures: Administrative practices, such as applying a single pay scale or a fixed wage ratio across all of a firm’s establishments regardless of location, that mechanically link foreign establishment wages to headquarters wages. The paper argues these procedures — rather than correlated technology shocks or employment adjustments — are the proximate driver of wage anchoring, on the basis of the employment non-response in Brazil, the persistence of anchoring after controlling for headquarters-country technology shocks, and the pattern of heterogeneity across country pairs.

Partial transmission: A load-bearing qualifier in this paper describing the magnitude of wage anchoring: headquarters wage changes arising from external shocks are not fully extended to foreign workers, but a fraction of the change is passed through. The estimated pass-through in descriptive regressions ranges from about 0.09 to 0.31 depending on specification and sample, and is highest (around 0.28) for low-skill occupations. The partial nature of transmission means that the spatial compression is real but incomplete.

Wage slope: The difference between log average wages paid by an employer to workers in jobs of consecutive skill levels within an occupational category, at a given establishment. The paper documents that the wage slope at foreign establishments is correlated with the wage slope at headquarters — a 10 percent greater consecutive-skill wage gap at headquarters is associated with a roughly 1.4 percent greater gap at the foreign establishment — suggesting that the anchoring extends beyond the level of wages to the internal wage structure.

External shocks to headquarter wages: Minimum wage increases in the headquarters country or U.S. state, and exchange rate fluctuations that change the USD value of wages set in local currency. These shocks serve as instruments or quasi-experimental sources of variation in headquarters wages that are plausibly exogenous to conditions at foreign establishments, enabling causal identification of the effect of headquarter wage changes on foreign establishment wages.

Causal forest (heterogeneous treatment effect estimation): A machine learning algorithm used in the paper to estimate the conditional average treatment effect of a minimum wage shock at headquarters, allowing the size of the foreign wage response to vary flexibly with a large set of characteristics (job, employer, sector, headquarter country, establishment country, headquarter-establishment country pair). The resulting predicted treatment effect scores are used to construct above- and below-median transmission groups, which are then compared across observable characteristics to identify what predicts stronger wage anchoring.

Summary based on NBER Working Paper 26788 (February 2020, Revised April 2025). Source text was truncated after the beginning of Section 4.1 (minimum wage event study analysis); all causal evidence descriptions draw on the introduction and Section 3–4 framing rather than the full Section 4 tables and Section 5 heterogeneity analysis. AI-assisted, human review pending.

Additionality and Asymmetric Information in Environmental Markets: Evidence from Conservation Auctions

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

This paper investigates the problem of additionality — the likelihood that a conservation action is marginal to (i.e., caused by) an incentive — in the United States Department of Agriculture’s Conservation Reserve Program (CRP), one of the largest and most mature Payments for Ecosystem Services (PES) mechanisms in the world. The CRP pays landowners $1.6–$1.8 billion per year under 10-year contracts to retire cropland and plant grass mixes, trees, or wildlife habitats, using a discriminatory scoring auction in which landowners submit bids on a menu of heterogeneous contracts ranked by a scoring rule.

The central argument is that additionality represents a form of asymmetric information. Landowners possess private knowledge about their counterfactual land use (whether they would have conserved anyway), while the auction screens only on their private cost of accepting the contract. Because lower-cost landowners are lower-cost partly because they expect to conserve regardless of the CRP, cost and additionality are positively correlated — generating adverse selection: the least costly participants to purchase are the least socially valuable. The status quo scoring rule implicitly assumes all landowners are fully additional (tau = 1), an assumption the paper tests and rejects.

The authors construct a dataset linking confidential administrative CRP bid data across seven auctions from 2009 to 2021 to satellite-derived land use classifications from the Cropland Data Layer (30m resolution) and USDA administrative land use reports. They exploit a regression discontinuity (RD) in contract awards around the winning score threshold to estimate the causal effect of CRP contracts on land use at the margin. The first-stage is close to one. The key finding is that CRP contracts reduce cropping by approximately eight percentage points at the margin, but the 100%-additional benchmark predicts a reduction of roughly 33 percentage points (matching the share of land covered by a contract at the margin). Therefore, only approximately one quarter (22–29%) of marginal auction winners are additional — meaning three-quarters would have conserved without the CRP contract.

To test for adverse selection, the authors use the 82% of rejected bidders in the 2016 auction (the most restrictive) for whom counterfactual land use is observed, constructing a landowner-specific additionality measure. They document a systematic positive correlation between bid rental rates (reflecting higher costs) and additionality, which persists conditional on rich observable characteristics including prior land use interacted with soil productivity. Contract choice further reveals additionality: tree-related contract bidders exhibit substantially lower additionality than base grassland contract bidders.

To quantify welfare implications, the authors develop and estimate a joint structural model of bidding and additionality. Costs are inferred via revealed preferences in optimal bidding (following the empirical auctions literature), and additionality is estimated as a conditional expectation function of observable characteristics and unobserved costs, matched to observed land use among rejected bidders via Method of Simulated Moments. Social benefits are taken from the CRP literature and USDA revealed preferences.

Key welfare findings: (1) Despite widespread non-additionality and adverse selection, a hypothetical uniform-price market for the base conservation contract generates social welfare gains of $14.37 per acre-year at the socially-optimal price. Setting price equal to the full social benefit B — ignoring counterfactual land use — causes welfare losses of $12.68 per acre-year, nearly eliminating the gains. (2) The status quo auction generates social welfare gains of approximately $120 million per auction relative to no market, but implements only 12% of the gains achievable under the efficient allocation. (3) Simple modifications to the scoring rule that incorporate expected additionality — via uniform adjustments and market-size reductions — close 37% of the gap between the status quo and the efficient allocation, increasing social welfare by over $300 million per auction. Nearly all gains arise from incorporating additionality into the scoring rule. These modifications are described as implementable by the USDA in practice.

Q: What is additionality, and why does it matter for conservation markets? A: Additionality is defined as the expected impact of contracting on a landowner’s conservation action — i.e., the probability that a landowner would not have conserved absent the incentive. Social surplus depends on both a landowner’s cost of accepting a contract and her additionality, but market mechanisms screen only on cost. When the lowest-cost participants are the least additional, standard procurement mechanisms fail to implement the efficient allocation, undermining the environmental and fiscal effectiveness of conservation programs.

Q: What is the rate of additionality at the margin of CRP contract awards? A: Approximately one quarter (22–29% depending on specification) of marginal auction winners are additional. The RD design shows contracts reduce cropping by about eight percentage points at the margin, compared to the 100%-additional benchmark of approximately 33 percentage points (the share of land covered by the contract at the margin). This implies three-quarters of marginal winners would have conserved without a CRP contract.

Q: What is the empirical evidence for adverse selection? A: Among rejected bidders in the 2016 auction — where additionality is directly observed for 82% of bidders — there is a systematic positive correlation between bid rental rates (reflecting higher costs of accepting the contract) and additionality. This correlation persists conditional on rich observable characteristics, including prior land use interacted with soil productivity estimates. Contract choice also reveals additionality: bidders selecting tree-related contracts have substantially lower additionality than those choosing base grassland contracts.

Q: How does soil productivity relate to additionality? A: USDA-constructed soil productivity estimates, which approximate the earning potential of a parcel, are predictive of additionality in practice, consistent with theory. Higher soil productivity is associated with lower additionality — landowners with less productive land are more likely to conserve regardless of the CRP. Soil productivity is not currently incorporated into the CRP scoring rule to rank bidders.

Q: How is the RD design validated? A: The histogram of normalized score distributions shows no bunching at the winning threshold, validating that bidders do not know the exact ex-post threshold realization. Pre-period RD coefficients are indistinguishable from zero in both the remote sensing and administrative land use data. The first stage (share of bidders with a CRP contract just above the threshold) is close to one. Treatment effect magnitudes are stable over the 10-year contract period with no evidence of attenuation, and there are no spillovers to non-bid fields.

Q: What do the social welfare calculations show for a uniform-price market? A: Despite widespread non-additionality and adverse selection, a hypothetical uniform-price market for the base conservation contract generates social welfare gains of $14.37 per acre-year at the socially-optimal uniform price. However, setting price equal to the full social benefit B — as the status quo implicitly does by assuming tau = 1 — causes welfare losses of $12.68 per acre-year, nearly eliminating all gains.

Q: How does the status quo auction perform relative to the efficient benchmark? A: The status quo auction generates social welfare gains of approximately $120 million per auction relative to no market. The efficient allocation, which awards contracts based on both landowner costs and expected social benefits (incorporating additionality), would be substantially larger. The status quo implements only 12% of the social welfare gains achievable under the efficient allocation.

Q: Can the efficient allocation be implemented by any mechanism? A: Not necessarily. Implementing the efficient allocation requires that the expected net social surplus function B·tau(c) - c be monotonically decreasing in cost, so that a standard incentive-compatible auction can rank bidders appropriately. If lower-cost landowners are sufficiently less additional that the allocation rule is non-monotone in cost, no incentive-compatible mechanism can implement the efficient allocation (per Myerson 1981). Empirically, the authors find that for the base contract the efficient allocation is in the implementable case (similar to their Figure 1a), but implementing it exactly via an incentive-compatible auction remains complex.

Q: What alternative auction designs are proposed, and how much do they improve welfare? A: The authors propose alternative scoring rules that incorporate expected additionality — through uniform adjustments to the scoring rule, reductions in market size, and differentiation among heterogeneously additional landowners based on observables such as soil productivity and contract choice. These simple modifications close 37% of the gap between the status quo and the efficient allocation, increasing social welfare by over $300 million per auction. Nearly all gains come from incorporating additionality into the scoring rule, with a large share accruing through simple uniform adjustments.

Q: How is the structural model of bidding estimated? A: Estimation proceeds in three steps. First, beliefs about the winning score threshold distribution are estimated by simulating auctions via resampling (following Hortacsu 2000). Second, landowner costs are estimated via Maximum Simulated Likelihood using revealed preference inequalities from optimal bidding in the scoring auction. Third, the additionality conditional expectation function is estimated via Method of Simulated Moments, matching observed additionality levels, its distribution across rejected bidders, its covariance with scores, and its distribution by contract choice.

Q: What sources of scoring rule variation identify the model? A: Three sources are used. A mid-mechanism policy change in the 2021 auction added carbon sequestration payments differentially across contracts, providing two bids from the same bidders under different scoring rules. A policy change around 2011 shifted Wildlife Priority Zone (WPZ) bonus points to be contract-specific. Air Quality Zone (AQZ) status shifts the level of the score. These sources provide variation in relative payments across contracts, though the authors note the variation is modest and rely also on parametric extrapolation.

Q: What assumptions are required for identification and how robust are results? A: Key assumptions include perfect compliance (validated by inspection of over 1,000 aerial photographs), no spillovers to non-bid fields (validated in Table 2), and stability of the additionality function tau(z,c,kappa) across auction years. The authors assess robustness to alternative functional forms of tau, conduct a non-parametric inversion exercise across cost quantiles, and construct alternative scoring rules using cross-auction and cross-tract variation to probe the stability assumption. Model-implied additionality at the RD margin (23%) closely matches the empirical RD estimate.

Q: Are the adverse selection and additionality findings specific to the 2016 auction? A: The 2016 auction provides the most complete view because bid fields are observed and 82% of bidders are rejected. But cross-auction evidence replicates the core patterns. RD estimates exploiting threshold variation across auctions show additionality ranging from 10–20% among lower bidders to 40–50% among higher bidders across auctions, consistent with adverse selection. Tree-contract null RD effects replicate across all auctions. Cross-tract cropping rates show similar observable heterogeneity across auctions.

Q: What is the social welfare impact of the market for conservation existing at all? A: Theoretically ambiguous because non-additional landowners may receive transfers without generating social value, and adverse selection may tilt the market toward low-additionality participants. Empirically, despite these concerns, there exist positive social welfare gains of $14.37 per acre-year at the socially-optimal uniform price for the base contract, indicating that conservation markets of this type can improve welfare even in the presence of substantial non-additionality and adverse selection.

Additionality: The expected impact of contracting on a landowner’s conservation action — formally, tau(c) = E[1 - a_i0 | c = c_i], the probability that a landowner would not have conserved absent the incentive. A landowner is additional if she would have cropped without the CRP contract; the social benefit of contracting depends only on this incremental conservation impact.

Adverse Selection: The positive correlation between landowner cost of accepting a contract and additionality. Because landowners with low costs are low-cost partly because they expected to conserve regardless of the program, lower-cost participants are less socially valuable. This upward-sloping contract value curve mirrors adverse selection in insurance markets as modeled by Einav, Finkelstein, and Cullen (2010).

Contract Value Curve: The function B·tau(F^{-1}_C(q)) plotting the expected social value of contracting at each quantile q of the cost distribution. It lies below the social benefit B due to non-additionality and slopes upward due to adverse selection. The vertical distance between the contract value and marginal cost curves equals expected social surplus B·tau(c) - c.

Efficient Allocation: The allocation that maximizes expected social surplus B·tau(c) - c by awarding contracts to landowners for whom this quantity is positive. Implementing this allocation via an incentive-compatible mechanism requires that B·tau(c) - c be monotonically decreasing in cost; if not, no standard mechanism can achieve it.

Scoring Rule: The known function s(b_i, z^s_i) that converts a landowner’s multi-dimensional bid (rental rate and contract choice) and observed characteristics into a score, determining contract awards. The status quo scoring rule implicitly assumes full additionality (tau = 1), ranking bidders as if all conservation actions are marginal to the incentive.

Source Text Origin: The classification of the text on which a summary is based — “pdf” or “oa-html” for full working paper text, or “abstract-only” which is blocked from summarization. Determines the validity and completeness of any summary produced.

An Equilibrium Analysis of the Effects of Neighborhood-Based Interventions on Children

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

Overview

Research question. How should governments design neighborhood-based policies to improve long-run outcomes for children, once one accounts for general equilibrium (GE) forces—endogenous rents, neighborhood quality, wages, and distortionary taxation—that small-scale experimental studies cannot identify?

Model. The paper embeds neighborhood effects into a quantitative, heterogeneous-agent overlapping-generations (OLG) model with endogenous location choice and child skill development. The economy has three building blocks: (1) a dynastic life-cycle structure in which parents choose a neighborhood (from two options: a disadvantaged n=1 and an advantaged n=2) and allocate time to child development, with child skills produced by a nested CES aggregator combining parental time and neighborhood quality (proxied by per-capita income in the tract); (2) a GE Aiyagari incomplete-markets framework with endogenous labor supply, wage uncertainty, and progressive labor taxation; and (3) a government that finances housing vouchers or place-based wage subsidies by adjusting the labor income tax parameter, with all additional net expenses fully offset by tax revenue. Housing supply is upward-sloping (elasticity 1.75, from Saiz 2010), so rents are endogenous.

Data and calibration. The model is estimated by simulated method of moments to match U.S. data from the 2000s, drawing on the PSID, NLSY, ATUS, the 2012–2016 ACS, and the Opportunity Atlas (Chetty et al. 2018). Neighborhoods are mapped to Census tracts divided into bottom-10-percent and top-90-percent median household income groups within each commuting zone. Key targeted moments include the income gap between neighborhoods (108 percent higher mean individual income in n=2), the 30 percent higher incomes for children from low-income families raised in the better neighborhood, and a 32 percent gap in weekly parental time with children across neighborhoods.

Validation. Before policy counterfactuals, the calibrated model is validated against two bodies of reduced-form evidence. First, a simulated small-scale, single-generation, partial-equilibrium voucher experiment generates 23 percent higher income for children—close to the 31 percent MTO experimental estimate from Chetty et al. (2016), with the difference largely explained by a smaller poverty-rate contrast (18 vs. 22 percentage points) in the simulation. Second, a simulated 20 percent place-based wage subsidy generates 17–21 percent earnings gains for adult residents of n=1, consistent with Busso et al.’s (2013) quasi-experimental EZ estimates of 17–24 percent.

Main findings — housing vouchers. The welfare-maximizing voucher program features a 100 percent subsidy rate, targets households with children and wages below the 80th percentile (fourth quintile), and is financed by progressive labor taxes. In the long-run steady state this policy raises 12.5 percent more children in the advantaged neighborhood, increases labor productivity by 1.1 percent, reduces income inequality (variance of log after-tax lifetime earnings) by 6.3 percent—comparable in magnitude to the Sweden–U.S. after-tax inequality gap—and raises upward mobility by 27.7 percent (roughly half its standard deviation across U.S. Census tracts). The average marginal tax rate must increase by 15.7 percent to fund the program. Despite this, long-run welfare rises by 3.4 percent in consumption equivalence units. A decomposition shows that intergenerational dynamics add 11.5 percentage points to welfare (relative to a short-run, single-generation scenario), while taxation subtracts 10.2 percentage points, and rent plus neighborhood-quality effects together subtract only 1.4 percentage points—leaving the net long-run GE gain similar to the short-run partial-equilibrium gain of 3.5 percent. Crucially, non-targeting children generates welfare losses of 5.0 percent, confirming that restriction to households with children is essential.

Main findings — place-based wage subsidies. A 12 percent wage subsidy to workers in the disadvantaged neighborhood yields the highest steady-state welfare gain of 0.7 percent. This is approximately one-fifth of the gain achievable with the optimal voucher. The subsidy induces substantial resorting toward n=1, reducing the share of children in n=2 by 6.7 percent while raising neighborhood quality in n=1 by 19.7 percent. Income inequality falls by 8.7 percent and upward mobility rises by 20.4 percent. However, in a short-run partial-equilibrium setup, the wage subsidy has a negative welfare effect of −1.0 percent because it draws parents (and their children) into the disadvantaged area; the positive net effect only emerges through long-run intergenerational channels (+2.5 percentage points) and equilibrium neighborhood-quality adjustments.

Political economy. Because voucher gains are concentrated among young cohorts (those aged 16–43 at introduction), only 33 percent of incumbent adults would rationally vote for the housing voucher program. In contrast, the place-based wage subsidy provides positive average welfare gains for all age cohorts alive at introduction, yielding estimated majority support from over 63 percent of adults. This creates a fundamental political economy tradeoff: the policy with the larger long-run social gains lacks majority democratic support, while the policy with broader support delivers smaller long-run gains.

In depth

Q1. What are the two market frictions that justify government intervention in the model?

A1: The first friction is the absence of intergenerational borrowing markets: parents cannot borrow against their child’s future income, which limits the parent’s willingness to pay the higher rent in n=2 to give their child a developmental advantage. Housing vouchers act as a tax-financed substitute for this missing contract by paying the rent premium and recovering the cost through taxes on the high-earning adults the children become. The second friction is a neighborhood externality: individuals do not internalize the effect of their own income on the neighborhood quality experienced by neighbors’ children. Place-based wage subsidies partially correct this externality by subsidizing work in the disadvantaged area, raising local income per capita and thereby improving the neighborhood quality index for all children resident there.

Q2. How is neighborhood quality defined and modeled, and why is this specification chosen?

A2: Neighborhood quality sn is defined as total income per capita (the sum of labor and capital income) for all residents of neighborhood n, including non-workers. This specification is intended to capture multiple mechanisms: school quality (which depends on local tax bases), role-model effects from productive adults, and social organization effects through adult supervision of children. The formulation includes retired and non-working residents, which means the arrival of children mechanically reduces neighborhood quality per capita in the model, partially capturing a crowding channel. Formally, the neighborhood spillover function takes the power form f(sn) = A * sn^ζ, where ζ governs the elasticity of child development to neighborhood quality.

Q3. How does the paper validate the model’s key mechanism — the neighborhood effect on children?

A3: The validation mimics the MTO RCT within the calibrated model: the government provides a 100 percent rent voucher usable only in n=2 to households in n=1 with incomes below the 10th percentile, holding prices and neighborhood qualities fixed (as in a small-scale experiment). The model generates 25 percent voucher take-up and a 23 percent increase in children’s income in their late 20s. This compares to the experimental MTO estimate of approximately 31 percent. The paper attributes most of the gap to the smaller poverty-rate contrast in the simulation (18 percentage points) relative to MTO (22 percentage points), and shows that plotting the simulated result against the site-specific MTO estimates in a scatterplot of child income gains against neighborhood poverty reductions places the model prediction on the fitted line through the experimental data.

Q4. What is the quantitative role of long-run intergenerational dynamics in the voucher program, relative to other GE channels?

A4: The decomposition in Table 5 isolates four GE channels. Starting from a short-run partial-equilibrium welfare gain of 3.5 percent (for the children of a single treated generation), allowing the economy to operate for the long run while holding prices and taxes fixed raises welfare to 15.0 percent — an increase of 11.5 percentage points — because improved skills in one generation create higher-skilled, higher-income parents who invest more in the next generation. Introducing housing market price adjustments (rents rise by 3.9 percent in n=2) reduces welfare by only 0.6 percentage points. Allowing neighborhood quality to adjust (quality in n=2 falls by 4 percent as lower-income families move in) reduces welfare by an additional 0.8 percentage points. Adding full taxation to balance the government budget reduces welfare by 10.2 percentage points, from 13.6 to 3.4 percent. The four channels nearly cancel, leaving the long-run GE steady-state gain close to the short-run single-generation gain.

Q5. Why does the optimal voucher program require targeting to families with children, and what happens without this restriction?

A5: When the voucher is extended to all households regardless of children (Column 6 of Table 4), nearly 82.6 percent of the population receives a subsidy, pushing almost everyone to n=2. Rents in n=2 rise by 5.3 percent. To finance this much broader program, the average marginal tax rate must increase by 44 percent, far exceeding the 15.7 percent required for the children-targeted program. The large tax increase suppresses labor supply and income, which reduces neighborhood quality in n=2 by 11.6 percent. The net effect is a welfare loss of 5.0 percent. The intuition is that the benefit of the voucher program flows primarily through child skill development, so subsidizing adults without children is fiscally expensive without producing the intergenerational gains that justify the cost.

Q6. What drives the difference in long-run welfare gains between vouchers (3.4 percent) and place-based wage subsidies (0.7 percent)?

A6: The primary channel is labor productivity. The optimal voucher program raises labor productivity by 1.1 percent by increasing the average neighborhood quality to which children are exposed by 1.2 percent. The wage subsidy raises productivity by only 0.2 percent because it induces resorting toward the disadvantaged neighborhood, meaning children’s average neighborhood quality actually decreases by 0.2 percent despite large improvements in n=1’s quality (up 19.7 percent), since fewer children reside in n=1 after the subsidy draws their parents there. Inequality reduction is not the source of the gap: the wage subsidy actually reduces inequality more (8.7–8.9 percent) than the voucher (6.3 percent), but this inequality effect does not translate into larger aggregate welfare because productivity effects dominate.

Q7. How does the wage subsidy produce positive long-run welfare when it generates negative welfare in the short run?

A7: In the short run, the wage subsidy draws parents into the disadvantaged neighborhood to exploit higher wages, which reduces the share of children in the advantaged neighborhood n=2 and lowers children’s late-life productivity (welfare of −1.0 percent for treated children in the single-generation scenario). Two long-run channels flip the sign. First, the subsidy is permanent, so children themselves receive it as adults, providing a direct wage income benefit. Second, the sustained presence of higher-income workers in n=1 raises neighborhood quality there durably (by 19.7 percent at the steady state), which benefits the children who reside in n=1. Together these intergenerational effects add 2.5 percentage points to welfare, while taxation costs reduce it by only 1.4 percentage points, yielding a net gain of 0.7 percent.

Q8. What determines the political economy divide between the two policies?

A8: For the housing voucher, welfare gains are concentrated among younger incumbent adults (ages 16–43), particularly those who are about to have or already have children, while older adults tend to lose because they face higher taxes without benefiting from improved neighborhood quality for their (now independent) children. This concentration implies only 33 percent of incumbent adults would support the voucher under the model’s welfare metric. For the place-based wage subsidy, average welfare gains are positive for every age cohort alive at introduction (though larger for younger cohorts), because the wage subsidy raises incomes for workers in n=1 immediately and benefits from equilibrium rent declines in n=1 that allow all residents to benefit. Over 63 percent of adults would support the wage subsidy. The paper notes that if the government could borrow to initially finance the voucher program and pay for it later (as in Daruich 2020 for early childhood programs), majority support for the voucher could potentially be achieved.

Q9. How sensitive are the welfare results to the key calibrated parameters?

A9: The sensitivity analysis (Table 9, following Andrews et al. 2017) shows that individual parameters would need to change substantially to overturn the conclusion that vouchers generate larger steady-state welfare gains than wage subsidies. For example, the altruism parameter β̃ would need to increase by 22 percent to eliminate the voucher welfare gain, which would require average parental transfers to rise to 198 percent of income — far from the empirical target of 125.4 percent. Using the more conservative tract-level housing supply elasticity from Baum-Snow and Han (2021) of 0.3–0.4 (about 80 percent below the baseline Saiz 2010 estimate of 1.75) would reduce the voucher welfare gain from 3.37 to approximately 2.57 percent, not reversing the qualitative conclusion. The parameters with the largest influence on welfare gains are the labor disutility parameter µ and the altruism parameter β̃; the housing supply elasticity matters more for the voucher than the wage subsidy because easier housing supply accommodates growth in n=2 without displacement under the voucher.

Q10. What does the transition path of the voucher program look like, and why do welfare gains initially dip before recovering?

A10: When the voucher is unexpectedly introduced, the first newborn cohort gains approximately 4 percent welfare, but gains for subsequent cohorts initially dip to around 3 percent before stabilizing at 3.4 percent by the 20th post-introduction cohort. The dip occurs because moving costs slow resorting: immediately after introduction, rents in n=2 begin rising and neighborhood quality there begins falling as low-income families move in, but the capital stock adjustment (which would counteract these effects by raising GDP) lags the resorting. The rebound comes as capital accumulates in n=2 over time and as intergenerational productivity gains build through successive cohorts of better-skilled parents. Labor productivity jumps noticeably for the first cohort born to parents who received the voucher (approximately 28 years after introduction) and again for the first cohort born to grandparents who received it, visibly demonstrating the intergenerational mechanism. In contrast, the wage subsidy’s welfare gains are approximately constant at 0.7 percent across all cohorts because the key channels (neighborhood quality improvement in n=1 and wage gains) materialize rapidly and remain stable throughout the transition.

Key Concepts

Neighborhood quality (sn): In this paper, neighborhood quality is not school quality or amenities in a generic sense but is explicitly defined as total income per capita — the sum of labor income and capital income — for all residents of neighborhood n, including non-workers. This endogenous measure rises when higher-income or more productive residents move in and falls when lower-income residents or additional children arrive.

Intergenerational borrowing constraint: The inability of parents to borrow against their child’s future income, modeled as a non-negativity constraint on the monetary transfer from parent to child (transfer ≥ 0). This is the paper’s first key market friction: without it, a poor parent who moved to a better neighborhood would smooth consumption across generations by having the high-earning child compensate the parent. The constraint prevents this, reducing parental investment below the socially efficient level.

Consumption equivalence (veil of ignorance): The welfare metric used throughout the policy analysis. It is defined as the percentage change in consumption that would make a newborn individual indifferent between the pre-policy and post-policy steady states, computed before knowing their position in the skill or income distribution. This is the paper’s measure of long-run steady-state welfare.

Parental investment aggregator (CES): A nested constant-elasticity-of-substitution function that determines how parental time τ and neighborhood quality sn combine to form the effective investment input I into child skill development: I = Ā[αI f(sn)^γ + (1 − αI)τ^γ]^(1/γ). The elasticity parameter 1/(1 − γ), estimated at 0.41, governs the degree of complementarity between time and neighborhood quality; a lower elasticity (γ = −1.43) implies the two inputs are complements, so parents with children in better neighborhoods also spend more time with them.

Place-based wage subsidy: A neighborhood-specific wage premium (denoted w̃s) paid to all workers who both live and work in the disadvantaged neighborhood n=1, raising their effective wage to w1 = (1 + w̃s)w2. This policy targets the neighborhood externality by increasing the income of residents in n=1, which raises neighborhood quality and provides an incentive for higher-skilled workers to relocate to (or remain in) the disadvantaged area.

Upward mobility: Measured in this paper as the probability that a child born to parents in the bottom 20 percent of the income distribution reaches the top 20 percent of the income distribution during the working stage of their own life. This is distinct from mean income rank measures; it specifically tracks cross-quintile transitions in the model’s stationary distribution.

Equilibrium decomposition: A simulation-based method in which GE channels are progressively activated. Starting from a short-run, partial-equilibrium, single-generation baseline (analogous to an RCT), the authors sequentially allow: (i) long-run intergenerational dynamics while holding prices fixed; (ii) housing market price adjustments; (iii) neighborhood quality adjustments; (iv) tax and production-price adjustments. Each step’s change in outcomes identifies the quantitative contribution of that specific channel.

Anatomy of the Phillips Curve: Micro Evidence and Macro Implications

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

Layer 1 — Overview

Research Question

This paper addresses a fundamental puzzle in macroeconomics: why do estimates of the New Keynesian Phillips curve (NKPC) slope differ sharply depending on whether real marginal cost or the output gap is used as the real activity variable? The conventional, output gap-based NKPC yields very flat slope estimates (e.g., 0.006 to 0.024 in Hazell et al. 2022 and Rotemberg and Woodford 1997), which has led to the widespread view that the Phillips curve is “flat,” at least during the pre-pandemic period. The authors argue that this view conflates two distinct structural relationships: the elasticity of inflation with respect to real marginal cost, and the elasticity of marginal cost with respect to the output gap.

Data and Methodology

The authors assemble a unique quarterly micro-level dataset covering 4,598 manufacturing firms in Belgium over 84 quarters (1999:Q1–2019:Q4), totaling 132,915 observations. The dataset combines product-level domestic prices and quantities from the PRODCOM administrative database, customs data on foreign competitors’ prices, and firms’ variable production costs (labor costs from social security declarations plus intermediate input costs from VAT declarations). Intermediate inputs account for approximately 75 percent of total variable costs on average and are the most volatile cost component (within-firm coefficient of variation 1.77, versus 0.77 for labor costs).

Their estimation strategy follows a “bottom-up” approach. Starting from a theoretical framework with heterogeneous firms subject to Calvo (1983) nominal rigidities and strategic complementarities in price setting (imperfect competition including dynamic oligopoly and Kimball demand), they derive a forward-looking dynamic pass-through regression linking a firm’s current price to discounted present values of its own marginal costs and competitors’ prices, plus a lagged price level that serves as an error-correction term. This is Model A; robustness variants include Model B (absorbing competitor prices via industry-by-time fixed effects), Model C (imposing an AR(1) process for marginal cost), and Model A-U (unrestricted lagged-price coefficient).

The structural parameters governing the NKPC slope — the degree of nominal rigidity (θ) and the strength of strategic complementarities (Ω) — are estimated jointly via GMM. Instruments for marginal cost are four-quarter-lagged firm-level total factor productivity (TFPQ), and instruments for competitors’ prices exploit variation in EU-area export prices to third-country destinations and bilateral exchange rates between non-EU competitor currencies and the Euro. Sector-by-time fixed effects and firm fixed effects absorb confounding trends, shifting trend inflation, and permanent markups.

Main Findings with Quantitative Magnitudes

The baseline estimate (Model A) yields θ = 0.711 (SE 0.014), implying that prices remain fixed for approximately three to four quarters on average, consistent with Nakamura and Steinsson (2008) Belgian PPI data (0.72). The strategic complementarity parameter is Ω = 0.570 (SE 0.059), indicating that competitor price dynamics reduce the pass-through of own marginal cost shocks by approximately half relative to the no-complementarities benchmark.

These structural estimates imply a slope of the marginal cost-based NKPC of λ = 0.052 (SE 0.007), tightly estimated and robust across specifications: λ = 0.077 in Model B, λ = 0.069 in Model C, and λ = 0.056 in the unrestricted Model A-U. This slope is two to ten times larger than existing estimates of the conventional output gap-based NKPC slope (κ ≈ 0.024, Rotemberg and Woodford 1997; κ ≈ 0.006, Hazell et al. 2022).

Reconciling the High Cost-Based Slope with the Flat Output-Based Slope

The paper shows that the output-based slope κ equals the product of the cost-based slope λ and the output elasticity of marginal cost σ_y: κ = λ · σ_y. Using Bartik-style instruments based on high-frequency ECB monetary policy surprises interacted with industry-level sensitivities, the authors estimate σ_y using two models. Model D yields σ_y = 0.406 and κ = 0.021; Model E (directly regressing changes in marginal cost on changes in output) yields σ_y = 0.112 and κ = 0.006. These estimates are consistent with, and overlap with, Rotemberg and Woodford (1997) and Hazell et al. (2022) during the pre-pandemic sample period. The low elasticity of marginal cost to output is attributed to near-constant short-run returns to scale at the firm level and wage rigidity that mutes general equilibrium effects.

Aggregate Inflation Dynamics

Feeding an aggregate marginal cost index (constructed as a Törnqvist-weighted average of firm-level marginal costs) into the model-implied inflation expression produces a series that tracks Belgian manufacturing PPI inflation well: marginal cost fluctuations alone account for approximately 70 percent of inflation variation (R² = 0.68, correlation 0.8), without appealing to unobservable cost-push shocks or inflation lags.

Model Validation via Supply Shocks

A validation exercise using identified oil shocks (Känzig 2021 — measured as unexpected OPEC-day movements in oil futures prices) confirms the model. A one-standard-deviation shock to oil prices (a 15.7 percent increase in Brent crude) raises firms’ real marginal costs by approximately 1.5 to 3 percent within the first three quarters, before reverting. The price response peaks at approximately 3 percent after six quarters, consistent with nominal rigidities generating a delayed but persistent response. Impulse-response matching yields λ_IRF = 0.042 (SE 0.005), within the confidence bands of the micro-level estimate λ = 0.052, validating the bottom-up approach.

Scope Conditions

All estimates are drawn from Belgian manufacturing firms over 1999–2019, a period of moderate inflation during which Calvo pricing provides a good approximation of firm behavior. The authors note that the elasticity of marginal cost to output may be time-varying and nonlinear, and that during large aggregate shocks (such as the post-pandemic inflation surge), both the frequency of price adjustment and the sensitivity of marginal cost to output can rise substantially, requiring state-dependent pricing models (addressed in a companion paper, Gagliardone et al. 2025).

In depth

Q1. What is the primitive formulation of the NKPC, and how does it differ from the conventional formulation?

A1: The primitive NKPC features real marginal cost (in log-deviation from its steady state) as the real activity variable: π_t = λ·mc_t + β·E_t{π_{t+1}} + u_t, where λ is the slope depending on nominal rigidities and strategic complementarities. The conventional formulation uses the output gap (or unemployment gap) as a proxy for marginal cost, which is valid only under specific conditions including perfectly flexible wages. When those conditions fail, the output gap is a poor proxy for marginal cost, typically leading to downward bias in slope estimates. Even when a proportionality holds, the output-based slope κ equals λ multiplied by σ_y (the output elasticity of marginal cost), so the two slopes carry different economic content.

Q2. What structural parameters govern the slope of the cost-based NKPC, and what is the formula?

A2: The slope is λ = (1−θ)(1−βθ)/θ, where θ is the Calvo probability of price non-adjustment (capturing nominal rigidity) and Ω = Γ/(1+Γ) is the strategic complementarities parameter derived from the markup elasticity Γ with respect to relative prices. High nominal rigidity (high θ) flattens the slope by making individual price adjustments less frequent; strong strategic complementarities (high Ω) flatten it further because firms mute their price response to marginal cost in order to avoid deviating from competitors. The discount factor β is calibrated at 0.99 for quarterly data.

Q3. How does the dynamic pass-through regression differ from the static (long-run) pass-through regressions used in prior literature?

A3: The dynamic pass-through regression (Model A) includes the firm’s lagged price as a regressor, which functions as an error-correction term controlling for persistent deviations between the price and the optimal reset price. Failing to include this term with quarterly data leads to omitted variable bias of magnitude −θ·Var(Δp_ft), since the cointegration error is autocorrelated with coefficient θ. Static pass-through regressions (as in Amiti, Itskhoki and Konings 2019 using annual data) are appropriate only when nominal rigidities can be ignored (θ ≈ 0); with quarterly data and θ ≈ 0.711, the orthogonality condition of the static model fails and the dynamic framework is necessary.

Q4. What are the baseline estimates of the structural parameters, and how robust are they?

A4: The baseline Model A yields θ = 0.711 (SE 0.014) and Ω = 0.570 (SE 0.059), implying prices fixed for approximately three to four quarters and competitor-price influence roughly equal to own marginal cost influence. The implied NKPC slope is λ = 0.052 (SE 0.007). Robustness checks across six specifications (Models B, C, A-U, variable SR-RTS controls, Translog TFPQ, eight-quarter-lagged instrument) yield λ in the range 0.044 to 0.077, with all estimates statistically significant and within each other’s confidence bands. The unrestricted model (A-U) cannot reject the restriction Ϛ = θ on the lagged-price coefficient (p-value 0.90).

Q5. What is the short-run elasticity of a firm’s own price to a permanent marginal cost shock, and how do nominal rigidities and strategic complementarities each contribute?

A5: The short-run pass-through elasticity is (1−Ω)(1−θ) ≈ (1−0.570)(1−0.711) ≈ 0.125. This is substantially below one because both forces dampen price adjustment: nominal rigidity (1−θ ≈ 0.289) means most firms cannot adjust in any given quarter, and strategic complementarities (1−Ω ≈ 0.430) mean that adjusting firms reduce their pass-through to avoid deviating from competitors’ prices. Without strategic complementarities (Ω = 0), the elasticity would be roughly 0.289; without nominal rigidities (θ = 0), it would be roughly 0.430; both together produce the observed 0.125.

Q6. How is marginal cost measured in the data, and why is the inclusion of intermediate input costs important?

A6: Marginal cost is proxied by average variable cost per unit of output: the log-nominal marginal cost equals ln(TVC_ft/Y_ft) + ln(1+ν_ft), where TVC is the sum of intermediate input costs (from VAT declarations) and labor costs (wage bill from social security declarations), and Y_ft is a quantity index. Intermediate inputs account for approximately 75 percent of total variable costs on average and are the most volatile component (within-firm coefficient of variation 1.77 vs 0.77 for labor). The authors note that DSGE models typically feature only labor as a variable input, but accounting for intermediates is pivotal because intermediate goods price shocks were among the most important drivers of the post-pandemic inflation surge.

Q7. What instruments are used for marginal cost and competitors’ prices, and what are the identifying assumptions?

A7: The instrument for marginal cost is the four-quarter lagged firm-level TFPQ (physical total factor productivity), estimated as the residual from a gross-output production function. Its relevance depends on TFP persistence (confirmed); the exclusion restriction requires that persistent TFP variation is orthogonal to current and future demand shocks after removing permanent demand components (via firm fixed effects) and industry trends (via sector-by-time fixed effects). Two instruments for competitors’ prices exploit international trade variation: (i) sales-weighted average export prices of EU-area competitors to non-Belgium, non-EU destinations (orthogonal to Belgian demand shocks by construction), and (ii) bilateral exchange rate movements between non-EU competitor currencies and the Euro. All instruments pass the Cragg-Donald and Kleibergen-Paap F-statistics (strongly rejecting weak instruments) and Hansen-Sargan over-identification tests (failing to reject validity).

Q8. What evidence supports the validity of the TFPQ instrument against capacity utilization concerns?

A8: The authors run two empirical tests. First, regressing marginal cost on four-quarter-lagged capacity utilization yields a small, statistically insignificant elasticity (0.011, SE 0.052), suggesting the TFPQ instrument’s predictive power does not reflect capacity utilization variation. Second, re-estimating with “purified” TFPQ instruments adjusted for capital utilization (Column 4) and for both capital and labor utilization (Column 5) produces parameter estimates and NKPC slopes essentially unchanged from baseline. Additionally, regression residuals show only weak and short-lived autocorrelation (−0.09 at one-quarter lag, p=0.09; −0.01 at two-quarter lag, p=0.69), indicating demand shocks are highly transitory after conditioning on fixed effects.

Q9. How does the model track aggregate Belgian manufacturing PPI inflation, and what does this imply for cost-push shocks?

A9: Using the reduced-form expression π_t = λ̃(mc_t^n − p_{t-1}) + α + θu_t, where the reduced-form slope λ̃ = 0.22 is evaluated at baseline structural estimates, the model produces a model-implied inflation series that accounts for approximately 70 percent of variation in manufacturing PPI inflation (R² = 0.68, correlation 0.8), without including inflation lags or cost-push shocks. The model captures the inflation drop during the 2008 financial crisis, the run-up in 2016, and the subsequent decline. This contrasts with the quantitative DSGE literature in which cost-push shocks (variation in desired price and wage markups) account for approximately 70 percent of inflation volatility (e.g., Primiceri, Schaumburg and Tambalotti 2006).

Q10. How do the authors estimate the output elasticity of marginal cost σ_y, and what do they find?

A10: They use two approaches. Model D is a pricing equation directly relating firm-level prices and nominal output (value added), estimated via GMM, instrumented with Bartik-style shifters based on high-frequency ECB monetary policy surprises (Altavilla et al. 2019) interacted with industry-level sensitivities. Model E directly regresses changes in nominal marginal cost on changes in nominal output, also instrumented. Model D yields σ_y = 0.406 (SE 0.099) and implied κ = 0.021 (SE 0.005); Model E yields σ_y = 0.112 (SE 0.026) and κ = 0.006 (SE 0.001). The low σ_y is consistent with near-constant short-run returns to scale at the firm level and wage rigidity muting general equilibrium labor-market feedback, at least during the moderate-inflation pre-pandemic period.

Q11. How does the oil shock validation exercise confirm the cost-based NKPC slope estimate?

A11: Following Känzig (2021), the authors identify oil shocks as unexpected movements in Brent crude oil futures around OPEC meeting days, normalizing to a one-standard-deviation shock (15.7 percent Brent increase). Local linear projection IRFs show that firms’ real marginal costs rise 1.5 to 3 percent within three quarters and then revert, while prices peak at approximately 3 percent increase after six quarters (consistent with nominal rigidity delaying the price response). Impulse-response matching — minimizing the weighted distance between empirical and model-implied price IRFs — yields λ_IRF = 0.042 (SE 0.005), which is close to and within the confidence bands of the micro-level estimate λ = 0.052, validating the bottom-up estimation approach.

Q12. What do the estimates imply about why the conventional NKPC appears flat in normal times?

A12: The flat conventional NKPC slope (κ ≈ 0.006–0.024) does not reflect limited transmission of marginal cost fluctuations to inflation — that transmission is high (λ ≈ 0.052–0.077). Rather, flatness reflects a weak link between the output gap and marginal cost during the pre-pandemic period (σ_y ≈ 0.112–0.406), attributable to near-constant short-run returns to scale in production and wage rigidity. This decomposition matters for policy: supply shocks that directly raise marginal cost will pass through strongly to inflation even when output does not move much, whereas demand shocks that operate through the output-cost channel face attenuated transmission.

Q13. Under what conditions does the cost-based Phillips curve decompose cleanly into a product of the two elasticities?

A13: The decomposition κ = λ · σ_y requires assuming that real wages are flexible and determined in general equilibrium at the industry level, with real wages increasing in industry output with elasticity σ_w; that the natural level of output is defined as the equilibrium under flexible prices and constant desired markups; and that the firm’s marginal product of labor depends on productivity and output with a common short-run returns-to-scale parameter ν (homogeneous across firms and time-invariant). Under these assumptions (which parallel those used to derive the conventional NKPC in the standard NK model), the output elasticity of marginal cost is σ_y = σ_w + ν, and the theoretical restriction κ = λ · σ_y holds exactly.

Q14. How do macroeconomic complementarities from aggregate decreasing returns to scale affect the NKPC slope?

A14: If aggregate SR-RTS fall below unity, the NKPC slope formula gains an additional term Θ = 1/(1+γν(1−Ω)) < 1, where ν is inversely related to average SR-RTS and γ is the within-industry elasticity of substitution. However, empirical estimates of sectoral SR-RTS range from 0.93 to 0.98, with an aggregate estimate of approximately 0.965 (implying ν ≈ 0.036). Given this and calibrating γ = 4, Θ ≈ 0.941, so macroeconomic complementarities would reduce the NKPC slope by only about 6 percent — well within the confidence bounds of the baseline estimates. The authors conclude that the constant-returns assumption in their main framework is a good approximation.

Key Concepts

Primitive (cost-based) NKPC slope (λ): The coefficient linking inflation to real marginal cost in the underlying New Keynesian pricing equation, defined as λ = (1−θ)(1−βθ)/θ. It captures how strongly firms’ aggregate price setting responds to movements in real marginal cost per unit of output, holding the discount factor, nominal rigidity, and strategic complementarities fixed. Estimated at 0.052 (tightly, range 0.044–0.077 across specifications) for Belgian manufacturing.

Calvo probability of price non-adjustment (θ): The parameter from Calvo (1983) staggered price setting capturing the share of firms that cannot change their price in a given period, equal to one minus the per-period probability of price adjustment. In this paper, θ is estimated directly from the dynamic pass-through regression coefficient on lagged prices, yielding θ ≈ 0.711, implying prices fixed approximately three to four quarters on average.

Strategic complementarities parameter (Ω): Defined as Ω = Γ/(1+Γ), where Γ is the elasticity of a firm’s desired markup with respect to its own relative price. Captures the extent to which a firm weights competitors’ prices (rather than its own marginal cost) when resetting its price. High Ω means firms strongly mute price responses to own cost changes to avoid relative price deviations from competitors. Estimated at Ω ≈ 0.570, implying competitor prices and own marginal cost enter the reset price with roughly equal weight.

Dynamic pass-through regression: A forward-looking pricing equation (Model A) relating observed firm prices to the discounted present values of own marginal costs and competitors’ prices, plus lagged own price as an error-correction term. The structural parameters θ and Ω are identified jointly from the regression coefficients, using GMM with instruments for the present values. The dynamic specification is necessary at quarterly frequency because the error-correction term (omitted in static pass-through models) is non-negligible when θ > 0.

Output elasticity of marginal cost (σ_y): The elasticity of firm-level real marginal cost with respect to the firm-level output gap, defined under the assumptions that real wages are flexible and industry-level, equal to σ_y = σ_w + ν (wage elasticity with respect to industry output plus the short-run returns-to-scale parameter). This parameter bridges the cost-based and output-based Phillips curve slopes via κ = λ · σ_y. Estimated from micro data using monetary policy shock instruments at σ_y ≈ 0.112–0.406 in the pre-pandemic period.

Short-run returns to scale (SR-RTS): The extent to which a firm’s marginal cost rises with output scale in the short run, parameterized by ν in the cost function MC^n_ft = C_{it} · A_{ft} · Y_ft^ν. If ν = 0, marginal cost is independent of output scale (constant returns), which the authors assume in their baseline. Firm- and sector-level estimates from Translog production functions yield SR-RTS ≈ 0.93–0.98 across sectors (aggregate ≈ 0.965), broadly consistent with the constant-returns assumption and implying modest macroeconomic complementarities.

Reduced-form aggregate pass-through slope (λ̃): A composite parameter capturing the contemporaneous pass-through of aggregate real marginal cost (defined as nominal marginal cost relative to the lagged price level) into quarterly inflation under the assumption that nominal marginal cost follows a random walk. Evaluated at θ ≈ 0.70 and Ω ≈ 0.52 (median across models), λ̃ = 0.22. This is distinct from the structural NKPC slope λ because it also captures the persistence of cost shocks.

Borrowing and Spending in the Money: Debt Substitution and the Cash-Out Refinance Channel of Monetary Policy

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

Overview

Research Question. Does monetary policy stimulate household borrowing and consumption by enabling cash-out mortgage refinancing (“the cash-out refinance channel”), or does it primarily induce substitution across borrowing products without meaningfully changing total new household borrowing?

Motivation. Prior work (Eichenbaum, Rebelo and Wong 2022; Berger et al. 2021) interprets the strong positive correlation between a borrower’s refinance incentive and cash-out refinancing as evidence of a potent, path-dependent monetary policy transmission channel: when rates fall below a borrower’s outstanding mortgage rate (“in-the-money”), the incentive to refinance generates large cash-out activity and consumption. This interpretation presumes that mortgages are effectively the only household borrowing product and that cash-out refinancing reflects a stimulated demand for new borrowing.

Alternative Hypothesis. The authors argue instead that households have inelastic, exogenous liquidity needs (for consumption smoothing, housing repairs, health shocks, etc.) and satisfy those needs using whichever borrowing product is cheapest given the rate environment. When mortgage rates fall below a borrower’s outstanding rate, cash-out refinancing becomes the least-cost vehicle, so borrowers shift from credit cards, HELOCs, personal loans, and second liens (closed-end seconds) toward cash-out refinancing—substituting borrowing products rather than expanding total borrowing.

Data. The authors use the Equifax Credit Risk Insight Servicing McDash (CRISM) dataset, which anonymously matches credit bureau records to mortgage servicing data (McDash). The main sample is a 16.5% draw of fixed-rate, first-lien mortgage loans observed at monthly frequency during 2013, yielding approximately 35 million loan-month observations. For the long time-series analysis, the full 2006–2021 sample is used. Borrowing events are identified across five credit instruments: cash-out refinance, HELOC, closed-end second (CES), credit card, and personal loan, each requiring at least $5,000 in new credit.

Identification Strategy. The paper uses two complementary approaches to address the endogeneity of mortgage rates and borrower refinance incentives.

Taper Tantrum quasi-experiment (main): In late spring 2013, two FOMC communication events triggered an approximately 80 basis-point increase in the 30-year fixed mortgage rate over the course of one month. Critically, because the shock arose from changes in long-term rate expectations (LSAPs), short-term rates—and thus HELOC and consumer credit rates—were largely unchanged. The authors exploit cross-sectional variation in pre-Taper “rate gaps” (outstanding mortgage rate minus estimated current market rate) using a difference-in-differences design (equation 6) to compare how cash-out and alternative borrowing change after the shock for borrowers with different pre-existing refinance incentives.
Monetary policy surprise IV (2006–2021): Following Berger et al. (2021), the authors instrument for the aggregate share of borrowers with rate gaps between 0 and 2 percentage points using the Bu, Rogers and Wu (2021) (BRW) unified measure of Fed monetary policy shocks, which spans both conventional and unconventional policy. This approach tests whether substitution persists when both long and short rates move together.

Main Findings.

Extensive margin (probability of borrowing): After the Taper Tantrum, the monthly probability of cash-out refinancing declines for all rate gap bins, most strongly for borrowers pushed out of the money by the rate increase (a roughly 0.0012 percentage-point monthly probability decline—more than 85 percent below baseline—for borrowers with pre-Taper rate gaps of approximately 1 percent). Simultaneously, the probability of other borrowing (HELOCs, credit cards, personal loans, CES) rises in a near-mirror image, especially for borrowers at intermediate rate gaps. The combined effect on total borrowing probability is negligible and shows little variation with rate gap.
Intensive margin (amount borrowed conditional on borrowing): Conditional on a cash-out refinance occurring after the Taper, the average extraction amount increases, consistent with a borrower-selection effect: low-liquidity-need borrowers, who face the highest effective borrowing cost increase when they move out of the money, disproportionately exit cash-out refinancing, leaving behind a pool of high-liquidity-need borrowers. For borrowers with pre-Taper rate gaps of around 1 percent, the conditional cash-out amount rises about 20 percent after the Taper.
Aggregate borrowing elasticity: Combining extensive and intensive margin estimates via a hurdle model, a 1 percentage-point increase in mortgage rates reduces total new household borrowing by between 0 and 8 percent (the aggregate borrowing elasticity is not statistically significantly different from zero at the preferred estimate, with a lower-bound of −8 percent), compared with a cash-out probability elasticity of approximately −45 percent in absolute terms.
Debt paydown: About 10–12 percent of new mortgage debt from cash-out refinances is used to pay down other outstanding debt, and this share is constant across rate gap groups and is not affected by the Taper, implying the MPC from cash-out borrowing does not vary with the rate environment.
Conventional monetary policy: Using the BRW IV over 2006–2021, the IV first stage yields an F-statistic of approximately 11. The cash-out extensive margin responds positively to the in-the-money share (elasticity 3.5 in IV), while other borrowing responds negatively (elasticity −0.87 in IV), and the all-borrowing elasticity is 0.09 and statistically insignificant. The intensive margin results are directionally consistent: conditional cash-out amounts fall as more borrowers are in the money, while total borrowing amounts respond positively (but insignificantly). Substitution thus holds even when both long and short rates move together.

Implications for Path Dependence. Because out-of-the-money borrowers substitute toward non-cash-out products, the non-linear dependence of cash-out refinancing on the distribution of outstanding mortgage rates does not translate into a correspondingly path-dependent total borrowing response. A back-of-the-envelope calculation using standard MPC assumptions (100 percent for cash-out, 80 percent for rate-term savings) and empirical refinancing frequencies and amounts (average first-lien equity extraction of $40,000 vs. average annual payment savings of $3,000 from rate-term refinancing, with rate-term frequency about 1.5x higher and semi-elasticity about 2x larger) implies that the potential near-term consumption stimulus from cash-out refinancing is approximately 5.5 times larger than from rate-term refinancing—making cash-out the dominant channel in principle. But because debt substitution substantially offsets the interest-rate sensitivity of cash-out refinancing, and because the path dependence of cash-out refinancing is largely eliminated by borrower substitution, the paper concludes that the overall path dependence of monetary policy is weaker than suggested by Berger et al. (2021) and Eichenbaum, Rebelo and Wong (2022).

In depth

Q1. What is the “rate gap” and why does it capture the cash-out refinance incentive?

The rate gap is defined as a borrower’s outstanding fixed mortgage rate minus an estimate of the 30-year fixed mortgage rate currently available to that borrower if they were to refinance (estimated from a regression of origination-period rates on LTV, credit score, loan type, investor type, and month fixed effects). A positive rate gap means the borrower is “in the money” for a rate-term refinance: they can reset their existing mortgage at a lower rate. The rate gap captures the degree of refinance incentive because resets the interest cost on the entire outstanding balance. Cash-out refinancing is especially attractive when the rate gap is positive because the rate reduction on the existing balance partially subsidizes the new borrowing, lowering its effective cost relative to alternative products.

Q2. What is the conceptual model of debt substitution the authors propose?

The authors model a homeowner with an inelastic liquidity need l that arrives with probability λ. The borrower can satisfy this need through a cash-out refinance at mortgage rate r_m (resetting their entire mortgage at r_m, which implies an interest cost on the existing balance) or through an alternative product at rate r_a > r_m. The key trade-off is that a cash-out refinance saves on the rate for the liquidity need itself but incurs a cost or benefit depending on whether r_m exceeds or falls below the outstanding rate r_0. When the rate gap is negative (r_0 < r_m), the cash-out refinance penalizes the borrower on the existing balance; when the gap is positive (r_0 > r_m), it saves on the existing balance, further lowering the effective cost of the liquidity need. The model predicts that: (i) the probability of cash-out refinancing is nonlinear and step-like in the rate gap; (ii) the probability of alternative borrowing has the opposite pattern; (iii) higher mortgage rates raise the conditional cash-out amount through selection (low-l borrowers exit cash-out); and (iv) total borrowing is relatively insensitive to mortgage rates.

Q3. How does the Taper Tantrum provide exogenous variation, and what are its limitations?

The Taper Tantrum began in late spring 2013 when two FOMC communication events—Chairman Bernanke’s congressional testimony and the subsequent FOMC meeting—shifted market expectations about the pace of tapering large-scale asset purchases (LSAPs). The 30-year fixed mortgage rate rose approximately 80 basis points within one month, driven by changes in long-term rate expectations. Because the shock was unanticipated and FOMC did not announce any concrete policy change, the scope for a “Fed information effect” biasing results is limited. The critical limitation is that the Taper Tantrum affected primarily long-term rates: HELOC rates and consumer credit rates (tied to the federal funds rate and bank prime rate, which were unchanged) were little affected. This means the estimated substitution elasticity holds when the rate spread between mortgage and alternative products widens, which is more directly applicable to unconventional monetary policy (LSAPs) than to conventional policy that moves rates across the full yield curve.

Q4. What do the Taper Tantrum extensive margin results show, and what pattern confirms substitution?

Figure 4 plots the difference-in-differences coefficient β₂ + β₃ by pre-Taper rate gap bin for three outcome variables. The cash-out refinancing probability (blue line) declines for all rate gap bins, most sharply for intermediate rate gap values (borrowers pushed out of the money by the Taper). Borrowers with pre-Taper rate gaps of ~1 percent experience a decline in monthly refinancing probability of about 0.0012, or more than 85 percent below their baseline rate. Other borrowing (black line) shows an almost exact mirror-image pattern: it rises after the Taper, most strongly for the same intermediate rate gap borrowers. The total borrowing probability (red line) shows essentially no response and little variation across rate gap groups, implying substitution nearly completely offsets the cash-out decline.

Q5. How do the intensive margin results for cash-out refinancing compare to the extensive margin, and what explains the difference?

After the Taper, the conditional cash-out amount rises (the intensive margin effect is positive), while the cash-out probability falls (the extensive margin effect is negative). These opposite signs are consistent with borrower selection: borrowers with small liquidity needs face the steepest increase in effective borrowing cost when they move out of the money and so disproportionately exit cash-out refinancing, raising the average extraction amount among those who remain. For borrowers with pre-Taper rate gaps of ~1 percent, the conditional cash-out amount rises approximately 20 percent after the Taper. Figure 6 corroborates this by showing the increase in average extraction is driven by a sharp decline in small extraction amounts (relative to outstanding balance).

Q6. How is the aggregate borrowing elasticity computed and what does it imply about monetary policy transmission?

The authors combine extensive and intensive margin estimates using a two-tiered (hurdle) model that allows the decision to borrow and the decision of how much to borrow to respond differently to covariates. The total expected borrowing amount is the product of the estimated borrowing probability and the expected conditional borrowing amount. Pre- and post-Taper aggregate predicted borrowing is calculated for each rate gap group, and the percentage change is divided by the 80 basis-point rate increase to produce a semi-elasticity. The aggregate borrowing elasticity is not statistically significantly different from zero at the main estimate, and the lower-bound estimate (which avoids reliance on the Post dummy for aggregate borrowing) is at most −8 percent per percentage-point increase in rates. This compares with a cash-out probability elasticity of approximately −45 percent, illustrating that substitution accounts for the overwhelming majority of the observed cash-out response.

Q7. Why is the BRW monetary policy shock IV important for generalizing the Taper Tantrum findings?

The Taper Tantrum moved only long rates, whereas conventional monetary policy moves both long and short rates. When short rates rise, the alternative borrowing products (HELOCs, credit cards, personal loans) become more expensive, which could dampen substitution in two ways: (a) the rate spread between mortgage and alternative products narrows, reducing the range of borrower-amount combinations for which substitution makes financial sense; and (b) higher absolute borrowing costs on alternative products may reduce total borrowing among borrowers who would otherwise substitute. The BRW IV, which spans 2006–2021 and reflects shocks to the full yield curve (conventional and unconventional), addresses whether substitution holds when both rate types move. The IV results in Table II (F-statistic ~11) confirm that the cash-out probability elasticity is 3.5 (IV), the other-borrowing elasticity is −0.87 (IV), and the all-borrowing elasticity is 0.09 and statistically insignificant, broadly consistent with the Taper Tantrum findings.

An event study finds that total household debt increases by about 88 percent of the increase in mortgage balance in the first two months after a cash-out refinance, implying approximately 12 percent debt paydown; by six months out, the net paydown stabilizes at around 8 percent. Crucially, this share is constant across rate gap groups and does not change after the Taper Tantrum. This constancy implies that the marginal propensity to consume (MPC) out of cash-out refinances does not vary with the rate environment, and therefore the path-dependence of the cash-out channel cannot be attributed to compositional changes in how borrowers use extracted funds.

Q9. Why does the paper argue cash-out refinancing has far greater near-term consumption potential than rate-term refinancing, and what are the implications for path dependence?

A back-of-the-envelope calculation uses: (1) empirical frequencies (rate-term refinance probability is ~1.5x higher than cash-out); (2) near-term liquidity per event (average first-lien cash-out extraction ~$40,000 vs. annual payment savings ~$3,000 from rate-term); (3) semi-elasticities (rate-term has ~2x higher semi-elasticity to rates than cash-out per the IV estimates); and (4) standard MPC assumptions (100% for cash-out, 80% for rate-term savings). The calculation implies the consumption stimulus potential from cash-out refinancing is approximately 5.5 times that of rate-term refinancing per percentage-point change in rates. Because the paper shows the path-dependence of cash-out refinancing is largely offset by substitution, and because cash-out is the dominant near-term channel, the overall path-dependence of monetary policy is weaker than prior models predict.

Q10. What are the key robustness checks and how do they address potential confounds?

Three main robustness exercises are reported. First, a QE1 robustness (Appendix) uses the large decline in mortgage rates after the first LSAP announcement in 2008 as an alternative shock, finding consistent substitution patterns (households shift into cash-out refinancing from other borrowing when pushed into the money). Second, a placebo test shifts the sample back six months and estimates the same specification over the twelve months preceding the Taper; Figure 8 shows no differential substitution by rate gap during this stable-rate period, supporting the interpretation that the Taper Tantrum rate increase drives the cross-sectional substitution pattern. The placebo does reveal a negative Post dummy for other borrowing, consistent with a possible pre-trend in other borrowing, which motivates the lower-bound elasticity calculation that avoids reliance on this coefficient. Third, the authors show that results are little changed when adjustable-rate mortgages (~10 percent of outstanding mortgages in 2013) are included in the sample.

Key Concepts

Rate Gap: The difference between a borrower’s outstanding fixed mortgage rate and the estimated current 30-year fixed mortgage rate available to that borrower if they were to refinance (adjusting for borrower-specific LTV and credit score). A positive rate gap means the borrower is “in the money” for a rate-term refinance. This is the paper’s central measure of refinance incentive, determining whether cash-out refinancing or an alternative borrowing product is the cost-minimizing option for satisfying a given liquidity need.

Debt Substitution: The paper’s core mechanism: households shift their new borrowing across products (cash-out refinance, HELOC, CES, credit card, personal loan) in response to changes in relative borrowing costs, without proportionally changing total new borrowing. When the rate gap is positive, cash-out refinancing is the cheapest way to borrow (it lowers the rate on the existing balance while providing liquidity), so borrowers substitute from alternative products into cash-out. When the rate gap is negative or mortgage rates rise, borrowers substitute in the opposite direction, keeping their original mortgage rate intact by using alternative products.

Cash-Out Refinance Channel of Monetary Policy: The theoretical transmission mechanism by which monetary easing lowers mortgage rates, incentivizes in-the-money borrowers to refinance and extract home equity at reduced cost, and thereby stimulates consumption. Prior literature (Eichenbaum, Rebelo and Wong 2022) treats this channel as path-dependent and quantitatively important because it depends on the distribution of outstanding mortgage rates.

Path Dependence of Monetary Policy: The property by which the same monetary policy shock generates different aggregate borrowing or consumption responses depending on the historical distribution of outstanding fixed mortgage rates, which reflects prior monetary policy. A large share of in-the-money borrowers (due to a prior rate-cutting cycle) amplifies the cash-out refinance channel; a large share of out-of-the-money borrowers weakens it. The paper shows this path dependence is substantially attenuated by debt substitution.

In-the-Money Borrower: A borrower whose outstanding mortgage rate exceeds the current market mortgage rate (positive rate gap), creating a financial incentive to refinance. In-the-money status interacts with borrowing product choice because a cash-out refinance resets the interest cost on the entire existing balance, generating implicit savings that partially subsidize new liquidity extraction.

Hurdle (Two-Tiered) Model: An estimation approach that allows the decision to borrow (extensive margin) and the amount borrowed conditional on borrowing (intensive margin) to respond differently to covariates. The authors use this model to combine extensive and intensive margin estimates into a single aggregate borrowing elasticity, avoiding the distortion that arises from using dollar volume as a dependent variable when intensive and extensive margins have opposite responses to the rate gap.

Taper Tantrum (2013): A quasi-experimental shock used as the paper’s main source of exogenous variation. In late spring 2013, Federal Reserve communications about tapering large-scale asset purchases (LSAPs) caused the 30-year fixed mortgage rate to increase approximately 80 basis points within one month. Because the shock operated through long-term rate expectations, it moved mortgage rates without significantly affecting HELOC or consumer credit rates (tied to the unchanged federal funds and bank prime rates), enabling the authors to estimate substitution holding alternative product rates approximately fixed.

Community Engagement and Public Safety: Evidence from Crime Enforcement Targeting Immigrants

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

This paper studies how immigration enforcement affects public safety, asking two questions: (1) what is the effect of increased enforcement on criminal victimization, and (2) how does increased enforcement affect victims’ willingness to report crimes to police? The authors exploit the staggered rollout of the U.S. Secure Communities (SC) program — the largest expansion of interior immigration enforcement in U.S. history — across counties between 2008 and 2013. SC expanded information sharing between local police and federal immigration authorities, causing ICE honored detainer requests to increase by over 50% following program activation.

The primary data source is the restricted-access National Crime Victimization Survey (NCVS), which measures victimizations independently of whether they were reported to police and includes respondent ethnicity. This allows the authors to separately estimate effects on underlying crime incidence and on reporting behavior for Hispanic and non-Hispanic individuals. The empirical strategy uses a staggered difference-in-differences design following Sun and Abraham (2021), comparing earlier-treated counties to the last 25% of counties to activate SC, with estimates run separately by ethnicity.

The main findings run contrary to the stated policy goal of improving public safety. Among Hispanic individuals, SC caused a statistically significant 0.15 percentage point increase in monthly victimization — a 16% increase relative to the pre-period baseline of 0.9 percentage points — implying approximately 1.3 million additional crimes against Hispanics in the two years following program activation. The increase is concentrated primarily in property crimes (a statistically significant 15% increase), with a similarly sized but imprecisely estimated 15% increase in violent crime victimizations. The victimization increase is larger for Hispanic females (0.23 percentage points, or 25%) and in counties with higher shares of non-citizen Hispanic residents.

Simultaneously, SC caused a 9.5 percentage point decline in the likelihood that Hispanic victims report incidents to police — a 30% decline relative to the pre-period mean reporting rate of 33 percentage points. This reporting decline is primarily driven by a 34% decline in the reporting of property offenses. No changes in victimization or reporting are found for non-Hispanic individuals in the aggregate, though non-Hispanic individuals in neighborhoods with high Hispanic population shares do experience higher victimization rates after SC.

Critically, reported crime rates (the product of victimization and reporting) are unchanged for both Hispanic and non-Hispanic individuals, explaining why prior studies using administrative reported-crime data found null effects of SC. The null effect on reported crime masks two large, opposing causal forces.

The authors provide evidence that the decline in crime reporting is the primary driver of the increase in victimization. Cohorts with larger reporting declines experienced larger victimization increases, and a decomposition exercise shows the reporting decline is substantially more important than concurrent SC-induced changes in unemployment, wages, female-headed household shares, and the male immigrant share. Supporting data from 75 police departments confirm no change in 911 call volumes or total arrest volumes, while showing a decline in the Hispanic share of arrestees in both Hispanic and non-Hispanic neighborhoods — consistent with reduced reporting leading to reduced apprehension of offenders, with offending shifting toward non-Hispanic individuals.

Scope conditions: results are estimated for the population residing in counties exceeding 100,000 residents (representing 61% of total U.S. population and 69% of the Hispanic population), excluding southern border counties and states that actively resisted SC implementation (Illinois, Massachusetts, New York). Effects apply to all Hispanic respondents — citizens and non-citizens — consistent with prior evidence that citizen Hispanics respond to immigration enforcement out of concern for non-citizen contacts.

Q: What was the Secure Communities program and how was it implemented? A: SC was a federal program launched in 2008 that required fingerprints of individuals booked into local jails to be forwarded not only to the FBI but also to the Department of Homeland Security, enabling automatic screening for immigration violations. Local authorities could not prevent federal officials from learning of an arrestee’s immigration status. The program rolled out county-by-county between October 2008 and January 2013 due to technological constraints and resource bottlenecks, generating the staggered variation used for identification.

Q: How large was the first-stage effect on actual immigration enforcement? A: County-level honored ICE detainer requests increased by over 50% following SC activation, with a similar 40% increase in all detainer requests. The number of honored detainers nationwide doubled between 2008 and 2012. Over 90% of detainers and removals in any given month were for individuals of Hispanic ethnicity.

Q: What is the main finding on Hispanic victimization? A: SC caused a 0.15 percentage point increase in monthly Hispanic victimization rates, a 16% increase relative to the pre-period baseline of 0.9 percentage points. This translates to approximately 1.3 million additional crimes against Hispanics over two years following program activation, calculated by multiplying the monthly effect by 24 months and the 35.3 million Hispanics in the sample counties.

Q: What is the main finding on Hispanic crime reporting? A: SC caused a 9.5 percentage point decline in the likelihood that Hispanic victims report incidents to police, a 30% decline relative to the pre-period mean reporting rate of 33 percentage points. This decline occurred relatively quickly after activation and was concentrated in property offenses, where reporting fell by 34%.

Q: Why do reported crime rates show no change despite large shifts in victimization and reporting? A: Reported crime rates — the probability of being victimized and reporting the crime — are unchanged because the 16% increase in victimization and the 30% decline in reporting are approximately offsetting in magnitude. This explains why prior work using administrative police data (Miles and Cox 2014; Treyger et al. 2014; Hines and Peri 2019) found null effects of SC on reported crime: those data sources cannot separately identify the two underlying changes.

Q: Does SC affect non-Hispanic individuals? A: In the aggregate, SC has no statistically significant effect on non-Hispanic victimization or reporting. However, non-Hispanic individuals living in neighborhoods with high Hispanic population shares do experience victimization increases, and in those neighborhoods their reporting rates also decline slightly. Re-weighting non-Hispanic respondents to match the county composition of Hispanic respondents yields an 8% increase in non-Hispanic victimization, suggesting spillover effects in Hispanic-dense areas.

Q: What mechanism links the reporting decline to the victimization increase? A: The authors argue that reduced victim reporting lowers the probability that offenders are apprehended, thereby reducing the cost of committing crimes. They demonstrate this through two analyses: first, cohorts of counties with larger reporting declines experienced larger victimization increases; second, a decomposition shows the reporting channel is substantially more important than concurrent SC-induced changes in unemployment, wages, female-headed household shares, and the male immigrant share of the population.

Q: What do the police administrative data show about offender composition? A: Data from 75 police departments show no change in 911 call volumes or total arrest volumes following SC — consistent with the NCVS finding of unchanged reported crime rates. However, the Hispanic share of arrestees declined after SC, with a 1.5 percentage point drop in Hispanic neighborhoods (off a base of 54%), suggesting the rise in offending was more concentrated among non-Hispanic offenders as reduced reporting lowered expected punishment probabilities.

Q: How does the victimization effect vary by gender? A: The victimization point estimate for Hispanic males is 0.085 percentage points and imprecisely estimated (SE = 0.088). For Hispanic females, the effect is over 2.5 times larger at 0.23 percentage points, a 25% increase. The decline in reporting is comparable in magnitude across male and female Hispanic victims, suggesting fear of enforcement is similar by gender but that females disproportionately bear the crime burden.

Q: How does the victimization effect vary by neighborhood non-citizen Hispanic share? A: Victimization effects for Hispanics are relatively constant across neighborhood types but are higher — around 25% — in neighborhoods with the highest shares of non-citizen Hispanics. Counties with higher non-citizen Hispanic shares also exhibit higher ICE removal rates, indicating greater total enforcement, and these counties have higher victimization effects. Reporting declines among Hispanics appear relatively uniform across neighborhood types.

Q: Could survey attrition or compositional changes explain the results? A: The authors rule this out through several tests. First, SC has no statistically significant effect on household survey response rates, even in Census tracts above the 90th percentile of Hispanic share. A worst-case bias calculation implies attrition could account for at most 26% of the victimization effect. Second, re-estimating using predicted victimization (based on pre-SC demographics) yields precise null effects, indicating the increase is not driven by compositional change. Third, results are stable when restricting to respondents present at all survey waves or using individual fixed effects.

Q: Could the reporting decline be mechanical — reflecting a change in the types of crimes committed rather than behavioral change? A: The authors test this by constructing predicted reporting rates using pre-SC incident characteristics. The largest alternative estimate is -1.45 percentage points, over six times smaller than the estimated main reporting effect of 9.5 percentage points, ruling out crime composition change as the primary explanation. Results also hold when focusing on always-respondents and using individual fixed effects, ruling out entry of low-reporting individuals into the survey.

Q: How robust are the results to alternative empirical strategies? A: Results are robust to including states that resisted SC (with somewhat smaller magnitudes as expected), alternative population cutoffs, TWFE specifications, the Borusyak et al. (2021) and Callaway and Sant’Anna (2021) estimators (which yield larger point estimates), a triple-differences specification using non-Hispanics as an additional control group, and the inclusion of time-varying unemployment rates. The dynamic event-study plots show parallel pre-trends across all specifications.

Q: What are the policy implications of the null effect on aggregate victimization? A: The authors estimate that the policy ruled out declines in aggregate victimization larger than 3.3%, indicating SC did not generate meaningful improvements in aggregate public safety. This contradicts the stated mission of immigration enforcement agencies. The findings imply that policies targeting immigrant communities can generate public safety costs through trust erosion that outweigh any deterrence or incapacitation benefits.

Secure Communities (SC): A federal program launched in 2008 requiring automatic sharing of fingerprints from local jail bookings with the Department of Homeland Security, enabling identification of unauthorized immigrants among local arrestees and triggering ICE detainer requests; the largest expansion of interior immigration enforcement in U.S. history.

Chilling effect: The mechanism by which immigration enforcement raises the perceived cost of contacting law enforcement for immigrant victims and witnesses — through fear that they, a family member, or neighbor will be detained or deported — thereby reducing willingness to report crimes independently of any change in underlying criminality.

Victimization rate: The likelihood that an individual is the victim of a crime in a given period, measured via the NCVS independently of whether the crime was reported to police; the paper’s primary measure of public safety.

Reporting rate: The likelihood that a criminal victimization is reported by the victim to the police, measured as a share of all crime incidents; distinct from victimization rate and central to the paper’s decomposition of reported crime into its two components.

Reported crime rate: The joint probability of being victimized and reporting the crime, analogous to measures available in administrative police data such as the FBI UCR; this outcome masks the opposing effects of SC on victimization and reporting.

Honored detainer: An ICE detainer request that results in a transfer of the arrested individual to ICE custody; the paper’s preferred measure of immigration enforcement intensity because it is available both before and after SC activation and is more directly linked to deportation actions than all detainer requests.

Decomposition of victimization increase: The paper’s procedure for quantifying the relative importance of the reporting-channel (reduced probability of apprehension) versus other SC-induced social and economic changes (unemployment, wages, female-headed households, male immigrant share) in explaining the rise in Hispanic victimization.

Consistent Evidence on Duration Dependence of Price Changes

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

Layer 1 — Overview

Research Question. This paper asks two related questions. First, can one develop a robust, distribution-free estimator for the discrete-time mixed proportional hazard (MPH) model of duration with unobserved heterogeneity? Second, what does that estimator reveal about the shape of the hazard of price changes, the role of heterogeneity in shaping aggregate price dynamics, and the distinction between regular price changes and sales?

Methodology. The authors develop a linear generalized method of moments (GMM) estimator for the discrete-time MPH model, building on identification results in Honoré (1993). The model specifies that the probability a price spell ends at duration t, conditional on surviving to t, equals the product of a product-specific frailty parameter θ (unobserved, fixed over time) and a common baseline hazard bt. The estimator exploits repeated price spells per product via moment conditions that are linear in bt, making estimation and inference straightforward. It accommodates right- and left-censored data, competing risks, and spell-specific observable characteristics, without requiring any parametric assumption on the frailty distribution. The estimator is consistent as the number of products grows, even with a short time dimension. A Hansen-Sargan J-test of overidentifying restrictions and a test of the monotone-average-type prediction are also developed.

The estimator is applied to two datasets: (1) IRI weekly store data (2001–2011), covering 30 product categories and more than 21 million products, yielding 684,919,778 pairs of durations; and (2) Online Micro Price data from Cavallo (2018), comprising approximately 250,000 products at daily frequency.

Main Findings with Quantitative Magnitudes.

Baseline hazard and heterogeneity. In the pooled IRI data, the Kaplan-Meier hazard is steeply declining throughout the entire range from 2 to 60 weeks. In contrast, the estimated baseline hazard is roughly constant until week 4 and then declines only modestly, with a noticeable spike at week 52. The ratio of the Kaplan-Meier hazard to the baseline hazard — the average type, E[θ|t] — drops by approximately 60 percent within the first 20 weeks, and continues to decline, reaching roughly 0.3 of its initial value after one year. This decomposition reveals substantial unobserved heterogeneity that accounts for a large fraction of the observed decline in the Kaplan-Meier hazard.

Implications for structural models. The finding of a decreasing baseline hazard is inconsistent with canonical state-dependent pricing models (Golosov and Lucas, 2007), which predict an increasing hazard, conditional on a given firm’s type. The decreasing baseline hazard is instead broadly consistent with time-dependent pricing models, though not with a constant-hazard (Calvo, 1983) specification.

Monetary policy impulse response. In a calibrated time-dependent pricing model with strategic complementarity (α = 0, 0.5, 0.95), the aggregate price level dynamics in the estimated heterogeneous-firm MPH economy are close to those of a homogeneous-firm economy that uses the Kaplan-Meier hazard as the common price-change hazard. The homogeneous-firm approximation is substantially closer to the MPH economy than a Taylor (1979, 1980) staggered-contract economy with the same Kaplan-Meier hazard, particularly when strategic complementarity is strong (α = 0.95). The Calvo economy provides a poor approximation due to its exponential (constant-speed) price convergence structure.

Regular versus temporary price changes. Using the competing-risks extension with spell-specific observables — classifying spells by whether they start and end with a price increase (+) or decrease (−) — the authors separately estimate four baseline hazards. The baseline hazard for consecutive price increases (b++t) is relatively flat, especially for the first 6 weeks, then flat until week 45, with a spike near one year, consistent with price-plan models. The baseline hazard for reversals (particularly b−+t, price decreases followed by price increases, associated with sales) is steeply declining. The J-test statistics are substantially lower for price trends (J++ = 3,920; J−− = 3,401) than for reversals (J+− = 8,737; J−+ = 7,910), and markedly lower than the pooled-model J = 10,498, indicating that the MPH structure fits regular price changes considerably better than sales.

Scope Conditions. Results are conditional on weekly store-level price data for mostly packaged consumer goods (30 IRI product categories). The analysis focuses on price spells of at least 2 weeks to avoid spurious duration-one spells from mid-week price changes. The maximum duration examined is 60 weeks. The comparison of estimation methods relies on the IRI data only; the Online Micro Price data confirm weekly decision-making through a spike in the daily hazard every 7 days. Comparisons with maximum likelihood estimates show that GMM recovers more heterogeneity (average type declines to 0.37 at 6 months by GMM versus 0.48 by continuous-time MLE), and that time aggregation explains most of the discrepancy between the two methods.

In depth

Q1. What is the mixed proportional hazard (MPH) model as used in this paper, and what does the estimator identify?

A1. The MPH model specifies that the hazard that a price spell ends at duration t, conditional on surviving to t, equals θ·bt, where θ is a product-specific frailty parameter drawn from an unknown distribution G and bt is a baseline hazard common to all products. The estimator, which is linear in bt, identifies the baseline hazard up to a multiplicative constant using moment conditions derived from repeated spell data, without restricting the shape of the frailty distribution. Identification relies on comparing the joint survival probabilities of two consecutive spells for the same product and exploits the symmetry implied by the MPH structure across spells.

Q2. How does the Kaplan-Meier hazard relate to the baseline hazard, and what does this relationship imply about heterogeneity?

A2. The paper proves that the Kaplan-Meier hazard Ht equals bt times E[θ|t], the mean frailty among spells surviving to duration t. Because higher-type products (those with a higher propensity to change prices) exit the pool of surviving spells earlier, E[θ|t] is strictly decreasing in t — a form of dynamic selection. The ratio Ht/bt, normalized to 1 at the start, falls to approximately 0.4 by week 20 in the pooled IRI data and to approximately 0.3 after one year, documenting that a large share of the decline in the Kaplan-Meier hazard reflects heterogeneity rather than structural negative duration dependence.

Q3. What does the estimated baseline hazard imply about structural models of price setting?

A3. A decreasing baseline hazard is inconsistent with the canonical state-dependent model of Golosov and Lucas (2007), in which a firm’s hazard of price change is increasing in the time since the last change, because larger deviations from the desired price accumulate with duration. The decreasing baseline hazard is instead consistent with time-dependent pricing models and with price-plan models where within-plan switches are costless. The mild spike at week 52 in the baseline hazard is consistent with Taylor-type annual pricing rules.

Q4. What is the approximate aggregation result for monetary policy, and how quantitatively accurate is it?

A4. In the time-dependent pricing model without strategic complementarity (α = 0), the impulse response of the aggregate price level to a monetary shock in a heterogeneous-firm economy is exactly the same as in a homogeneous-firm economy whose single firm uses the Kaplan-Meier survival function. This extends Carvalho and Schwartzman (2015) to an approximation in the case with strategic complementarity (α = 0.5 and α = 0.95). Numerically, the path of aggregate prices in the estimated MPH economy is close to that in the homogeneous-firm Kaplan-Meier economy, and substantially closer to it than to the Taylor-contract economy — the difference is most pronounced at horizons beyond about half a year when α = 0.95, where the Taylor economy shows notably slower initial convergence and faster later convergence relative to the MPH and homogeneous economies.

Q5. How do the paper’s results differ from those obtained using maximum likelihood estimation of the continuous-time MPH model?

A5. The GMM estimator recovers substantially more heterogeneity than maximum likelihood (MLE) applied to the continuous-time model with continuous records (assumed gamma frailty). The average type falls from 1 to 0.37 at six months under GMM, versus only 0.48 under MLE. The authors investigate two sources of this discrepancy: the assumed frailty distribution family (gamma) and time aggregation. They conclude that time aggregation is quantitatively more important in the IRI weekly data — that is, the continuous-time MLE approach fails to properly account for the discrete nature of the data-generating process, leading it to understate heterogeneity and recover a steeper baseline hazard.

Q6. How does the paper distinguish regular price changes from sales without directly observing a sales flag?

A6. The competing-risks extension classifies each spell by whether it starts with a price increase or decrease (observable characteristic χ ∈ {+, −}) and by whether it ends with a price increase or decrease (competing risk ρ ∈ {+, −}). Price trends — spells where the direction is the same at both the start and end (++ or −−) — are interpreted as regular price changes; price reversals (especially −+, i.e., price decrease followed by increase) are associated with sales. This approach is consistent with the statistical model used for estimation, avoids the bias from simply dropping suspected sales spells before estimation, and allows the MPH structure to hold only for the risks of interest even if it fails for others.

Q7. How well does the MPH model fit regular price changes versus sales?

A7. The J-test of overidentifying restrictions yields test statistics of J++ = 3,920 for consecutive price increases and J−− = 3,401 for consecutive price decreases, compared with J = 10,498 for the pooled model and J+− = 8,737 and J−+ = 7,910 for the reversal hazards. All rejections are at conventional significance levels (critical value 1,749 at 5%), but the rejection is substantially milder for price trends than for price reversals. For individual product categories, the model cannot be rejected for 8 categories (out of 30) for b++ and 21 categories for b−−, suggesting the MPH structure is a much better description of regular price changes than of sales.

Q8. What role do one-week price spells play in the data, and why are they excluded?

A8. In the IRI data, prices are measured as the ratio of weekly revenue to quantity, so a price change occurring mid-week generates a spurious price spell of duration one week. If all spells including one-week spells are retained, the autocorrelation of spell durations is only 0.029 in levels and even negative (−0.042) in logs, which is inconsistent with a mixture model. Once one-week spells are excluded, the autocorrelation rises to 0.235 in levels and 0.233 in logs, and is stable when two-week spells are also excluded (0.248 and 0.256). The paper therefore sets the lower duration bound at T̲ = 2 weeks.

Q9. What does the daily Online Micro Price data add relative to the weekly IRI data?

A9. The daily data reveal a sharp spike in the price-change hazard every seven days, suggesting that even when prices are observed daily, the decision to change prices is made at the weekly frequency. This justifies the use of a discrete-time model with a one-week period. The estimates from daily and weekly aggregations of the same data are broadly similar, though weekly data recovers somewhat less heterogeneity than daily data. Aggregating IRI weekly data to monthly frequency understates heterogeneity even more, confirming that frequency matters for measuring heterogeneity.

Q10. What are the computational advantages of the GMM estimator relative to maximum likelihood?

A10. Because the moment conditions are linear in the baseline hazard bt, the GMM estimator is obtained in closed form, making estimation fast and inference straightforward. On the pooled IRI sample, GMM estimation (including standard errors) required 70 minutes on a machine with 60 GB memory, whereas the maximum likelihood estimator required 15 hours on a machine with 256 GB memory and failed entirely on the 60 GB machine. The GMM approach also avoids the need to specify the frailty distribution family and guarantees a global solution (proved by the identification result), whereas the likelihood function is non-linear in bt and may have multiple local maxima.

Q11. What is the shape of the b++ baseline hazard for regular price increases, and what models does it support?

A11. The baseline hazard for spells starting and ending with a price increase (b++) is decreasing during the first 6 weeks — dropping by almost 50% — and then flat until approximately week 45, with a pronounced spike at around one year. This shape is consistent with price-plan models (Eichenbaum, Jaimovich, and Rebelo, 2011) with Calvo-type switching between plans, where within-plan changes are costless and the hazard of between-plan switching is approximately constant. The annual spike is consistent with Taylor-type pricing. Approximately 76.8% of complete spells starting after a price increase last at most 6 weeks.

Key Concepts

Baseline hazard (bt). The component of the MPH hazard that is common to all products and may vary arbitrarily with elapsed duration t. It represents structural duration dependence — the tendency for a given product to be more or less likely to change price as a function of how long its current spell has lasted — net of heterogeneity. It is identified only up to a multiplicative constant.

Frailty parameter (θ) / frailty distribution (G). The product-specific scaling factor in the MPH model, fixed over all spells for a given product, that captures permanent unobserved differences in price-change frequency across products. The paper treats G as a nuisance parameter and does not require a parametric assumption on its shape. A higher θ means the product has a higher baseline propensity to change its price.

Average type (E[θ|t]). The mean frailty parameter among spells that have survived to at least duration t. Because high-type products change price earlier and exit the pool of surviving spells first, the average type is provably strictly decreasing in t under the MPH model. It is measured as the ratio of the Kaplan-Meier hazard to the baseline hazard, and its rate of decline measures the importance of dynamic selection.

Kaplan-Meier hazard (Ht). The probability that a randomly drawn spell ends at duration t, conditional on having lasted at least t periods. It mixes together structural duration dependence (captured by bt) and dynamic selection (captured by changes in the average type). It can be estimated without imposing the MPH structure, requiring only stationarity of the duration process.

Competing risks. The framework in which a price spell can end for multiple distinct reasons — here, ending with a price increase or a price decrease — each with its own hazard function. The paper’s GMM approach allows the MPH structure to hold for only a subset of risks and observables, without imposing any structure on the remaining risks.

Price trends vs. price reversals. A classification of spells based on the direction of the surrounding price changes. Price trends are spells where the direction of the price change at the start and end of the spell is the same (++ or −−), interpreted as regular price changes. Price reversals are spells where the direction switches (e.g., −+, a price decrease followed by a price increase), associated with sales and other temporary price changes.

Strategic complementarity in pricing (α). The degree to which a firm’s target price responds to the average price set by other firms. Parameterized by α ∈ [0, 1), where α = 0 yields the exact aggregation result (only the Kaplan-Meier hazard matters) and higher α increases aggregate price stickiness by making firms reluctant to deviate from the average price when few others are adjusting.

Dynamic selection. The mechanism by which the composition of the pool of surviving price spells shifts toward lower-type (more price-sticky) products as duration increases, because higher-type products change price sooner and exit the pool. This is the source of the gap between the steeply declining Kaplan-Meier hazard and the more modestly declining baseline hazard.

Consumer Credit and the Incidence of Tariffs: Evidence from the Auto Industry

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

Overview

Research Question. Do import tariffs affect consumer credit terms, and does focusing solely on goods prices understate tariff pass-through to consumers? The paper also asks whether vertical integration – specifically, the ownership of a captive finance subsidiary – expands the channels through which manufacturers can pass on cost shocks, and whether tariff incidence falls disproportionately on consumers with less elastic credit demand or in areas with lower credit market competition.

Setting. The Trump administration’s 2018 metal tariffs – a 25 percent tariff on steel and a 10 percent tariff on aluminum – created a large and largely unanticipated cost shock for US auto manufacturers who are heavy consumers of both metals across their supply chains. Crucially, auto manufacturers own captive finance subsidiaries (e.g., Ford Credit, GM Financial, Honda Finance) that originate consumer auto loans alongside independent noncaptive lenders (banks, credit unions, independent finance companies). Because noncaptive lenders had no direct exposure to the metal tariffs, they serve as a natural control group in a difference-in-differences design.

Data. The primary data source is Regulation AB II, which requires issuers of public auto loan asset-backed securities to report loan-level information monthly to the SEC. The final sample covers 1,973,639 auto loans originated between January 2017 and December 2018 across 14 lenders (8 captive, 6 noncaptive). Vehicle invoice price data come from Regulation AB II; consumer sales price data come from the Texas Department of Motor Vehicles (covering approximately 3.9 million vehicle transactions in 2017-2018). Population credit bureau data from Equifax are used for representativeness checks and HHI construction.

Empirical Strategy. The baseline difference-in-differences compares captive auto loans to otherwise-identical noncaptive auto loans originated in the same state, the same quarter, for the same vehicle make-model-condition, and to borrowers in similar income and credit score bins. Parallel pre-trends tests confirm no economically meaningful differential pre-trends across captive and noncaptive lenders for any outcome variable.

Main Findings.

Interest Rate Pass-Through. Relative to noncaptive lenders, captive lenders increased average interest rates by 26 basis points following the tariff announcement, representing a 10 percent increase relative to the pretreatment captive mean of 252 basis points. This corresponds to an average present value increase in total loan payments of $179 per loan (discounted at 5 percent for an average $26,914 principal with 66-month maturity). By the fourth quarter of 2018, the dynamic estimate reaches 48 basis points – nearly double the pooled average – as metal prices continued to rise. The increase is concentrated among more-exposed captive lenders (those whose manufacturers operate two or more domestic production plants), not less-exposed captive lenders (primarily BMW, Mercedes-Benz, Volkswagen), ruling out captive-specific omitted variables.
Non-Price Loan Terms. There is no economically significant change in captive loan amounts, maturities, or loan-to-value ratios following the tariffs. Captive lenders responded to the tariff shock exclusively by raising interest rates, consistent with prior evidence that auto loan demand is less sensitive to interest rates than to non-price terms.
Vehicle Prices. Invoice prices for makes with greater domestic production rose by approximately 1.0 percent (relative to makes with less domestic production), and consumer sales prices rose by approximately 0.7 percent ($225 average increase relative to a pretreatment mean of $32,206) for these same makes.
Relative Magnitude of Pass-Through Channels. After accounting for estimated spillover effects on noncaptive lenders of 7 basis points, the spillover-adjusted estimate implies captive interest rates rose by 33 basis points on average, corresponding to $227 per loan in present value terms. Interest rate pass-through is estimated to be almost two-thirds as large as vehicle price pass-through, meaning that focusing solely on vehicle prices would underestimate tariff incidence on consumers by approximately 37 percent. The population-weighted average cost increase per vehicle is $146 – roughly equally split between higher vehicle prices ($74) and higher financing costs ($72).
Intensive vs. Extensive Margin. The composition of captive borrowers did not deteriorate following the tariffs: average household incomes of captive borrowers increased slightly (economically small), credit scores were unchanged, and future default rates showed no significant change. This confirms that the interest rate increase reflects tariff pass-through to inframarginal borrowers along the intensive margin, not a shift in borrower composition.
Heterogeneity by Credit Demand Elasticity. Pass-through via interest rates was higher for borrowers with lower incomes (33 basis points vs. 20 basis points for higher-income consumers), lower credit scores (36 basis points vs. 15 basis points), and smaller loan amounts (36 basis points vs. 12 basis points). These groups are proxies for less elastic credit demand, consistent with theoretical predictions that cost pass-through is larger where demand is less price sensitive.
Heterogeneity by Market Competition. Tariff pass-through via interest rates was higher in states with lower credit market competition (as measured by state-level Herfindahl-Hirschman Index). Consumers in the lowest competition decile experienced an average captive interest rate increase of 41 basis points, compared to 24 basis points for consumers in the highest competition decile. This 17 basis point differential implies that interest rate pass-through was approximately 88 percent as large as vehicle price pass-through in less competitive markets, versus 57 percent in more competitive markets.

In depth

Q1. What is a captive finance subsidiary, and why does it create a novel channel for tariff pass-through?

A captive finance subsidiary is a wholly owned lending unit of an auto manufacturer (e.g., Ford Credit, GM Financial, American Honda Finance) whose primary purpose is to finance the sale of the manufacturer’s vehicles. Because the captive lender and the manufacturing unit share a parent company, a cost shock to the manufacturing side – such as higher steel and aluminum prices from the tariffs – can be passed on to consumers not only through higher vehicle prices but also through worse financing terms offered by the captive. Prior studies documented tariff pass-through to goods prices but found limited evidence of pass-through to consumer prices; this paper shows that the bundling of a product with captive financing creates a second, previously unmeasured channel. The institutional structure also facilitates “price shrouding”: because consumers are less attentive to financing costs than vehicle sticker prices, captive lenders can exploit this inattention to pass on cost shocks along the financing margin.

Q2. Why is the auto loan market a particularly suitable setting for studying this question?

The auto loan market provides three key advantages. First, both captive lenders (directly exposed to metal tariffs via manufacturing) and noncaptive lenders (with no direct tariff exposure) compete for the same borrowers on the same vehicle purchases, creating a clean within-vehicle, within-period control group. Second, the Regulation AB II data contain vehicle make-model-condition information, allowing the authors to hold vehicle choice fixed and isolate tariff pass-through to loan terms separately from any vehicle switching by consumers. Third, the indirect dealer-intermediated financing process means that consumers typically do not observe the full set of lender bids, weakening their ability to actively arbitrage between captive and noncaptive loan offers.

Q3. What is the Regulation AB II data, and how representative is it?

Under Regulation AB II (effective November 2016), issuers of publicly offered auto loan asset-backed securities must report monthly loan-level data to the SEC, including interest rates, loan amounts, maturities, vehicle characteristics, borrower credit scores and incomes, and loan performance. The final sample covers approximately 8 percent of all open auto loans in the United States and around 30 percent of the total auto loan portfolios of the 14 sampled lenders. Average loan characteristics in the Regulation AB II data closely match population credit bureau data from Equifax, indicating that securitization selection is not a major concern. Average credit scores and incomes are slightly higher in Regulation AB II than in the population, primarily because small banks and credit unions that serve riskier borrowers do not access public securitization markets.

Q4. What is the baseline empirical specification and what identifying variation does it use?

The baseline is a difference-in-differences regression comparing captive loans (treated) to noncaptive loans (control) before and after January 2018 (the date of the Department of Commerce’s initial tariff recommendation, chosen conservatively). The regression includes lender fixed effects, vehicle make-model-condition x origination quarter fixed effects, state x origination quarter fixed effects, $25,000 income bin x origination quarter fixed effects, and 10-point credit score bin x origination quarter fixed effects. The coefficient of interest is estimated using within-lender variation after netting out common vehicle-level shocks, state-level shocks, and shocks common across income and credit score cells. This granular fixed effect structure ensures that the estimate compares captive and noncaptive loans for exactly the same vehicle, in the same state, in the same quarter, to borrowers with similar incomes and credit scores.

Q5. What are the main coefficient estimates on interest rates, and how do they evolve dynamically?

In the full sample, the pooled difference-in-differences estimate is 26 basis points (t = 2.75), representing a 10 percent increase relative to the pretreatment captive mean of 252 basis points. Excluding subvented (subsidized) loans, the estimate is 29 basis points (t = 2.85). Dynamically, captive interest rates started rising within one quarter of the treatment date and continued increasing alongside metal prices, reaching a terminal coefficient of 48 basis points in the fourth quarter of 2018 – nearly double the pooled average. Consistent with the parallel trends assumption, there is no economically significant evidence of differential pre-trends across captive and noncaptive loans in the pretreatment period.

Q6. How do the authors validate that noncaptive lenders constitute a valid counterfactual?

Four alternative specifications are presented. First, when splitting captive lenders by tariff exposure (more exposed: Ford, GM-AmeriCredit, Honda, Toyota; less exposed: BMW, Mercedes-Benz, Volkswagen), only more-exposed captive lenders show a significant increase in interest rates (30 basis points; t = 3.37), while less-exposed captive lenders show no significant increase (-18 basis points; t = -1.33). This rules out captive-specific correlated omitted variables. Second, the authors add interactions of the treatment indicator with changes in the Fed Funds rate and 1-, 5-, and 10-year Treasury yields; results are unchanged in magnitude, ruling out differential sensitivity to the rising interest rate environment of 2018. Third, using CarMax (a noncaptive that also sells and finances vehicles but does not participate in DealerTrack) as the sole control group yields similar results. Fourth, lender-specific borrowing cost controls do not attenuate the estimates.

Q7. Did captive lenders adjust any non-price loan terms in response to the tariffs?

No. Columns 2-4 of Table 3 document that loan amounts, maturities, and loan-to-value ratios showed no economically significant changes for captive lenders relative to noncaptive lenders following the tariffs. Some coefficient estimates in the full sample are statistically significant but economically small, and they lose significance or flip signs once subvented loans are excluded. The event study plots confirm no meaningful pre-trends and no meaningful post-treatment changes in non-price terms. The authors note that this is consistent with prior evidence that auto loan demand is less sensitive to interest rates than to maturity, making interest rates the optimal margin along which to pass through costs.

Q8. How do the authors rule out that the increase in captive interest rates reflects a change in borrower composition rather than intensive-margin pass-through?

The authors estimate a separate regression (equation 4) with log household income, log credit score, and future default rate as outcomes. Relative to noncaptive borrowers, captive borrowers experienced a small but positive increase in average household income (Gamma = 0.012, t = 3.25), no significant change in credit scores (Gamma = 0.001, t = 1.13), and no significant change in 12-month or 24-month default rates. The income increase is of the wrong sign and too small in magnitude to explain the observed interest rate increase from a risk-based pricing perspective. Additionally, captive loan origination volumes declined 6.7 percent after the tariffs, inconsistent with a demand surge driving the interest rate increase.

Q9. How do the authors rule out alternative explanations including demand surges, borrowing cost increases, securitization changes, and dealer markup changes?

For demand surges: vehicle sales volumes showed no noticeable increase following the tariff announcement, and captive loan originations actually declined. For differential borrowing costs: controlling for lender-specific CDS spreads and other borrowing cost measures does not attenuate the main estimate. For securitization changes: combining Regulation AB II and credit bureau data, the authors find no significant change in captive lenders’ securitization rates, the ratio of securitized to total loan amounts, maturities, or monthly payments. For dealer markup changes: noncaptive loans are also subject to dealer markups, so common changes are absorbed in the DiD; additionally, subvented loans (which dealers cannot mark up) also show higher captive interest rates post-tariff, ruling out differential markup changes. For interest rate sensitivity differentials: controlling for changes in risk-free rates does not alter results. For prepayment responses: 12-month and 24-month prepayment rates show no significant change for captive loans.

Q10. How do the authors measure vehicle price pass-through, and what data do they use?

To measure invoice price pass-through, the authors use Regulation AB II data (which contains the invoice price for new vehicles) and estimate a regression comparing the change in log invoice prices for makes with a higher proportion of US-assembled vehicles versus those with lower domestic production, controlling for vehicle make-model fixed effects and price bin x quarter fixed effects. Invoice prices rose approximately 1.0 percent for more-exposed makes. For consumer sales price pass-through, the authors use Texas DMV data (1,819,498 new and 2,105,938 used vehicle transactions in 2017-2018) with the same identification strategy. Sales prices rose approximately 0.7 percent ($225 average increase) for more-exposed makes. Both effects are robust to defining exposure at either the make level or the make-model level.

Q11. How is the overall pass-through rate decomposed between the interest rate and vehicle price channels?

The authors define total tariff pass-through as the sum of interest rate pass-through (change in aggregate captive financing costs divided by aggregate production cost increase) and vehicle price pass-through (change in aggregate new vehicle sales revenue divided by aggregate production cost increase). Taking the ratio of these two components allows them to estimate the relative importance of each channel without needing to directly measure production costs. With a captive loan penetration rate (M) of 0.59, a per-loan present value financing cost increase of $179 (unadjusted) or $227 (adjusted for 7 basis point spillover effect on noncaptives), and a $225 average vehicle price increase, the spillover-adjusted estimate implies interest rate pass-through is almost two-thirds as large as vehicle price pass-through. Focusing solely on vehicle prices would underestimate tariff incidence on consumers by approximately 37 percent. The population-weighted average total cost increase is $146 per vehicle, roughly equally split between vehicle prices ($74) and financing costs ($72).

Q12. How large is the estimated aggregate impact of the tariffs on consumer financing costs?

Using population data of approximately 50 million vehicles sold annually in the United States and a population-weighted average financing cost increase of $72 per vehicle, the authors estimate that the tariffs resulted in approximately $3.6 billion (= 50,000,000 x $72) in additional present value financing costs each year. For reference, Flaaen, Hortacsu, and Tintelnot (2020) estimated that the 2018 tariffs on washing machines led to $1.5 billion in additional annual consumer costs.

The triple-differences results show monotonically higher pass-through for borrowers with less elastic credit demand. Lower-income borrowers (below median) experienced an average captive interest rate increase of 33 basis points versus 20 basis points for higher-income borrowers. Lower-credit-score borrowers experienced an increase of 36 basis points versus 15 basis points for higher-credit-score borrowers. Borrowers with smaller loan amounts (below median) experienced an increase of 36 basis points versus 12 basis points for larger loan amounts. Within income quartiles, consumers in the lowest income quartile experienced a 37 basis point increase compared to 17 basis points in the highest quartile. These patterns are not driven by changes in borrower composition, as default rates show no significant change across any of these subgroups.

Q14. How does credit market competition affect tariff pass-through via interest rates?

States with lower credit market competition (higher Herfindahl-Hirschman Index, constructed from pretreatment lender market shares) experienced higher interest rate pass-through. Comparing above- versus below-median HHI states, the difference is 5 basis points (28 vs. 23 basis points), statistically significant at the 10 percent level. When restricting to the tails of the competition distribution, the difference is substantially larger: consumers in the lowest competition decile experienced an average increase of 41 basis points versus 24 basis points for consumers in the highest competition decile – a 17 basis point differential. This implies interest rate pass-through was 88 percent as large as vehicle price pass-through in less competitive markets versus 57 percent in more competitive markets, consistent with theoretical predictions that firm-specific cost shocks generate higher pass-through when competition is weaker.

Q15. Why do captive lenders spread interest rate increases broadly across vehicle types rather than targeting directly tariff-exposed new vehicle models?

The authors find that captive interest rates increased for both new and used vehicles, and that within more-exposed captive lenders, interest rate increases were not concentrated in domestically produced vehicle models. This is consistent with the hypothesis that firms spread cost shocks across multiple goods and business segments (as documented in the industrial organization literature for multiproduct firms). The authors argue this occurs because vehicles of different makes and models are substitutes for each other (making vehicle-specific price increases costlier in terms of demand loss), whereas auto loans are complementary to vehicle purchases and are offered as an add-on to the sales transaction. This bundled structure, combined with consumer inattention to financing terms, makes it optimal to spread the cost shock across the loan book rather than concentrating it in specific vehicle models.

Key Concepts

Captive Finance Subsidiary: A wholly owned lending unit of a manufacturer (e.g., Ford Credit, GM Financial) whose primary purpose is to originate loans and leases to finance the sale of the manufacturer’s own products. Unlike independent noncaptive lenders, captive lenders are vertically integrated with the manufacturing unit and can, in principle, use financing terms as an additional margin to pass through manufacturing-side cost shocks to consumers.

Tariff Pass-Through (Interest Rate Channel): The extent to which an input cost increase caused by an import tariff is transmitted to consumers via higher interest rates charged by captive lenders, rather than (or in addition to) higher goods prices. The paper defines interest rate pass-through as the ratio of the aggregate present value increase in captive financing costs to the aggregate increase in manufacturing production costs.

Intensive vs. Extensive Lending Margin: The distinction between raising loan prices charged to existing (inframarginal) borrowers (intensive margin) versus changing the pool of borrowers served or lending standards (extensive margin). The paper argues that the observed increase in captive interest rates reflects intensive-margin pass-through because borrower incomes, credit scores, and future default rates did not change significantly after the tariffs.

Price Shrouding: The practice of making price increases less salient to consumers by embedding them in a less-scrutinized component of a bundled transaction. In the auto market, because consumers are documented to be less sensitive to increases in financing costs than to vehicle sticker prices, captive lenders can pass on cost shocks through interest rates with less demand response than if they raised vehicle prices by an equivalent amount. The paper treats this as a key mechanism enabling the financing pass-through channel.

Subvented (Subsidized) Loan: A promotional auto loan offered at a below-market interest rate, often tied to specific vehicle models or sales events (e.g., “1.99 percent APR for well-qualified borrowers”). Subvented loans are typically fixed by the manufacturer and cannot be marked up by dealers. The paper uses the subsample of non-subvented loans as a robustness check and to isolate tariff pass-through from seasonal variation in promotional financing.

Captive Loan Penetration Rate (M): The ratio of captive auto loans originated to new vehicles produced and sold, used in the paper’s decomposition of total tariff pass-through into the interest rate and vehicle price channels. Estimated at approximately 0.59 from population data, this parameter determines how the aggregate present value financing cost increase scales relative to the aggregate vehicle sales price increase when computing the relative importance of the two pass-through channels.

Herfindahl-Hirschman Index (HHI) as Market Competition Measure: The paper constructs state-level HHIs based on pretreatment lender market shares in each state using population credit bureau data, as an inverse measure of credit market competition. Local (direct) auto lending markets exhibit meaningful geographic variation in HHI, in contrast to the largely national scope of indirect (dealer-arranged) lending. The paper uses this variation to test whether pass-through is higher in less competitive credit markets, consistent with theoretical predictions for firm-specific cost shocks.

Contextually Private Mechanisms

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

Haupt and Hitzig introduce a framework for comparing the privacy properties of different mechanism protocols. The core research question is: when a designer commits to implementing a social choice rule, how much superfluous private information must they inevitably learn about agents, and how should they design the elicitation protocol to minimize that exposure?

The setting is a finite-player extensive-form game in which a designer elicits agents’ private types through a dynamic protocol to compute a social choice function. The authors explicitly exclude cryptographic tools and trusted mediators, working under the minimal assumption that the designer learns information if and only if an agent discloses it. This assumption is motivated by the historical prevalence of live dynamic auction formats — ascending formats at Sotheby’s, descending formats at Aalsmeer, oral ascending formats used by the U.S. Forest Service for timber, multi-round clock auctions for radio-spectrum allocation — and by settings where mediating technology is unavailable or costly.

The central object is the contextual privacy violation. A protocol produces a contextual privacy violation for agent i at type profile θ if the designer can distinguish θ_i from some alternative type θ’_i while holding other agents’ types fixed, yet the social choice rule assigns the same outcome at both profiles. Violations are defined at the level of individual agent–state pairs, not aggregated ex ante. A protocol is fully contextually private if it produces no violations; it is maximally contextually private if its set of violations is inclusion-minimal among all protocols that implement the same rule.

The main characterization result (Theorem 1) connects privacy to pivotality: a social choice function admits a fully contextually private protocol if and only if, on every product subset of the type space where agents are collectively pivotal, at least one agent is individually pivotal. The contrapositive is what drives the paper’s impossibility results: whenever a rule contains a region where no single agent’s report changes the outcome but a group’s joint report does, any implementing protocol must produce contextual privacy violations.

Using this characterization, the authors establish that the first-price auction rule (Proposition 2) and serial dictatorship (Proposition 3) admit fully contextually private protocols. Conversely, k-item Vickrey auction rules (Proposition 4) and any stable school-choice rule (Proposition 5) do not admit fully contextually private protocols, because these rules contain type-space regions where agents are only collectively — not individually — pivotal.

For k-item Vickrey auctions, the authors study maximally contextually private protocols. They establish (Proposition 6) that, for a class of social choice rules on totally ordered type spaces that contains k-item Vickrey auctions, it is without loss to consider only protocols consisting of threshold queries that are monotonically increasing or decreasing after an initial guess. This reduction identifies two key design dimensions: the initial query posed to each agent, and the order in which agents are queried.

The main constructive result (Theorem 2) proves that an ascending-join protocol is maximally contextually private for the k-item Vickrey auction. Proposition 7 formalizes the sense in which this protocol protects privacy by delaying queries to certain bidders — it repeatedly asks agents whether they can rule out a particular outcome, and postpones questioning agents whose privacy it is protecting.

The authors also show (Proposition 19) that the ascending-join protocol is minimally relatively informative among protocols that are maximally contextually private. Extensions cover group contextual privacy (Proposition 11) and individual contextual privacy (Proposition 8), showing that individual contextual privacy violations equal the union of contextual privacy violations and nonbossiness violations.

Q: What is a contextual privacy violation, precisely? A: A protocol produces a contextual privacy violation for agent i at type profile θ if the designer can distinguish θ_i from some alternative type θ’_i — holding all other agents’ types fixed — yet the social choice rule assigns the same outcome at both profiles. The violation is defined at the level of individual agent–state pairs. A single additional superfluous distinction at the same (i, θ) pair does not register as a second violation; the framework records whether any unnecessary disclosure occurs for that agent at that state, not the degree of overexposure.

Q: How does contextual privacy differ from relative informativeness? A: Relative informativeness compares two protocols by whether one distinguishes every pair of type profiles the other does, treating all disclosures as equally undesirable. Contextual privacy conditions the notion of a “violation” on the social choice rule: a distinction between θ_i and θ’_i counts as a violation only when the rule assigns the same outcome at both profiles. Relative informativeness thus penalizes the designer for learning information that is necessary to implement the rule, whereas contextual privacy imposes no penalty for learning pivotal information.

Q: What is the pivotality characterization (Theorem 1)? A: A social choice function admits a fully contextually private protocol if and only if, on every product subset of the type space where agents are collectively pivotal, at least one agent is individually pivotal. The necessity direction shows that if a collectively pivotal set exists where no agent is individually pivotal, any implementing iterative partition must contain an earliest node that distinguishes two type profiles leading to the same outcome. The sufficiency direction constructs a contextually private protocol inductively by always querying an individually pivotal agent, ensuring every distinction implies a different outcome.

Q: Which social choice rules admit fully contextually private protocols? A: The first-price auction rule (Proposition 2) and serial dictatorship (Proposition 3) admit fully contextually private protocols. The authors use Theorem 1 to show this: in both rules, any collectively pivotal region contains an individually pivotal agent. By contrast, k-item Vickrey auction rules (Proposition 4), any stable school-choice rule (Proposition 5), efficient allocations in housing assignment, and generalized median voting rules (Section B) do not admit fully contextually private protocols.

Q: Why do k-item Vickrey auctions fail full contextual privacy? A: Proposition 4 shows that k-item Vickrey auctions for k ≥ 1 do not admit fully contextually private protocols. The argument uses the necessary conditions from Theorem 1 (Corollaries 1 and 2): the Vickrey payment rule creates type-space regions where multiple agents together determine the price but no single agent is individually pivotal over the price, so any protocol implementing the Vickrey rule must produce violations for at least some agents at some type profiles.

Q: What is the ascending-join protocol and what does Theorem 2 establish? A: The ascending-join protocol is a specific dynamic elicitation protocol for k-item Vickrey auctions that repeatedly asks agents whether they can rule out a particular outcome, structured as threshold queries ascending from an initial guess. Theorem 2 proves that the ascending-join protocol is maximally contextually private for the k-item Vickrey auction. Proposition 7 formalizes the protection mechanism: the protocol delays queries to the bidders whose privacy it is protecting, querying them only when their responses become necessary for determining the outcome.

Q: What does Proposition 6 establish about the structure of maximally contextually private protocols? A: For a class of social choice rules on totally ordered type spaces that contains k-item Vickrey auctions, Proposition 6 shows it is without loss of generality to consider only protocols consisting of threshold queries that are monotonically increasing or decreasing in the threshold after an initial guess. This result serves as a theoretical reduction (enabling proofs that certain protocols are maximally private) and as a practical design principle (identifying the initial query and the ordering of agents as the two key design dimensions).

Q: How does contextual privacy relate to obviously dominant strategies? A: The paper treats privacy properties and incentive properties as largely orthogonal questions, to be analyzed separately. For the ascending-join protocol specifically, the authors verify obvious dominance — the most demanding incentive notion they consider — which requires that at every history, the worst-case payoff from the equilibrium action exceeds the best-case payoff from any deviation. This analysis proceeds after the contextual privacy properties of the protocol are established.

Q: What is group contextual privacy and why do the authors focus on individual-level violations instead? A: Group contextual privacy requires that whenever the designer learns any property of the joint type profile, that property must affect the outcome. The authors show (Proposition 11) that a protocol is fully group contextually private if and only if every query rules out at least one outcome. They argue this standard is extremely demanding and produces a very coarse partial order: improving in the group privacy order requires restructuring the entire protocol tree rather than making agent- or state-specific improvements. They also note that normative accounts of privacy, including Nissenbaum’s contextual integrity theory, center on individual rather than group information.

Q: How does individual contextual privacy relate to nonbossiness? A: Individual contextual privacy (Proposition 8) requires that if two type profiles differing only in agent i’s type are distinguished, they must lead to different allocations for agent i — presuming a private allocation domain. The paper shows that the set of individual contextual privacy violations equals the union of contextual privacy violations and nonbossiness violations: individual contextual privacy is violated precisely when either (a) agent i’s superfluous type information is revealed, or (b) agent i is “bossy” — able to change others’ outcomes without changing their own.

Q: What is the relationship between the ascending-join protocol and minimal relative informativeness? A: Proposition 19 shows that the ascending-join protocol is not only maximally contextually private but also minimally relatively informative among protocols that are maximally contextually private. That is, among all maximally contextually private protocols, the ascending-join protocol reveals the smallest total amount of information about the type profile in the relative informativeness order. This establishes relative informativeness as a useful refinement for selecting among contextually privacy-equivalent protocols.

Q: What motivates the exclusion of cryptographic tools and trusted mediators from the framework? A: The authors work under the minimal assumption that the designer learns information if and only if an agent directly discloses it — no commitment to forget, anonymize, or cryptographically conceal. They motivate this on two grounds: first, many real-world auction formats are live and dynamic with no mediating technology; second, advanced cryptography is often costly in time, money, or computation, and studying the no-mediator benchmark can explain the historical prevalence of dynamic protocols and inform auction design in environments where cryptography may become unavailable (for example, due to quantum computing). The authors cite a Danish sugar-beet auction as a case where designers themselves questioned whether full multiparty computation was necessary.

Contextual privacy violation: A protocol produces a contextual privacy violation for agent i at type profile θ if the designer can distinguish θ_i from some alternative type θ’_i — holding other agents’ types fixed — yet the social choice rule assigns the same outcome at both profiles. The violation is assigned at the level of individual agent–state pairs.

Maximally contextually private protocol: A protocol whose set of contextual privacy violations is inclusion-minimal among all protocols that implement the same social choice rule — equivalently, a protocol that lies on the Pareto frontier of implementation and contextual privacy, such that no other implementing protocol weakly reduces every violation and strictly reduces at least one.

Iterative partition: A directed rooted tree whose nodes are subsets of the type space, where each non-leaf node is split into children by partitioning on a single agent’s type. Any protocol is equivalent (in terms of what the designer learns) to a partitional protocol induced by an iterative partition (Proposition 1).

Individual pivotality: On a product set of type profiles, agent i is individually pivotal if there exist two subsets of agent i’s types such that every type profile from one subset leads to a different outcome than every type profile from the other subset, holding others’ types fixed.

Collective pivotality: Agents are collectively pivotal on a product set if there exist two type profiles in that set with different outcomes. Collective pivotality without any agent being individually pivotal is precisely the condition that forces contextual privacy violations (Theorem 1).

Ascending-join protocol: A specific dynamic protocol for k-item Vickrey auctions that poses threshold queries in ascending order after an initial guess, repeatedly asking agents whether they can rule out a particular outcome. It is maximally contextually private (Theorem 2) and minimally relatively informative among maximally contextually private protocols (Proposition 19), and it achieves privacy protection by delaying queries to agents whose privacy it protects (Proposition 7).

Relative informativeness: A partial order on protocols defined by: protocol P is less relatively informative than P’ if every pair of type profiles P distinguishes is also distinguished by P’. Unlike contextual privacy, relative informativeness treats all disclosures as equally undesirable and does not condition on the social choice rule. The paper positions it as a useful refinement for selecting among contextually privacy-equivalent protocols.

Default Options and Retirement Saving Dynamics

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

Overview

Research question. Does automatic enrollment (auto-enrollment) in retirement savings plans increase lifetime wealth accumulation and welfare? The prior literature established large short-run participation effects but had not traced the policy’s consequences over a full working life.

Data. The paper draws on two primary sources. First, a proprietary panel of 401(k) administrative records from nearly 600 U.S. firms, covering roughly 159,216 first-year employees across 86 firms (for the “increasing default” fact) and 6,415 employees across 34 firms (for structural estimation), observed between December 2006 and December 2017. Second, 12 successive waves (2006–2017) of the U.K. Annual Survey of Hours and Earnings (ASHE), a 1% nationally representative panel of approximately 200,000 private-sector employees per year, including 37,120 job-switchers, used to exploit the phased rollout of the U.K. Pension Act of 2008.

Methodology. The paper proceeds in three steps. (1) Three empirical stylized facts are documented using quasi-experimental variation (comparing employees hired before versus after changes in the default contribution rate within the same firm, and exploiting the staggered employer-size-based rollout of U.K. auto-enrollment). (2) A structural lifecycle model is estimated via the Method of Simulated Moments, using three preference parameters—intertemporal discount factor (δ), elasticity of intertemporal substitution (σ), and opt-out cost (k)—identified from the within-firm default variation in 34 U.S. firms. (3) The estimated model is used for out-of-sample validation and counterfactual welfare analysis.

Three stylized facts.

Fact I — Increasing the default reduces participation. Among 159,216 first-year employees in 86 auto-enrollment firms, each percentage-point increase in the default contribution rate reduces 401(k) participation by approximately 1 percentage point and increases contributions strictly below the new default by 1 percentage point. When the default rose from 3% to 6%, workers were 3.2 percentage points more likely to contribute at 1% or 2% of salary. This “drop-out” pattern is consistent with an opt-out cost model but is inconsistent with loss-aversion and psychological-anchoring theories, both of which predict that raising the default should weakly increase low-end contributions.

Fact II — Non-autoenrolled workers catch up within three years. In the estimation sample of 34 U.S. firms offering a 50% match up to 6% and an auto-enrollment default of 3%, median cumulative employee 401(k) contributions of non-autoenrolled workers equal those of autoenrolled workers after three years of tenure. Because non-autoenrolled workers compensate for initial non-participation by contributing more later—earning similar cumulative employer match and tax benefits over the full three-year horizon—a modest opt-out cost suffices to explain the observed inertia. Previous studies (which examined only the first year of tenure and did not allow future contribution adjustment) inferred opt-out costs of $1,000–$2,200 or more; the dynamic model implies a cost of only approximately $250.

Fact III — Prior auto-enrollment reduces saving in the next job. Using the phased U.K. policy rollout, workers who were auto-enrolled in their previous job and then move to a new employer that has not yet implemented auto-enrollment participate 12.8 percentage points less and contribute 0.55% of salary less in the new plan relative to otherwise similar job-switchers from non-auto-enrollment employers. When the new employer also has auto-enrollment, no statistically significant difference is observed. Placebo rollout tests confirm the effect is not a pre-existing selection pattern. This negative spillover contradicts a “savings habit” hypothesis and suggests that auto-enrollment’s short-run boost overstates lifetime savings effects.

Structural estimation results. The estimated quarterly discount factor is δ = 0.987 (approximately 0.949 annually), and the elasticity of intertemporal substitution is σ = 0.435, both standard in lifecycle models. The opt-out cost is estimated at $254 per contribution-rate change (standard error $11). Sensitivity exercises show that combining a short observation window (first year only), sticky contributions (no intra-job adjustment), no income uncertainty, immediate vesting, and penalty-free DC withdrawals yields an opt-out cost of $3,004—broadly matching the range in previous studies. The low baseline estimate is thus driven by the dynamic nature of decisions (ability to compensate later), the illiquidity of retirement accounts (which reduces their perceived value), and income uncertainty (which expands the inaction range).

Long-run wealth effects. Simulating a universal 3% auto-enrollment policy, the model predicts that wealth at retirement changes by less than 2% for the top 7 income deciles. For individuals in the top two deciles, total wealth at age 65 is actually reduced by less than 1% because many high earners who would voluntarily contribute above 3% are pulled down to the default. At the bottom decile, however, auto-enrollment raises total retirement wealth by more than 12%; savings increases are concentrated in the first 20 years of working life and peak around age 45, where bottom-quintile workers hold an additional 20% of average annual lifetime earnings. Even at the bottom, approximately one-third of the early savings gains are offset by lower contributions after age 45, as the wealth effect dominates. Crowd-out of liquid savings is limited: for bottom-quintile individuals, 89% of the increase in retirement savings at age 65 passes through to total wealth; for middle-quintile individuals, 62% passes through.

Out-of-sample validation. The U.S.-estimated model is not rejected (at the 10% level) in 8 of 11 response moments in the 86-firm sample where defaults were raised between two positive rates, covering over 85% of workers. Recalibrated to U.K. institutions (using δ and σ from the U.S. and k = £160 via the average USD/GBP exchange rate), the model replicates the roughly 30-percentage-point increase in both participation and contributions at the 1% U.K. default. The model also predicts a 9.6-percentage-point drop in participation when workers move from an auto-enrollment to an opt-in employer, close to the empirical 12.8 percentage points.

Welfare and optimal policy. Under utilitarian preferences (policymaker shares individuals’ discount rate, no redistributive motive), the opt-in regime is always preferred to auto-enrollment regardless of policy incidence, because matching and tax incentives already induce over-saving relative to individuals’ revealed time preferences. Under paternalistic preferences (social discount factor = 1) or inequality-averse preferences (Pareto weights inversely proportional to income, with degree of inequality aversion ν = 1 following Saez 2002), an auto-enrollment default at or near the employer matching threshold (6% of income) maximizes social welfare. A 6% auto-enrollment default improves welfare by 0.3% in lifetime consumption-equivalent for the bottom decile even under a utilitarian policymaker when incidence is on employers. These optimal policy rankings are robust to whether the opt-out cost is treated as fully welfare-relevant (π = 1) or welfare-irrelevant (π = 0), and hold under three incidence scenarios (employer profit reduction, match-rate adjustment, wage adjustment).

In depth

Q1. What is the core mechanism by which non-autoenrolled workers “catch up” at the median, and why does this reduce the implied opt-out cost relative to prior estimates?

A: Non-autoenrolled workers who do not contribute in their first year are not permanently forgoing employer matching and tax benefits; they can contribute more later in the same job and earn similar cumulative benefits. The paper shows that at the median and 75th percentile, cumulative employee 401(k) contributions among opt-in workers equal those of autoenrolled workers after three years of tenure in 34 U.S. firms offering a 50%-up-to-6% match at a 3% default. This dynamic substitutability means the opportunity cost of initial non-participation is far smaller than one-period back-of-the-envelope calculations suggest. Previous studies, which implicitly or explicitly assumed static contribution decisions or examined only the first year, inferred opt-out costs of $1,000–$2,200; in a fully dynamic model the same inertia requires only ~$254.

Q2. Why does Fact I (higher default reduces participation) specifically rule out loss aversion and anchoring as the primary mechanism, and what does it support instead?

A: Under loss aversion, contributions above the default feel like losses while contributions below the default feel like gains. Raising the default shifts some contributions from the loss domain into the gain domain, making low contributions relatively less attractive. Proposition 2 demonstrates formally that loss-averse preferences predict a weakly lower fraction contributing below the new (higher) default — the opposite of what is observed. Similarly, Proposition 3 shows that psychological anchoring shifts preferences toward the new default, also predicting more participation at low rates when the default rises. Only the opt-out cost model (Proposition 1) predicts that a higher default causes some workers to incur the cost to switch away from the default and end up at lower contribution rates, matching the empirical finding that each 1-percentage-point rise in the default increases contributions strictly below the old default by approximately 1 percentage point.

Q3. What is the quantitative magnitude of the opt-out cost, and what modeling assumptions are responsible for it being much smaller than prior estimates?

A: The baseline estimate is $254 per contribution-rate change (s.e. $11), roughly an order of magnitude smaller than prior estimates of $1,000–$3,000+. Table 4 decomposes the sources of the difference: using only first-year data changes the estimate only slightly (to $226). Assuming contributions cannot be changed within a job (“sticky contributions”) raises the cost to $308 with four years of data or $712 with one year of data. Eliminating income uncertainty raises the estimate to $465. Assuming immediate vesting raises it to $344. Assuming penalty-free DC withdrawals raises it to $609. Combining all these restrictions simultaneously yields $3,004 — closely matching the prior literature. The three key drivers are thus: (1) the ability to adjust contributions over time within a job; (2) the illiquidity of the DC account (early-withdrawal penalties); and (3) income uncertainty widening the inaction range.

Q4. How does the paper validate the structural model out of sample, and what confidence does this provide in the long-run predictions?

A: Two out-of-sample exercises are reported. First, the model estimated on 34 U.S. firms (introduction of auto-enrollment from 0% to 3% default) is used to predict workers’ response when 86 other firms raised the default from one positive rate to a higher rate. The model prediction cannot be rejected at the 10% level in 8 of 11 response-moment cases, covering 71 of 86 firms and more than 85% of workers. Second, the model is re-calibrated to U.K. institutions (keeping U.S. preference estimates, setting k = £160 via exchange rate) and applied to the phased rollout of the U.K. Pension Act of 2008. The model replicates the roughly 30-percentage-point increase in both participation and contributions at the 1% default following the policy, and predicts a 9.6-percentage-point drop in participation when previously autoenrolled workers move to a new opt-in employer — compared with an empirical estimate of 12.8 percentage points (s.e. 5.5 pp).

Q5. What are the distributional implications of a universal 3% auto-enrollment policy for wealth at retirement?

A: The effect is concentrated at the bottom. For the top 7 income deciles, retirement wealth at age 65 changes by less than 2% relative to the opt-in counterfactual. For the top two deciles, total wealth at age 65 is actually reduced by less than 1% because high-earning workers who would voluntarily contribute above 3% are pulled down to the default. For the bottom decile, the policy raises total retirement wealth by more than 12%. Even at the bottom, roughly one-third of the early savings gains are later offset by lower contributions after age 45 as the wealth effect dominates, so even 20-year empirical follow-ups may overstate the policy’s lifetime effect at the bottom.

Q6. How large is crowd-out of liquid savings by auto-enrollment, and what explains the limited degree of substitution?

A: Crowd-out is modest. For bottom-quintile workers, 89% of the increase in retirement savings at age 65 translates into higher total wealth; for middle-quintile workers, 62% passes through. The limited crowd-out arises because liquid assets serve a precautionary motive and DC accounts serve a lifecycle motive — the two assets are not close substitutes. Additionally, as in Kaplan and Violante (2014), the marginal propensity to consume out of liquid assets is high in the model, so autoenrolled workers reduce consumption rather than run down liquid balances. These predictions align with Beshears et al. (2021), who find no significant increase in unsecured debt after four years, and Chetty et al. (2014), who estimate an 80% pass-through to total savings in a different Danish policy.

Q7. Why do previously autoenrolled workers contribute less when they switch to an opt-in employer, and how is this consistent with the model?

A: The most plausible explanation, and the one consistent with the model’s out-of-sample predictions, is a standard wealth effect: workers auto-enrolled early accumulate more retirement wealth and therefore have less incentive to contribute in a new job. The model predicts a 9.6-percentage-point participation drop for AE-to-non-AE movers, close to the empirical 12.8 pp. An alternative explanation — that previously autoenrolled workers rationally expect their new employer to soon adopt auto-enrollment and thus delay active enrollment — is partially ruled out by the finding that the empirical estimate is closer to the model prediction for job-switchers whose new employer is not expected to adopt auto-enrollment in the next 12 months.

Q8. What are the welfare implications of auto-enrollment under utilitarian, paternalistic, and inequality-averse policymakers, and how robust are these to the incidence assumption?

A: Under utilitarian preferences (policymaker shares individuals’ discount factor, no extra redistributive weight), the opt-in regime is always preferred regardless of whether the policy’s cost falls on employer profits, the match rate, or wages. The negative welfare effect is largest when incidence falls on wages (approximately 50% larger than under match-rate reduction). Under paternalistic preferences (social discount factor = 1), a 6% default (equal to the employer matching threshold) is optimal under all three incidence scenarios. Under inequality-averse preferences (ν = 1 Pareto weights), a 6% default is optimal when incidence falls on employers, and a 5% default when incidence falls on workers. These results are identical whether the opt-out cost is treated as fully welfare-relevant (π = 1) or welfare-irrelevant (π = 0). A 6% auto-enrollment default increases welfare by 0.3% in lifetime consumption-equivalent for the bottom income decile even under a utilitarian planner when incidence is on employers.

Q9. How does the paper address heterogeneity in default effects across age and income groups within a parsimonious homogeneous preference model?

A: The model has only three estimated preference parameters (δ, σ, k), yet it endogenously replicates empirical heterogeneity. Conditional on participating, workers in their 20s are approximately 20 percentage points more likely to stay at the 3% default than workers in their late 50s and early 60s; the model attributes this to the option value of waiting: young workers can compensate for current non-saving by contributing more later, so the cost of opting out is effectively smaller for them. The lowest-income workers are approximately 40 percentage points more likely to remain at the default than the highest-paid; the model explains this primarily because the fixed opt-out cost of $254 represents a larger share of earnings for low-income individuals (and secondarily because high-income workers have more to gain from active contribution decisions due to higher marginal tax rates and a lower Social Security replacement rate). All model-predicted coefficients fall within the 95% confidence intervals of the empirical estimates.

Q10. What does the paper conclude about the broader relevance of the “dynamic opt-out cost” framework beyond retirement saving?

A: The paper argues that wherever individuals can compensate for present inaction with future actions — as in retirement saving — the observed inertia at a default understates the freedom of choice preserved by the nudge, and short-run effects overstate long-term consequences. In contrast, in domains such as healthcare plan choice or school selection, future actions cannot easily offset present inertia; opt-out costs are likely to remain large; and the distinction between a nudge and a hard mandate collapses. The paper therefore argues that the appeal of “libertarian paternalism” (Thaler and Sunstein 2003) is domain-specific and is strongest precisely where intertemporal adjustment is possible.

Key Concepts

Opt-out cost (k). In this paper, a utility cost — estimated at $254 per contribution-rate change — that individuals must pay every time they choose a retirement contribution rate different from the current default. The cost is modeled as a consumption reduction and captures both real transaction costs (form-filling, adviser fees) and behavioral costs (cognitive cost of attention and optimal-choice search). It is fixed and homogeneous across individuals, and applies symmetrically in any direction of deviation from the default.

Auto-enrollment default contribution rate. The positive contribution rate at which new hires are automatically enrolled in a defined-contribution plan, with the option to opt out by incurring the opt-out cost. In the paper’s estimation sample, this is 3% of salary. The default is exogenous at the start of each new job but endogenous thereafter: once established, the default for subsequent periods equals the worker’s contribution rate in the previous period.

Default eﬀect. The empirically observed tendency of workers to remain at the default contribution rate rather than actively choosing a different rate. In this paper, the default effect is explained by opt-out costs rather than loss aversion or psychological anchoring — a distinction identified through the novel prediction that raising the default from a positive rate to a higher positive rate reduces overall participation (the “drop-out” effect), a pattern consistent only with opt-out costs.

Drop-out eﬀect. The paper’s term (following Caplin and Martin 2017) for the empirical finding that increasing the auto-enrollment default contribution rate causes some workers to stop contributing altogether or to contribute at rates strictly below the initial default. This effect is used as a discriminating test between competing theories of the default effect.

Dynamic opt-out cost framework. The paper’s core modeling insight: that opt-out costs must be estimated in a fully dynamic lifecycle model that allows workers to adjust contributions over time, to hold liquid assets and unsecured debt, and to face labor market risk. In a static or short-horizon model, the opportunity cost of initial non-participation appears large (because the worker permanently forgoes match and tax benefits), requiring large opt-out costs. In the dynamic model, the ability to compensate later shrinks the implied opportunity cost and hence the opt-out cost required to rationalize observed inertia.

Crowd-out of liquid savings. The extent to which higher DC retirement contributions induced by auto-enrollment reduce liquid asset holdings (or increase unsecured borrowing), rather than increasing total wealth. The paper estimates limited crowd-out (89% pass-through to total wealth for bottom-quintile workers, 62% for middle-quintile workers), attributable to the different roles of liquid assets (precautionary motive) and DC accounts (lifecycle motive) in the model.

Policy incidence. The channel through which employers balance their budget in response to higher matching costs created by auto-enrollment. The paper considers three scenarios: employers absorb costs through reduced profits; employers reduce the match rate; employers reduce wages. Optimal policy rankings and welfare magnitudes differ across these scenarios, but the qualitative conclusions — utilitarian policymaker prefers opt-in; paternalistic or inequality-averse policymaker prefers AE at 6% — are robust across incidence assumptions.

Consumption-equivalent variation (γ). The welfare metric used in the paper: the proportional increase in consumption in every period and every state of the world that would make the policymaker indifferent between an auto-enrollment policy at default d and the opt-in regime. A 6% default increases welfare by 0.3% in consumption-equivalent for the bottom income decile under a utilitarian policymaker when incidence is on employers.

Defying Distance? The Provision of Medical Services in the Digital Age

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

This paper asks whether digital platforms can improve healthcare outcomes by enabling needs-based matching between patients and physicians unconstrained by geography. Amanda Dahlstrand studies digital primary care in Sweden during 2016-2018, exploiting nationwide conditional random assignment between approximately 200,000 patients and 143 doctors employed by Europe’s largest digital primary care provider. Patients who selected the “first available doctor” option (82% of first visits) were effectively randomized to a doctor within each 3-hour shift-by-date stratum, generating quasi-experimental variation free of the patient-doctor sorting that confounds identification in physical primary care.

The paper defines three observable dimensions of primary care physician skill: (1) identifying risky patients and triaging them to higher levels of care, measured by whether patients subsequently have an avoidable hospitalization within 90 days; (2) providing guideline-consistent treatment, measured by counter-guideline antibiotic prescriptions; and (3) leaving patients sufficiently informed so they do not unnecessarily seek additional in-person care within the following week. Doctor skill in each dimension is estimated via a value-added framework in a hold-out sample (Sample 1, the first 600 randomized consultations per doctor), using empirical Bayes shrinkage to reduce noise. Complementarities between doctor skill and patient risk are then estimated in a disjoint main sample (Sample 2).

A central finding is that doctor skill is task-specific rather than governed by a single latent ability: skills across the three tasks are not positively correlated, meaning doctors within general practice have individual “specializations.” A patient ranked in the top 1% of avoidable hospitalization risk who is matched to a doctor ranked in the top 10% at reducing avoidable hospitalizations experiences a 90% reduction in that adverse outcome, relative to a patient with the same risk profile matched to the worst-performing doctor. Patients not estimated as risky show effects indistinguishable from zero when matched to the same high-skilled doctors, establishing a strong complementarity between doctor type and patient risk.

Using the Average Match Function framework of Graham, Imbens, and Ridder (2014, 2020), the paper evaluates counterfactual reallocation policies. Reallocating only 2% of patients — those in the top 1% of predicted avoidable hospitalization risk — to doctors in the top 10% of triage skill reduces aggregate avoidable hospitalizations by 20% relative to random assignment, without adversely affecting counter-guideline prescriptions or other measured outcomes. Doctor skills across outcomes are not positively correlated, so this reallocation does not generate meaningful trade-offs. The paper benchmarks this matching policy against a selective hiring/expansion policy in which doctors with above-median skill in three tasks expand their hours by up to 70% at the expense of below-median peers; that policy yields no significant reduction in avoidable hospitalizations and only a 4% reduction in counter-guideline prescriptions — smaller gains than matching and harder to implement.

The paper also documents that physical primary care quality is worse in lower-income and more deprived areas of Sweden (a negative relationship between deprivation index and patient-reported experience is statistically significant at the 1% level in a cross-section of roughly 120-150 primary care centers in Region Skane). Because the estimated risk of avoidable hospitalization and prior avoidable hospitalizations are concentrated in the lower end of the income distribution, needs-based digital matching reallocates triage skill toward lower-income patients, severing the correlation between local area income and service quality. Simulating positive assortative matching on patient income and doctor skill — approximating existing healthcare inequalities — leads to more avoidable hospitalizations than random assignment, because the most vulnerable patients tend to be the poorest. Scope conditions: findings derive from a single digital primary care provider in Sweden, 2016-2018, pre-pandemic, covering conditions amenable to video consultation and a patient pool younger and somewhat more urban than the average Swedish citizen.

Q: What is the key identification strategy, and why is it valid in this setting but not in physical primary care? A: Patients who selected the “drop in” (first available doctor) option — 82% of first visits — were assigned to whichever certified doctor was next in the roster within a 3-hour shift-by-date stratum, a by-product of the first-come-first-served queue. Neither patients nor doctors could intervene in this digital process. The author validates the assumption by regressing doctor characteristics on patient characteristics controlling for shift-by-date fixed effects and finds characteristics are balanced. In physical primary care, endemic patient-doctor sorting means doctors do not meet a common support of patient types, preventing causal identification of doctor effects.

Q: How are doctor skill estimates constructed and why does the split-sample matter? A: Doctor skill in each task is estimated as an empirical Bayes-shrunk random effect from a value-added regression on Sample 1, each doctor’s first 600 randomized consultations (40% of the sample). Sample 2 (60%) is entirely disjoint and used to estimate complementarities between doctor skill and patient risk. The split-sample design prevents overfitting: doctor skill was estimated on different patients than those in Sample 2. The Durbin-Wu-Hausman test does not reject random effects (p = 0.16).

Q: What is the main quantitative result on avoidable hospitalization matching? A: A patient ranked in the top 1% of predicted avoidable hospitalization risk matched to a doctor ranked in the top 10% at reducing avoidable hospitalizations could reduce that patient’s avoidable hospitalizations by 90%, relative to the worst-performing doctor in that skill. At the aggregate level, reallocating only 2% of patients (those in the top 1% risk group) to high-triage-skill doctors reduces avoidable hospitalizations across the full patient population by 20% compared to random assignment.

Q: Does the avoidable hospitalization reallocation harm other outcomes? A: No. The paper explicitly evaluates the Average Reallocation Effect on counter-guideline prescriptions and additional in-person care seeking when optimizing for avoidable hospitalizations, and finds no significant adverse effects on these other outcomes. The author attributes this to the fact that doctor skills across tasks are not positively correlated, so reallocating triage-skilled doctors does not systematically remove skill from other dimensions.

Q: How does matching compare to selective hiring and hour expansion as a policy? A: Even expanding the working hours of doctors with above-median skill across three tasks by as much as 70% yields no significant reduction in avoidable hospitalizations and only a 4% reduction in counter-guideline prescriptions — both smaller gains than the matching policy. Matching outperforms hiring expansion because patients have heterogeneous needs that can be identified from prior healthcare records, and doctors have differentiated skill sets relevant to some patients but not others.

Q: What is the evidence that doctor skills are task-specific rather than reflecting a single latent ability? A: The estimated doctor effects across the three tasks — triaging to avoid hospitalizations, guideline-consistent antibiotic prescribing, and minimizing unnecessary follow-up care — are not positively correlated with one another. This means a doctor who is effective at one task is not systematically effective at others, indicating individual specializations within general practice that are not accounted for in standard primary care organization.

Q: How is patient risk for avoidable hospitalizations measured? A: A propensity score is estimated from pre-digital physical healthcare data (2013-2015), regressing past number of avoidable hospitalizations on demographic and healthcare utilization variables — including age, a disease index of chronic diagnoses, and previous hospitalizations — all variables already available in patient medical records. The top 1% of predicted risk scores are classified as “risky.” Patients in the risky group had on average 0.35 avoidable hospitalizations in the prior 3 years, versus 0.01 for non-risky patients.

Q: What is the distributional (equity) implication of needs-based matching versus income-assortative matching? A: Estimated risk of avoidable hospitalization and the count of prior avoidable hospitalizations are concentrated in the lower end of the income distribution. Needs-based matching therefore reallocates triage skill toward lower-income patients. Simulating positive assortative matching on patient income and doctor skill — approximating observed inequalities in physical care — produces more avoidable hospitalizations than random assignment, because the most vulnerable patients are often the poorest. Needs-based digital matching can sever the link between local area income and service quality.

Q: How does digital care usage sort by income and demographics in the data? A: At the extensive margin, the deprivation index (Care Need Index) is similar among digital users and non-users in Region Skane. However, at the intensive margin, individuals with a higher deprivation index who use the digital service have more appointments in it; similarly, lower-income users use the service more intensively. Digital care users are younger than non-users and are more likely to live in cities than the average Swedish citizen.

Q: What are avoidable hospitalizations and why are they the primary outcome? A: Avoidable hospitalizations (also called hospitalizations for ambulatory care sensitive conditions) are hospital admissions defined in the medical literature as preventable by adequate and timely primary care. They are coded using ICD-10 diagnosis codes listed in Page et al. (2007). The most common diagnoses in the 90-day post-consultation window are respiratory and genitourinary, conditions commonly treated in digital care. The outcome is rare (0.2% of patients in the sample), but high-stakes: an estimated 1.1 potential life years are lost per avoidable hospitalization, and in Sweden they cost an estimated SEK 7.1 billion (~$820 million) annually (7% of inpatient curative and rehabilitative care costs).

Q: What is the scope of the counter-guideline antibiotic prescription outcome? A: Non-adherence is coded against 16 guidelines from Sweden’s strategic programme against antibiotic resistance (Strama 2017, 2019), all designed to limit or narrow antibiotic use. The measured rate of non-adherence is described as quite low by international standards; the CDC estimates 28% of US antibiotic prescriptions are unnecessary, while the author’s sample rate is 2%. The guidelines require doctors to sometimes refuse patients who request antibiotics, introducing a behavioral compliance dimension to this skill.

Q: What are the costs and feasibility considerations for implementing needs-based digital matching? A: The paper characterizes matching as a “resource-neutral” policy because it reallocates existing doctors without hiring or training. The primary costs are a small increase in waiting time for some patients and the costs of importing data and developing the matching algorithm. Because the algorithm handles patient-doctor allocation while doctors retain all clinical decision-making, the policy functions as a complement to human skill rather than a substitute, which the author argues makes it less subject to “algorithm aversion.”

Q: Why does the paper restrict to each patient’s first digital consultation only? A: The first visit is the one subject to conditional random assignment; subsequent visits could reflect endogenous selection by patients who preferred a particular doctor or outcome. Using only first visits eliminates this concern. The restriction reduces the sample from approximately 378,000 to 210,171 patients (56% of the original), paired with 143 doctors who each had at least 600 randomized consultations.

Conditional random assignment: The allocation mechanism by which patients selecting the “first available doctor” option in digital primary care were assigned to whichever certified doctor was next in the shift roster, conditional on 3-hour shift-by-date strata — a by-product of the first-come-first-served queue rather than an intended experimental design.

Average Match Function (AMF): The conditional mean of a patient outcome given observable doctor type and patient type under random assignment, β(x,w) = E[Y|X=x, W=w], which serves as the building block for evaluating counterfactual reallocation policies.

Average Reallocation Effect (ARE): The difference in expected patient outcomes between a counterfactual doctor-patient assignment and the status quo random assignment, taking into account the externality on the patient from whom a high-skilled doctor is moved.

Task-specific doctor skill: The paper’s finding that primary care physician effectiveness is not governed by a single latent ability but varies across distinct tasks — triage/risk prediction, guideline-consistent prescribing, and minimizing unnecessary follow-up care — with skills across tasks not positively correlated.

Avoidable hospitalization: A hospital admission coded to a diagnosis (per Page et al. 2007 ICD-10 classification) defined in the medical literature as preventable by adequate and timely primary care, used as the primary high-stakes outcome measure (0.2% incidence in the sample within 90 days of a digital consultation).

Counter-guideline prescription: A prescription of an antibiotic in violation of one of 16 guidelines from Sweden’s Strama antibiotic resistance programme, all of which are designed to limit use or require narrower-spectrum first-line antibiotics; used as the primary guideline-adherence outcome (2% incidence in the sample).

Empirical Bayes shrinkage: A procedure applied to raw doctor value-added estimates in which the noisy estimate of doctor quality is multiplied by the ratio of signal variance to total (signal plus noise) variance, yielding a best linear predictor of the underlying doctor random effect and reducing noise from small-sample estimation.

Designing Dynamic Reassignment Mechanisms: Evidence from GP Allocation

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

This paper studies the design of dynamic reassignment mechanisms—centralized systems that must not only provide good initial matches but also accommodate changes in agents’ preferences over time. The empirical setting is Norway’s system for allocating patients to general practitioners (GPs), where every individual is assigned a specific GP whose panel has a binding capacity cap. Since 2016, Norway has allowed patients to join waitlists for oversubscribed GPs while retaining their spot on their current GP’s panel, with reassignment proceeding strictly first-come, first-served (FCFS) as vacancies arise.

The paper makes three contributions. First, it provides direct evidence of unrealized gains from trade: in December 2019, 15 percent of the 133,332 patients then standing on waitlists could have been immediately reassigned via a single run of the Top-Trading Cycles (TTC) algorithm, which identifies not only bilateral swaps but arbitrary cycles. A mechanical simulation holding patient choices fixed shows that running TTC monthly from November 2016 through December 2019 would have left 23 percent fewer patients on waitlists by end-2019, with average waiting times among reassigned patients 29 percent shorter.

Second, the paper introduces a dynamic TTC mechanism and clarifies why static properties do not carry over. In the static case, TTC is both strategy-proof and Pareto-improving (Shapley and Scarf, 1974; Roth, 1982). In a dynamic setting, neither property holds. Repeated TTC is not strategy-proof because patients’ GP choices affect how long they wait. More importantly, TTC may leave some patients worse off: a panel slot that would have gone to the first person on a waitlist under FCFS may instead go to a later-arriving patient who can form a trading cycle, effectively de-prioritizing patients whose GPs are undersubscribed. In the mechanical simulation, 4.5 percent of patients face longer waiting times under TTC.

Third, the paper estimates a structural model of patient attention and GP choice using monthly Norwegian administrative data covering 4.78 million patients and 6,470 GP panels (2014–2019), restricting estimation to the Trondelag region (approximately 8 percent of the country). The model specifies: a Poisson attention process (patients consider switching only when an attention shock arrives); preferences over GPs as a function of travel time, GP fixed effects, and match characteristics; and a belief model mapping observed waitlist lengths into expected waiting times. Parameters are recovered via a Gibbs sampler with Metropolis-Hastings for the discount rate. Key estimates: the annual discount factor is approximately 0.91; a female patient under 45 would travel 7.3 minutes farther to see a female GP (6.3 minutes for a female patient over 45); GP fixed effects have a standard deviation of 31 minutes’ travel-time equivalent; idiosyncratic taste shocks have a standard deviation of 12.6 minutes.

The paper then simulates a stationary equilibrium for each counterfactual mechanism. Under the status quo in stationary equilibrium, 9.4 percent of patients are on a waitlist, 82.2 percent of GPs have a waitlist, and average expected waiting time is 16.7 months. Introducing TTC reduces average waiting time to 14.1 months and raises mean patient welfare by the equivalent of 0.75 minutes’ travel time (more than 13 percent of the gain achievable under a no-capacity-constraints benchmark). Over half of this gain (0.4 minutes) comes directly from patients obtaining geographically closer GPs. Benefits are concentrated among younger patients, female patients, and recent movers; rural patients gain 2.1 minutes. However, patients with undersubscribed GPs face waiting times that rise from 16.7 to 22.8 months and are worse off by the perpetuity equivalent of 0.8 minutes.

Two modified mechanisms are evaluated. Deferred Acceptance (DA), which strictly respects FCFS priority, achieves essentially no improvement over the status quo, illustrating a fundamental trade-off between eliminating envy and exploiting gains from trade. A “TTC with Priority” (TTCP) mechanism, which gives priority for panel vacancies to patients with undersubscribed GPs before running TTC, achieves 61 percent of TTC’s welfare gains (0.46 minutes flow payoff; 1.08 minutes NPV) while leaving patients with undersubscribed GPs no worse off than under the status quo. A benchmark simulation eliminating waitlists altogether raises mean welfare slightly (0.19 minutes) but lowers median welfare (−0.60 minutes), with gains concentrated among highly mismatched patients.

Q: What is the core market failure the paper documents? A: Norway’s waitlist mechanism assigns panel vacancies strictly first-come, first-served without allowing patients to trade. This creates a “double coincidence of wants” problem: patients can simultaneously be on each other’s waitlists but cannot swap. In December 2019, 15 percent of 133,332 waiting patients could have been immediately reassigned via a single TTC run. A mechanical simulation shows that monthly TTC would have left 23 percent fewer patients on waitlists by end-2019 and reduced average realized waiting times among reassigned patients by 29 percent.

Q: Why does TTC fail to be strategy-proof in a dynamic setting? A: In the static case, TTC gives every agent an assignment at least as good as their endowment, making truthful reporting a dominant strategy. In a dynamic setting, a patient’s choice of GP determines not only which GP they receive but also how long they wait — patients who choose less-demanded GPs reach the front of the waitlist faster. This creates incentives to misreport preferences strategically, breaking strategy-proofness. The paper shows this formally and builds it into the equilibrium model by requiring patients to optimize over both GP choice and expected waiting time.

Q: Why does dynamic TTC harm some patients relative to the status quo? A: Under FCFS, the first person on a waitlist is guaranteed the next available slot on the target GP’s panel. Under TTC, a patient who arrived later but whose current GP is oversubscribed can form a trading cycle that redirects that slot, effectively jumping the queue. Patients with undersubscribed GPs — whose panel endowment is not a scarce resource that others want — cannot form cycles and are systematically de-prioritized. In the stationary equilibrium, their expected waiting time rises from 16.7 to 22.8 months, and they are worse off by the perpetuity equivalent of 0.8 minutes’ travel time.

Q: What are the main parameter estimates and what do they imply? A: The annual discount factor is estimated at approximately 0.91 once GP fixed effects are included (rising to near 0.95 without them, because more desirable GPs have longer waitlists). Gender homophily is worth 6.3–7.3 minutes of travel time for female patients under 45. Age homophily is worth approximately 1 minute. The standard deviation of GP fixed effects is 31 minutes and idiosyncratic shocks are 12.6 minutes, both in travel-time equivalents, indicating substantial horizontal differentiation across GPs and across patients’ idiosyncratic tastes.

Q: How important are moves as a driver of GP switching? A: Moves are the dominant driver. Among non-movers, older men consider switching just once every 25 years; temporary residents consider switching approximately once every 7.5 years (1.084 percent per month). Among patients who moved more than 30 minutes, a temporary resident has an 18.59 percent monthly probability of considering switching in the month of or month after the move. For a permanent resident making a long-distance move, the cumulative attention probability over the 8 months surrounding the move rises to 34 percent (versus 22 percent for a short-distance move). In the data, 26 percent of waitlist users moved municipality during 2017–2019, versus 6 percent of non-switchers.

Q: What does the stationary equilibrium under the status quo look like? A: In the long-run stationary equilibrium, 9.4 percent of patients are on a waitlist, 82.2 percent of GPs have a waitlist, and the average expected waiting time to switch GPs is 16.7 months. Each month, 2,299 patients on average draw attention shocks; 85.2 percent of these choose to join a waitlist, while the remainder either switch to an open GP or stay with their current GP. The average attentive patient expects to successfully obtain their chosen GP after 16.8 months.

Q: What are the distributional consequences of TTC across patient subgroups? A: Female patients benefit especially because they are more likely to be attentive (and thus use waitlists) than males. Recent movers gain 2.3 minutes’ travel-time equivalent. Patients who have never moved still gain 1.0 minutes. Rural patients gain 2.1 minutes (larger than average), reflecting their longer baseline travel times and greater geographic mismatch potential. Urban patients also benefit but less so. The one group that is harmed is patients with undersubscribed GPs, who face longer waits and a welfare loss of 0.8 minutes perpetuity equivalent.

Q: Why does the Deferred Acceptance mechanism fail to improve on the status quo? A: DA strictly respects FCFS waiting-time priority: no patient may be reassigned to a GP for whom another patient has been waiting longer. This means DA can only execute swaps in which all patients ahead of each participant on their respective waitlists are also reassigned in the same month. In practice, this virtually never occurs, so DA reassigns almost no patients earlier than the status quo Waitlists mechanism. The result illustrates a fundamental trade-off: fully respecting FCFS priority eliminates nearly all gains from trade.

Q: How does TTCP restore fairness while preserving most of the efficiency gains? A: TTCP modifies TTC by prioritizing patients with undersubscribed GPs over those with oversubscribed GPs when assigning panel vacancies, while still respecting the constraint that patients cannot be assigned a GP they prefer less than their current one. This gives patients with undersubscribed GPs a compensating advantage in the queue that offsets their inability to trade via cycles. TTCP achieves 0.46 minutes’ mean flow payoff improvement versus 0.75 for TTC (61 percent of TTC’s gains), and an NPV measure of 1.08 minutes versus 1.25 for TTC. Patients with undersubscribed GPs are left no worse off than under the status quo.

Q: What happens when waitlists are eliminated entirely? A: Under No Waitlists, attentive patients may only choose among GPs with open panels at the moment of attention. Mean welfare rises slightly (0.19 minutes) because patients spend less time mismatched while waiting, but median welfare falls by 0.60 minutes. The gains are concentrated among a minority of highly mismatched patients who prefer limited choice with no waiting over broader choice with long waits, while most patients prefer the option to wait for a more preferred GP. The authors note this may partly explain why formal waitlists are rare in other primary care systems.

Q: What is the welfare benchmark and how large are the gains? A: The benchmark is a “No Caps” scenario in which all panel caps are removed, representing the maximum achievable improvement. The mean welfare gain from TTC (0.75 minutes) represents more than 13 percent of this upper bound. The “Truthful TTC” benchmark, where patients submit full preference lists, yields 1.04 minutes, but its gains are also concentrated: the median patient is no better off than under the status quo Waitlists mechanism.

Q: What are the scope conditions for these findings? A: The demand model is estimated on the Trondelag region of Norway (approximately 8 percent of the national population) over 2017–2019, a period when waitlists were growing rapidly rather than in steady state. Counterfactual comparisons are made in a stationary equilibrium calibrated to Trondelag. The model excludes patients under 16 (whose enrollment is managed by parents). The partially capitated payment structure and fixed panel caps are institutional features specific to Norway, though similar systems exist in Canada, the UK, Italy, and Sweden. GP characteristics are held fixed in the model. The analysis abstracts from health outcomes, focusing on preference-based welfare from GP assignment.

Top-Trading Cycles (TTC) algorithm: A centralized reassignment algorithm that takes agents’ preference lists and objects’ priority lists as inputs, has each agent “point to” their preferred object and each object “point to” their highest-priority current or waiting agent, identifies cycles of mutual pointing, and executes the trades in those cycles simultaneously. In the paper’s static application, TTC is both Pareto-improving (every participant receives an assignment at least as good as their endowment) and strategy-proof. In the dynamic setting studied here, neither property holds.

Dynamic TTC mechanism: A mechanism that runs the TTC algorithm repeatedly at the end of each period after naturally arising vacancies have been filled from waitlists. Because patients’ GP choices affect how long they wait — not only which GP they receive — this mechanism is not strategy-proof and may leave patients with undersubscribed GPs worse off than under strictly FCFS waitlists.

TTC with Priority (TTCP): A modified version of dynamic TTC that changes the priority ordering so that patients with undersubscribed current GPs are prioritized above patients with oversubscribed GPs when panel vacancies are allocated. This modification preserves patients’ endowment rights but compensates the group harmed by standard TTC. In the paper’s simulations, TTCP achieves 61 percent of TTC’s mean welfare gains while leaving patients with undersubscribed GPs no worse off than under the status quo.

Patient attention model: A model in which patients consider switching GPs only when they receive a Poisson-distributed attention shock. Attention rates vary by observable characteristics (age, gender, temporary vs. permanent residency, whether and how far the patient recently moved). The model interprets any switch request as evidence of both an attention shock and a preference for the requested GP over the current one. Patients who do not request switches may be either inattentive or attentive but satisfied.

Horizontal differentiation (GP preference heterogeneity): The extent to which different patients prefer different GPs for reasons unrelated to overall GP quality — primarily driven by geographic proximity, gender homophily (worth 6.3–7.3 travel-time-equivalent minutes for young female patients), and age similarity (approximately 1 minute). Horizontal differentiation is the fundamental source of gains from trade: if all patients preferred the same GP, there would be no mutual-benefit swaps to find.

Deferred Acceptance (DA) algorithm: The patient-proposing DA algorithm, which strictly respects FCFS waiting-time priority: no patient may be reassigned ahead of another patient who has been waiting longer for the same GP. In the dynamic context, DA achieves essentially no welfare improvement over the status quo because its strict respect for priority eliminates nearly all trading opportunities, illustrating the trade-off between envy-freeness and efficiency.

Double coincidence of wants: The situation in which two (or more) patients are simultaneously on each other’s waitlists and would mutually benefit from trading GP assignments, but cannot do so under the current mechanism because there is no vacancy on either panel. The paper’s direct evidence of this phenomenon — 15 percent of waiters could be immediately reassigned via one TTC run — motivates the counterfactual analysis.

Do Credit Conditions Move House Prices?

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

Overview

Research Question. To what extent did an expansion and contraction of credit drive the 2000s housing boom and bust? The existing literature offers sharply divergent answers — ranging from credit explaining virtually none of the boom (Kaplan, Mitman, and Violante 2020) to credit explaining the majority of it (Favilukis, Ludvigson, and Van Nieuwerburgh 2017, who find credit alone explains 60% of the rise in price-to-rent ratios). Greenwald and Guren argue that the source of these divergent findings is a single structural assumption: the degree to which credit-insensitive agents (landlords and unconstrained savers) can absorb credit-driven demand for housing, which in turn depends on the degree of segmentation between the owner-occupied and rental housing markets.

Key Mechanism. The paper organizes the literature around a “tenure supply” curve, defined in price-rent ratio versus homeownership rate space. A perfectly inelastic (vertical) supply curve — corresponding to perfect segmentation, in which housing cannot move between the owner-occupied and rental sectors — implies that credit expansion bids up house prices with no change in the homeownership rate. A perfectly elastic (horizontal) supply curve — corresponding to a frictionless rental market with deep-pocketed landlords who price at the present value of rents — implies that credit expansion raises the homeownership rate but not the price-rent ratio, because landlord reservation prices are unaffected by credit. Intermediate degrees of segmentation produce intermediate outcomes: credit raises both the price-rent ratio and the homeownership rate, with the relative magnitudes determined by the slope of the tenure supply curve.

Empirical Strategy. To measure where reality falls on this spectrum, the authors estimate the relative elasticity of the price-rent ratio to an identified credit supply shock, compared to the elasticity of the homeownership rate to the same shock. This ratio is a sufficient statistic for the slope of the tenure supply curve. They use three distinct identification strategies from prior literature — (1) Loutskina and Strahan (2015), instrumenting for local credit supply using differential city-level exposure to changes in the conforming loan limit (CLL); (2) Di Maggio and Kermani (2017), exploiting the 2004 OCC preemption of state anti-predatory-lending laws for national banks; and (3) Mian and Sufi (2019), using differential city-level exposure to the 2003 private label securitization (PLS) expansion through bank funding composition. Regressions are estimated on annual CBSA-level panels using local projection IV (LP-IV) or event-study reduced-form methods. Key data include the CoreLogic repeat-sales house price index, the CBRE Torto-Wheaton same-store rent index (a repeat-rent index for multi-unit apartment buildings, constructed from newly-leased units), and Census Housing Vacancy Survey homeownership rates.

Main Empirical Findings. All three instruments consistently find that credit supply shocks generate a significant increase in house prices and the price-rent ratio but a much smaller, rarely statistically significant, effect on the homeownership rate. Under the LS LP-IV, the price-rent ratio peaks at an increase of 0.471, while the homeownership rate response reaches only 0.037 at the 2-year horizon and peaks at 0.101 after 5 years. The ratio of price-rent to homeownership responses ranges from 3 to infinity across the three instruments and horizons. These estimates imply a substantial degree of segmentation — the no-segmentation model falls far outside the 95% confidence intervals at all horizons.

Structural Model and Calibration. The authors construct a general equilibrium model featuring a representative borrower, landlord, and saver, with long-term fixed-rate mortgages subject to loan-to-value (LTV) and payment-to-income (PTI) limits following Greenwald (2018). The key modeling innovation is within-type heterogeneity in the benefit of owning versus renting, captured by logistic distributions for both borrowers and landlords. The dispersion parameter of the landlord distribution (σω,L) governs the slope of the tenure supply curve and is calibrated to minimize weighted distance to the LS empirical impulse responses. The resulting benchmark calibration yields σω,L = 2.877, with the benchmark model’s price-rent-to-homeownership ratio between 6.98 and 9.31 depending on the horizon — consistent with the empirical estimates.

Quantitative Results on the 2000s Boom. The paper then uses the calibrated model to simulate a credit standard relaxation (LTV limits relaxed from 85% to 99%, PTI limits from 36% to 65%) from 1998 Q1 through 2007 Q1, with a reversion at the start of the bust. This credit relaxation alone explains 34% of the peak rise in price-rent ratios observed in the boom, with a lower bound of 26% accounting for parameter uncertainty. In contrast, the no-segmentation model explains -1%, while the full segmentation model explains 38%. Adding a 2 percentage point permanent decline in mortgage spreads alongside the credit standard relaxation allows the benchmark model to explain 72% of the observed rise in price-rent ratios and 80% of the rise in loan-to-income ratios, compared to only 4% in the no-segmentation model. In a “full boom” scenario where additional demand and supply shocks are added to match the entire boom in price-rent ratios and homeownership, removing the credit relaxation reduces the rise in price-rent ratios by 55% in the benchmark economy — larger than the 34% explained in isolation due to nonlinear interactions — compared to only 5% in the no-segmentation economy.

Scope Conditions and Extensions. These results apply to the benchmark calibration in which landlords do not use credit and saver housing demand is fixed. When landlords are allowed to use credit (LTV limit of 65% relaxed to 85% during the boom), the role of credit is strengthened: the recalibrated model explains 80% of the rise in price-rent ratios from combined credit and rate changes, suggesting the benchmark is a lower bound. When savers are allowed to frictionlessly trade housing with borrowers, credit explains 54% of the rise in price-rent ratios even after recalibration — a roughly 25% reduction relative to the benchmark 72%, representing what the authors characterize as an extreme lower bound given that saver housing markets are in practice substantially segmented due to indivisibility, quality, and location differences.

Policy Implications. The findings imply that macroprudential policies tightening LTV and PTI ratios can be effective at restraining house price growth, but only in the presence of the significant rental market segmentation found in the benchmark economy. In the no-segmentation economy, removing the credit relaxation from the full boom reduces price-rent ratio growth by only 5%.

In depth

Q1. What is the core theoretical insight that reconciles the divergent findings in the prior literature on credit and house prices?

The key difference is the degree to which credit-insensitive agents — specifically landlords and unconstrained savers — can absorb credit-driven demand for housing. Models with perfectly segmented rental markets (no rental sector or fixed homeownership rate) feature borrowers competing only with each other for a fixed stock, so credit expansion bids up prices. Models with frictionless rental markets feature deep-pocketed landlords who supply housing at a price equal to the present value of rents, which is unaffected by credit; credit expansion then raises the homeownership rate rather than prices. Intermediate degrees of frictions produce intermediate outcomes. This mechanism had not been recognized as the source of the literature’s divergence before this paper.

Q2. What is the “tenure supply curve” and why is its slope the key empirical object?

The tenure supply curve describes the menu of price-rent ratios at which landlords are willing to supply varying amounts of owner-occupied housing (given total housing stock), traced out in price-rent ratio versus homeownership rate space. Its slope determines how the equilibrium responds to a credit-induced demand shift: a steep (inelastic) supply curve translates credit expansion primarily into price-rent ratio increases; a flat (elastic) supply curve translates it primarily into homeownership rate increases. Identifying this slope empirically is therefore sufficient to discipline any macro-housing model’s predictions about the role of credit in price dynamics, for arbitrary underlying shocks.

Q3. How do the authors identify the slope of the tenure supply curve empirically?

They estimate the slope as the ratio of the causal elasticity of the price-rent ratio to that of the homeownership rate, with respect to an identified credit supply shock. Three instruments are used: (1) the Loutskina-Strahan shift-share instrument based on differential exposure to changes in the conforming loan limit, estimated by LP-IV on an unbalanced panel of 62 CBSAs from 1992 to 2016; (2) the Di Maggio-Kermani event study based on the 2004 OCC preemption of state anti-predatory-lending laws, covering 262 CBSAs for house prices and 82 CBSAs for homeownership from 2001 to 2010; and (3) the Mian-Sufi event study based on differential exposure to the 2003 PLS expansion via non-core deposit share, covering 245 CBSAs using ACS and FHFA data. In practice, they estimate the inverse slope (ratio of homeownership to price-rent response) because the first stage is far stronger using price-rent ratios as the endogenous variable.

Q4. What are the empirical results on the relative price-rent and homeownership responses?

Across all three instruments, credit supply shocks significantly raise the price-rent ratio but have a much smaller, rarely statistically significant effect on the homeownership rate. Under the LS LP-IV, the price-rent ratio peaks at 0.471 after 2 years, while the homeownership rate reaches only 0.037 at 2 years and peaks at 0.101 at 5 years. The naive point-estimate ratios range from 2.93 to 12.83 at horizons 2 through 5, with the 4-year estimate negative (implying an infinite slope). The directly estimated inverse slope coefficients are small (0.05 to 0.24) and never statistically different from zero. The DK instrument yields slopes of 6.72 in 2005, 3.67 in 2006, and 3.40 in 2007. The MS instrument yields a slope of approximately 4.49 in both 2006 and 2007. The lower bound of the 95% confidence intervals corresponds to slopes of at least 1.8 to 8.4.

Q5. What is the key modeling contribution on the structural side?

The key innovation is the introduction of within-type heterogeneity in ownership preferences for both borrowers and landlords, modeled as logistic distributions. This heterogeneity allows the model to generate a fractional and time-varying homeownership rate — a feature absent from most prior macro-housing models — and maps directly into the slopes of the demand and tenure supply curves. The dispersion in landlord ownership costs (σω,L) governs the supply curve slope and is calibrated to match the empirical impulse responses. Without this heterogeneity, the model would produce corner solutions with all housing owned by one type.

Q6. How is the landlord dispersion parameter σω,L calibrated, and what is the estimated value?

The calibration minimizes a weighted sum of squared deviations between model and data impulse responses for the price-rent ratio and homeownership rate, using the LS LP-IV estimates. Deviations are weighted by the inverse of empirical standard errors. Because model impulse responses jump on impact while empirical responses are hump-shaped (due to search frictions), the calibration uses only horizons 2 through 5 years. The minimum-distance estimate yields σω,L = 2.877, alongside a mortgage spread shock persistence of 0.965 and a shock size of -0.041 (corresponding to an annualized CLL subsidy of approximately 17 basis points, within the 10-24bp range found in prior literature). The benchmark model’s implied price-rent-to-homeownership response ratio ranges from 6.98 to 9.31, consistent with the empirical estimates.

Q7. What lower bound does the paper derive for σω,L, and how does the no-segmentation model compare?

A credible set for σω,L is derived by targeting the upper and lower bounds of the 95% confidence interval for the estimated inverse slope. The lower bound for σω,L (targeting the top of the confidence interval) is 0.810; the lower bound targets the bottom of the confidence interval but is best matched by the full segmentation case (σω,L → ∞). The no-segmentation economy (σω,L = 0) produces inverse ratios between 4 and 32 times the empirical upper bound, placing it far outside the credible set.

Q8. What is the model’s quantitative finding on the role of credit standard relaxation in isolation?

A credit standard relaxation (LTV from 85% to 99%, PTI from 36% to 65%) implemented from 1998 Q1 to 2007 Q1 and then reverted explains 34% of the peak rise in price-rent ratios in the benchmark model, with a lower bound of 26% conditional on parameter uncertainty. In the full segmentation model, the same relaxation explains 38%, while in the no-segmentation model it explains -1%. Credit standard relaxation also explains 51% of the rise in loan-to-income ratios in the benchmark, compared to 31% in the no-segmentation model.

Q9. What does adding a decline in mortgage rates contribute?

Adding a permanent 2 percentage point decline in mortgage spreads alongside the credit standard relaxation increases the benchmark model’s explained share of the price-rent ratio boom from 34% to 72%, and the loan-to-income ratio share from 51% to 80%. The no-segmentation model explains only 4% of the price-rent ratio boom and 38% of the loan-to-income ratio boom under the same combined experiment.

Q10. How does the “full boom” counterfactual estimate the marginal contribution of credit?

The full boom experiment adds exogenous demand shocks (shifts to µω,B) and supply shocks (shifts to µω,L) on top of the credit relaxation and rate decline, calibrated to exactly reproduce the observed peak increase in both the price-rent ratio and the homeownership rate during the boom. Removing the credit relaxation from this full boom scenario reduces the rise in price-rent ratios by 55% and the rise in loan-to-income ratios by 74% in the benchmark economy. This exceeds the 34% figure from the credit-alone experiment due to strong nonlinear interactions: without the credit relaxation, binding PTI limits constrain households’ ability to finance properties even when ownership preferences rise, dampening both price and credit growth. In the no-segmentation economy, removing the credit relaxation reduces price-rent ratio growth by only 5%.

Q11. What are the implications of allowing landlords to use credit?

When landlords face an LTV limit of 65% relaxed to 85% during the boom, the credit expansion also shifts the tenure supply curve upward (as in Panel (d) of the supply-demand framework), leading to a larger price-rent ratio response and a smaller homeownership rate response than in the baseline. Without recalibration, this model explains 81% of the price-rent ratio rise. After recalibration of σω,L (which is required because landlord credit changes the mapping from empirical moments to structural parameters), the model explains 80% of the price-rent ratio rise. This implies the benchmark results are a lower bound on the role of credit in driving house prices.

Q12. What are the implications of allowing savers to frictionlessly trade housing with borrowers?

When savers are allowed to frictionlessly adjust their housing demand (purchasing housing from or selling to borrowers as credit conditions change), the price-rent ratio response is dampened because savers absorb excess borrower demand. After recalibrating σω,L, the combined credit-and-rate experiment explains 54% of the price-rent ratio boom — roughly 25% less than the benchmark 72%. The authors regard this as an extreme lower bound because in practice saver and borrower housing markets are substantially segmented due to indivisibility, location, and quality differences.

Q13. What are the implications for macroprudential policy?

Macroprudential policies that tighten LTV and PTI limits are effective at slowing house price growth in the benchmark economy, where rental market frictions are substantial. In the full boom counterfactual, tightening credit standards reduces the rise in price-rent ratios by 55%. However, in the no-segmentation economy, the same tightening reduces price-rent ratio growth by only 5%, because landlords readily absorb credit-driven demand and pin prices to the present value of rents. The effectiveness of macroprudential policies is therefore deeply dependent on the degree of rental market segmentation.

Q14. Why do the authors prefer the CBRE Torto-Wheaton rent index over typical rent measures?

The TW index uses a repeat-rent methodology on newly-leased multi-unit apartments, which better captures current market conditions than median rent measures, which are biased by composition changes and are sticky due to long-term lease contracts. Since the price-rent ratio is meant to capture the rent a unit could command if leased instead of sold, newly-leased apartment rents are more appropriate for constructing this ratio. The TW index is available for 53 CBSAs from 1989 and 62 CBSAs from 1994.

Q15. Why do the authors estimate the inverse slope rather than the slope directly?

The first stage for the homeownership rate response is very weak — the estimated coefficients are small and imprecise, so using the homeownership rate as an endogenous variable would suffer severe weak instrument problems. Instead, the authors use the price-rent ratio as the endogenous variable (with a much stronger first stage) and the homeownership rate as the outcome, obtaining the inverse slope (homeownership response per unit price-rent ratio response). The upper bounds of the 95% confidence intervals for the inverse slope range from 0.12 to 0.56 across horizons, corresponding to lower bounds on the slope of 1.8 to 8.4.

Key Concepts

Tenure Supply Curve. The menu of price-rent ratios at which landlords are willing to supply varying quantities of owner-occupied housing (i.e., sell rental units to potential homeowners) at a given total housing stock. Defined in price-rent ratio versus homeownership rate space. Distinct from the absolute supply of housing via the construction sector; shifts in the construction margin affect absolute quantities and prices but not necessarily the price-rent ratio or the ownership share. The slope of this curve — not the level — is the central empirical and structural object of the paper.

Market Segmentation (in the paper’s sense). The degree to which credit-insensitive agents (landlords, unconstrained savers) cannot absorb credit-driven demand from constrained borrowers. Perfect segmentation means owner-occupied and rental housing are entirely non-fungible, so all credit-driven demand falls on a fixed supply of owned units. Zero segmentation means landlords (or savers) can frictionlessly convert between owned and rented housing at a price tied to present discounted rents. In this paper, segmentation is measured continuously by the slope of the tenure supply curve.

Sufficient Statistic (for segmentation). The ratio of the causal elasticity of the price-rent ratio to the causal elasticity of the homeownership rate, both with respect to the same identified credit supply shock. This ratio identifies the slope of the tenure supply curve and is sufficient to calibrate a structural model to recover the role of credit in driving house prices for arbitrary combinations of shocks, even when those shocks differ from the identifying variation.

Ownership Benefit Heterogeneity. An additional idiosyncratic utility flow (positive or negative) that borrowers or landlords receive from owning versus renting a given unit, modeled as a logistic distribution. This within-type heterogeneity generates a fractional and time-varying homeownership rate in the model and maps directly into the slope of the demand and tenure supply curves. The dispersion parameter σω,L for landlords governs the slope of the tenure supply curve; higher dispersion implies a steeper (more segmented) supply curve and larger price-rent ratio responses to credit shocks.

Marginal Collateral Value (CB,t). The shadow value to borrowers of the additional credit that can be collateralized by an additional dollar of housing value, equal to µB,t × FLTV × θLTV in the model. A relaxation of credit standards (raising θLTV or θPTI) or a decline in credit costs raises CB,t, increasing borrower reservation prices and shifting the housing demand curve outward. This is the channel through which credit conditions enter house price dynamics.

Local Projection IV (LP-IV). A generalization of Jordà (2005) local projections to instrumental variables settings, as in Ramey (2016) and Ramey and Zubairy (2018), extended to a panel context with CBSA and time fixed effects. Used to estimate impulse responses of price-rent ratios, house prices, and homeownership rates to credit supply shocks at horizons 0 through 5 years, instrumenting for endogenous credit growth using the conforming loan limit shift-share instrument.

Conforming Loan Limit (CLL) Instrument. A shift-share instrument for local credit supply constructed by interacting the share of mortgage originations in the prior year falling within 5% of the current year’s CLL with the percentage change in the national CLL. Cities where a larger fraction of loans cluster near the CLL threshold experience a larger credit supply shock when the CLL increases, because more loans shift from unsubsidized to GSE-subsidized rates. The instrument is constructed using the change in the national CLL only to avoid endogeneity from high-cost area adjustments.

Downward Rigidity in the Wage for New Hires

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

Layer 1 — Summary

Hazell and Taska use wages posted on online job vacancies — matched to job titles and establishment identifiers from Burning Glass Technologies — to measure the wage for new hires at the job level (same job title and establishment) over 2010Q1–2020Q2. They find that this measure of the wage for new hires is rigid downward and flexible upward. At the job level, the nominal posted wage changes infrequently — on average once every 5–6 quarters — and conditional on changing, is four times more likely to rise than to fall. In the cyclical dimension, job-level posted wages rise strongly when state unemployment falls but do not fall when state unemployment rises; real wages exhibit the same asymmetric pattern. These results do not appear in the average wage for new hires (which aggregates across all job types), because time-varying job composition inflates the variance of average wages and raises standard errors roughly twentyfold relative to job-level regressions — explaining why prior work using worker-level survey data found no evidence of downward rigidity. A Heckman (1979) selection correction for firms’ selection into vacancy posting suggests that selection bias in the job-level regression is moderate. The findings provide direct empirical support for models in which downward wage rigidity for new hires — specifically at the job level — amplifies unemployment fluctuations and generates asymmetric unemployment dynamics.

In depth

Q1. Q: What is the central empirical claim of the paper?

A: At the job level — defined as the same job title within the same establishment — the wage posted for new hires is rigid downward and flexible upward. It changes infrequently and, conditional on changing, rises far more often than it falls; and it responds to falls in unemployment but not to rises in unemployment.

Q2. Q: What data does the paper use, and what defines a “job”?

A: The paper uses the Burning Glass Technologies dataset of wages posted on online vacancies, covering January 2010 to June 2020. A “job” is a job title within an establishment whose wages are paid at a given frequency (e.g., hourly or annual). The data come from the near-universe of online job postings — roughly 40,000 sources — and the main regression sample consists of jobs that post wages, have job title and establishment information, and post vacancies in multiple quarters, yielding approximately 3.05 million vacancies, representing about 0.8% of total US vacancies.

Q3. Q: How do the authors validate that posted wages measure the wage for new hires?

A: They construct a measure of the wage for new hires from the Current Population Survey (CPS) — workers switching jobs or entering from unemployment — at the state, industry, and occupation level. Regressing log CPS wages on log Burning Glass wages (using an IV split-sample procedure to correct for attenuation bias) yields a coefficient close to 1 across specifications and levels of aggregation, indicating that average posted wages move roughly one-for-one with average wages for new hires in representative survey data.

Q4. Q: How is the frequency of wage change estimated?

A: Because wages are not observed in quarters without a vacancy posting, the authors adapt a constant-hazard model from the price-setting literature (following Nakamura–Steinsson and Klenow–Kryvtsov). The latent wage evolves stochastically between postings; the observed wage is treated as a draw from this process. The quarterly probability of wage change is estimated at 0.17–0.19 across specifications, implying implied durations of unchanged wages of 4–5 quarters.

Q5. Q: What is the asymmetry in the direction of wage changes?

A: In the unweighted baseline, the quarterly probability of a wage decrease is 0.04, whereas the probability of a wage increase is 0.12 — roughly a three-to-one ratio in probabilities, summarized in the paper’s abstract as wages being “four times more likely to rise than to fall.” The distribution of non-zero wage changes also shows a pronounced pile-up of small positive changes relative to small negative changes, consistent with a downward constraint on wage setting.

Q6. Q: What is the first piece of cyclical evidence for downward rigidity?

A: A binned scatterplot (Figure 1) of job-level wage growth against state-level quarterly changes in unemployment shows a strong, roughly linear relationship when unemployment is falling — wages rise with falls in unemployment, both for small and large declines. When unemployment rises, however, wages do not fall — neither for small nor for large increases in unemployment. This asymmetry is robust to regression-based analysis and to identified labor demand shocks.

Q7. Q: Are real wages also rigid downward?

A: Yes. The paper reports that real wages (nominal posted wages deflated) are also rigid downward and flexible upward, mirroring the pattern for nominal wages.

Q8. Q: What is the job-composition problem, and why does it matter?

A: The average wage for new hires — the object measured in most prior work — aggregates across all job types that are actively hiring. If the composition of jobs hiring shifts over the business cycle (e.g., the share of lower-wage jobs rises in recessions), then average wages can fall even if no individual job cuts its wage, and can stay flat or rise even if every job cuts its wage. Job composition therefore confounds cyclicality estimates based on average wages. By tracking the same job title at the same establishment across successive vacancies, the authors purge wage changes driven by shifting composition.

Q9. Q: Why did prior work find no evidence of downward rigidity for new hires?

A: Prior work used worker-level survey data (e.g., Bils 1985; Pissarides 2009 survey) that controls for worker characteristics but averages across jobs — the average wage for new hires. The volatility of job composition inflates the variance of this average measure. In the Burning Glass data, standard errors from regressions using average wages are roughly twenty times larger than those from job-level regressions, making it impossible to detect downward rigidity even if it exists. Point estimates in prior work suggested procyclicality but were too imprecise to exclude downward rigidity.

Q10. Q: How does this paper relate to Gertler, Huckfeldt, and Trigari (2020) and Grigsby, Hurst, and Yildirmaz (2021)?

A: Both papers attempt to control for job composition at the worker level. Gertler et al. focus on wages of workers hired from unemployment (less affected by composition than all new hires) and find weakly procyclical wages. Grigsby et al. use rich payroll data and worker-level matching to control for composition and also find weakly procyclical wages. The present paper complements these by using job-level data that directly purges composition without relying on worker characteristics, and adds evidence on the asymmetry of rigidity (not just average procyclicality).

Q11. Q: What is the role of the Heckman selection correction?

A: If firms select into vacancy posting depending on business-cycle conditions, the sample of observed posted wages may be non-random, biasing job-level wage-cyclicality estimates. The authors implement a standard Heckman (1979) two-step selection correction. The correction suggests that selection bias in the job-level regression is moderate — it does not overturn the finding of downward rigidity.

Q12. Q: What are the four main caveats the authors acknowledge?

A: (1) The main sample is small — 0.8% of US vacancies — though the authors show it is broadly representative on observables and that wages track representative survey data. (2) The paper measures rigidity only for jobs that post wages; jobs that do not post wages might be more flexible, though the share of vacancies posting wages does not decline during contractions. (3) Posted wages may differ from realized (bargained) wages; however, wages are rigid even in occupations where bargaining is uncommon. (4) The Pandemic Recession is the main contractionary episode in the sample, and it involved labor supply shocks as well as demand shocks; the authors address this through identified labor demand shock regressions and by ending the sample in June 2020.

Q13. Q: What are the implications for models of unemployment fluctuations?

A: In the Diamond–Mortensen–Pissarides search model, Pissarides (2009) emphasizes that the wage for newly hired workers — not continuing workers — is the relevant margin for unemployment fluctuations. Shimer (2005) showed the standard calibration produces too-small unemployment fluctuations; wage rigidity for new hires can resolve this. The paper’s finding of downward-but-not-upward rigidity additionally supports models (e.g., Dupraz, Nakamura, and Steinsson, 2020) in which this asymmetry generates asymmetric unemployment dynamics — unemployment rises sharply in contractions but falls more slowly in expansions.

Q14. Q: How do wages for new hires compare with wages for continuing workers in terms of rigidity?

A: The paper finds approximate parity. The implied duration of unchanged wages from the job-level posted wage data (4–5 quarters) is similar to estimates for continuing workers in the prior literature. This is perhaps surprising because wages could in principle be more flexible for new hires than continuing workers — firms might cut wages for new hires even while insuring continuing workers (Beaudry and DiNardo, 1991). The results instead suggest that internal equity concerns (Bewley, 2002) or other forces produce similar rigidity for both groups.

Key Concepts

Job level wage: The wage across successive vacancies posted by the same job title at the same establishment. This is the unit of observation in the paper’s main analysis and the object for which downward rigidity is documented. Distinct from the average wage for new hires (which aggregates across all job types).

Downward rigidity (as used in this paper): An empirical pattern in which wages at the job level do not fall during contractions — they do not respond to rising unemployment — while rising during expansions in response to falling unemployment. The claim is descriptive: the data show wages do not fall; the paper does not structurally identify the mechanism enforcing this floor.

Job composition problem: The bias introduced when measuring cyclicality of the average wage for new hires using data that aggregates across different types of jobs. If the mix of job types hiring shifts with the business cycle, average wages can change even when no individual job changes its wage, and can mask individual-job wage changes. Job-level data resolve this by holding the job fixed.

Burning Glass Technologies dataset: A database of wages posted on online job vacancies, drawn from approximately 40,000 online sources (job boards and company websites), covering the near-universe of US online vacancies. The paper’s main regression sample uses the subset with posted wages, job title, establishment identifiers, and multiple quarters of postings, spanning January 2010 to June 2020.

Constant hazard model (wage change frequency): An estimation procedure adapted from the price-setting literature to recover the quarterly probability of wage change from a dataset in which wages are only observed when a vacancy is posted. The latent wage evolves with a constant hazard of change between observations; observed wage changes identify the hazard rates for increases and decreases separately.

Average wage for new hires: The mean wage across all workers newly entering employment (or across all new-hire jobs), used in prior work (Bils 1985 and related). Does not control for job composition. Shown in this paper to exhibit no detectable downward rigidity, with standard errors roughly twenty times larger than in job-level specifications — because job composition variance inflates the residual variance.

Heckman selection correction: A two-step procedure (Heckman 1979) to correct for the possibility that firms that post vacancies — and post wages — are a selected sample that differs systematically across the business cycle. The paper applies this to assess whether selection into vacancy posting biases the job-level wage-cyclicality estimates; the correction suggests bias is moderate.

Summary based on LSE Research Online accepted version (accepted manuscript, covers full paper including introduction, data, and Section 3; extraction terminated at line 595 before Sections 4–5). AI-assisted, human review pending.

Dynamics of the Long-Term Housing Yield: Evidence from Natural Experiments

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

Each month a fraction of UK property leases are extended by 90 years or more, creating thousands of natural experiments in which the same property’s rent and capital value are revealed simultaneously. This paper uses these lease extensions — and Massachusetts and Cambridge rent-control removals as a second identification strategy — to estimate the expected long-term housing yield (annual rent-to-price ratio) and decompose its dynamics into rent-growth expectations and discount-rate components. The central finding is that housing yield movements are dominated by discount-rate shocks: variation in required returns on housing explains the overwhelming majority of yield variance, while expected rent growth contributes less than 10 percent. Housing booms are therefore primarily driven by falling required returns, not by rational expectations of higher future rents. The yield responds to real long-term interest rates with a slope significantly below one, consistent with a non-pecuniary convenience yield on housing that is not fully displaced by interest rate changes.

Summary of a forthcoming paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What do the natural experiments identify?

Lease extensions reveal the market’s valuation of the same physical dwelling at two points — just before and just after the 90-year extension — with the extension itself creating a clean variation in the remaining lease term (and hence in the present value of ownership) without changing the property’s rent-generating characteristics. This design separates the rent and price components of the yield at the property level, allowing identification of discount-rate and rent-growth contributions free of compositional differences across properties.

Q2. Why do discount rates dominate yield variation?

A present-value decomposition of the housing yield into expected rent growth and the discount rate assigns more than 90 percent of variance to the discount rate component, implying that periods of low housing yields (high prices relative to rent) reflect primarily that investors demand a lower return on housing — not that they expect rents to rise faster. This result mirrors Campbell-Shiller findings for equity markets but is especially striking for housing, where naive narratives often attribute booms to expected rent appreciation.

Q3. What does the convenience yield interpretation imply?

Housing yields respond less than one-for-one to real interest rate movements — a slope well below one in the yield-rate regression — implying that housing carries a non-pecuniary convenience yield (liquidity, collateral value, direct utility of ownership) that buffers the required return on housing against interest rate changes. When real rates rise, housing yields rise by less, so price-to-rent ratios decline by less than a frictionless model would predict.

Key concepts

housing yield : the annual rent-to-price ratio on residential property; the paper’s central object, decomposed into discount-rate and rent-growth components.

discount-rate channel : the dominant source of housing yield variation in this paper; movements in investors’ required return on housing, not expected rent growth, drive the observed yield dynamics.

convenience yield : the non-pecuniary value of housing ownership (liquidity, collateral, direct utility) that drives a wedge between the housing yield and the risk-free real interest rate; explains the less-than-one slope in the yield-rate relationship.

Efficiency Criteria, Income Taxation, and Heterogeneous Elasticities

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

Overview

Research Question. Can income tax schedules be justified as utilitarian-optimal without adopting extreme normative assumptions about how household welfare should be measured? The paper proposes a welfare criterion strictly stronger than Pareto efficiency—called rationalizability with bounded curvature—and asks whether observed US income taxes satisfy it.

Starting Point. Any Pareto-efficient nonlinear income tax schedule can, in principle, be rationalized as utilitarian-optimal under some cardinalization of household utilities (i.e., some choice of how to measure the cardinal scale of each household’s well-being). However, the paper shows that rationalizing Pareto-efficient taxes in this way often requires cardinalizations under which there is no population upper bound on the curvature of utility with respect to consumption. Equivalently, a utilitarian planner’s marginal willingness to transfer resources to households must fall arbitrarily quickly with the size of those transfers—an extreme form of status quo bias violated by virtually all quantitative optimal-tax exercises.

The Proposed Criterion. The authors restrict attention to cardinalizations with locally bounded curvature: there exists a finite (though potentially arbitrarily large) upper bound on the coefficient of relative risk aversion across the population. This admits two interpretations: (i) ex post, it requires that the social value of transfers not change arbitrarily quickly with transfer size; (ii) ex ante, it corresponds to a decision-maker behind a veil of ignorance with bounded risk aversion.

Main Theoretical Result. Within a standard Mirrlees model of nonlinear income taxation with arbitrary preference heterogeneity and intensive-margin labor supply, the paper proves that a tax schedule can be rationalized with bounded curvature if and only if government revenues are both decreasing and concave (not merely decreasing) with respect to a class of narrowly targeted “two-bracket” reforms—reforms that raise retention by $1 local to some income level $z$ and zero elsewhere. This contrasts with Pareto efficiency, which requires only that revenues be decreasing in these reforms (Bierbrauer, Boyer, and Hansen 2023). The additional requirement of revenue concavity is what distinguishes the bounded-curvature criterion from pure Pareto efficiency.

Sufficient Statistics. The paper derives explicit sufficient-statistics expressions for the first- and second-order derivatives of tax revenue with respect to these targeted reforms. The second derivative depends on higher moments of the elasticity distribution, specifically the income-conditional variance of compensated elasticities of taxable income (ETIs). Revenue convexity—which causes the second-order condition to fail—arises when income-conditional ETI variance is sufficiently high, even holding the mean ETI fixed. The economic mechanism is a “sort-and-extort” dynamic: a small tax reform sorts higher-elasticity households into income brackets where marginal taxes fall and lower-elasticity households into brackets where marginal taxes rise; repeating the reform then exploits this sorting by differentially taxing households by elasticity, as if applying group-specific tax schedules within a uniform income tax.

Empirical Findings. Using the NBER panel of US tax returns from 1979 to 1990, the paper estimates income-conditional mean ETIs of approximately 0.2–0.3 at most income levels. Crucially, it estimates a lower bound on income-conditional ETI variance by comparing elasticities of light versus heavy itemizers (defined by whether a household claims above or below the mean value of deductions in its income bracket). The low-elasticity group has an ETI of approximately zero and the high-elasticity group has an ETI of approximately one, implying a lower bound on ETI variance of roughly 0.2 at most incomes and approximately 0.25 at the top of the distribution. This lower bound is close to—and under plausible assumptions above—the threshold required for the second-order condition to fail. The authors conclude that the US income tax schedule in 1990 was likely Pareto efficient but likely not rationalizable with bounded curvature.

Quantitative Welfare Gains. In a calibrated model with a 50% top marginal tax rate, Pareto-tail shape of 2.5, mean ETI of 0.3, and ETI standard deviation of 0.75 (50% above the estimated lower bound), the planner gains significant welfare from either raising or lowering top marginal taxes. The welfare-maximizing top rate below the baseline is 13.3%, generating social value equivalent to a transfer of $1,966 per top earner. The welfare-maximizing top rate above the baseline is 71.2%, generating social value equivalent to a transfer of $972 per top earner. The revenue-maximizing rate is 80.9% under the baseline calibration, ranging from 74.6% to 86.8% as ETI standard deviation varies by ±25% of the lower bound.

Scope Conditions. The theoretical analysis is restricted to intensive-margin labor supply (abstracting from extensive-margin decisions); the empirical application focuses on top incomes where extensive-margin effects are likely small. The empirical period is 1979–1990, covering major federal and state tax reforms. Results concern local efficiency of the tax schedule, not global optimization.

In depth

Q1. What exactly is “rationalizability with bounded curvature” and how does it differ from Pareto efficiency?

A: Pareto efficiency requires that no small reform makes someone better off without making anyone worse off. Rationalizability (with any cardinalization) is equivalent to Pareto efficiency in this setting. Rationalizability with bounded curvature additionally restricts the cardinalization: there must exist a finite upper bound on the coefficient of relative risk aversion (or equivalently, on the curvature of utility with respect to consumption) across the population. This is a strictly stronger criterion than Pareto efficiency. A schedule can be Pareto efficient but not rationalizable with bounded curvature if the only cardinalizations that rationalize it require unbounded consumption utility curvature.

Q2. Why do “extreme” cardinalizations with unbounded curvature arise when rationalizing Pareto-efficient taxes?

A: When a Pareto-efficient schedule is rationalized as utilitarian, the cardinalization must make the set of feasible, recardinalized utilities convex so it can be separated from the set of Pareto-improving allocations. The paper constructs such a cardinalization explicitly: it takes the form of a function whose second derivative approaches negative infinity as utility approaches its baseline value. This implies the planner’s marginal value of transfers to a household falls precipitously as the household is made even slightly better off—an extreme status quo bias. Theorem 2.b establishes that all cardinalizations rationalizing a schedule with convex revenues must share this pathology.

Q3. What is the “sort-and-extort” mechanism and how does it generate revenue convexity?

A: When elasticities of taxable income (ETIs) are heterogeneous within an income level and the income density is declining steeply, a reform that lowers marginal taxes around income $z$ brings more households into the local bracket (because there are more households just below $z$ than above). Crucially, it disproportionately attracts households with higher ETIs, since they respond more strongly to the marginal tax cut and relocate from further away, where the density differs more. Repeating the reform therefore faces a higher-elasticity composition at $z$, generating larger positive behavioral effects—making revenues convex in the size of the reform. The second step (“extort”) involves raising taxes on the now-concentrated low-elasticity households at adjacent brackets, achieving as-if group-specific taxation within a single income tax schedule.

Q4. What is the precise relationship between revenue convexity and ETI variance?

A: The paper shows (Theorem 4) that the second-order revenue derivative with respect to a narrow two-bracket reform around income $z$ equals a positive function of the income density times the expression $-[1-R’_0(z)]\varepsilon(z) + [1-R’_0(z)]\alpha(z)[\varepsilon^2(z) + \text{var}_h[\varepsilon^h | z^h_0=z]]$. The first term is always negative (pushing toward revenue concavity). The second term, which includes the income-conditional variance of ETIs, can dominate and create revenue convexity when ETI variance is sufficiently large. In the benchmark case with a single household type at each income (no within-income heterogeneity), the variance term vanishes and revenues are always concave whenever decreasing.

Q5. What is the sufficient statistics test for rationalizability at the top of the income distribution?

A: At top incomes (assuming no income effects, no super-elasticities, and CES preferences), taxes are Pareto efficient if and only if $\tau_\text{top} < \frac{1}{1+\alpha_\text{top}\varepsilon_\text{top}}$, and they are rationalizable with bounded curvature if and only if additionally $\tau_\text{top} < \frac{2}{1+\alpha_\text{top}(\varepsilon_\text{top} + \sigma^2_\text{top}/\varepsilon_\text{top})}$, where $\tau_\text{top}$ is the top marginal tax rate, $\alpha_\text{top}$ is the Pareto tail shape, $\varepsilon_\text{top}$ is the mean ETI at the top, and $\sigma^2_\text{top}$ is the income-conditional ETI variance at the top.

Q6. How does the paper estimate a lower bound on income-conditional ETI variance?

A: The authors divide households at each income level into “heavy” and “light” itemizers based on whether their total deductions exceed the local income-bracket mean. They then estimate group-specific ETIs using local polynomial regressions of log income changes on log marginal retention changes, interacting tax changes with heavy-itemizer indicators. The within-year difference in elasticities between groups provides a lower bound on within-income ETI variance, since the two-group decomposition captures only a fraction of true variance. The interaction coefficient is allowed to vary by year to isolate within-year, within-income variation in elasticities rather than between-year compositional changes.

Q7. What are the estimated magnitudes of mean and variance of ETIs?

A: Income-conditional average ETIs are estimated at between 0.2 and 0.3 at most income levels, consistent with but somewhat below prior literature estimates. The low-elasticity group (light itemizers) has an ETI of approximately zero, while the high-elasticity group (heavy itemizers) has an ETI of approximately one. Given roughly equal group sizes, this implies a lower bound on ETI variance of approximately 0.2 at most incomes and approximately 0.25 at the ninety-fifth percentile. Subdividing the high-elasticity group into two, three, and four subgroups yields a lower bound of approximately 0.25 for variance at the top.

Q8. How does the back-of-the-envelope calculation work to assess whether the second-order test fails?

A: With $\tau_\text{top} \approx 0.5$, $\alpha_\text{top} \approx 2.5$, and $\varepsilon_\text{top} \approx 0.3$ (from prior literature), the second-order condition fails if and only if ETI variance exceeds approximately 0.27. The authors’ lower bound estimate of ETI variance is already approximately 0.25 (standard deviation approximately 0.5), just below this threshold. The authors note that if the true standard deviation exceeds the lower bound by more than 4%, the second-order condition fails, making it empirically likely that the 1990 US tax schedule was not rationalizable with bounded curvature.

Q9. Why does the paper focus on the top of the income distribution for the empirical test?

A: The second-order condition is most likely to fail at high incomes for three reasons simultaneously: (i) the marginal tax rate is highest, (ii) ETI means are somewhat higher there, and (iii) the Pareto parameter $\alpha(z)$ is largest (income density falls steeply), which amplifies the sort-and-extort mechanism. The authors also note that extensive-margin labor supply responses—which are abstracted away in the theory—are likely small at high incomes.

Q10. What does the calibrated quantitative application reveal about optimal top tax policy?

A: Calibrated with a 50% initial top marginal tax rate, Pareto tail shape of 2.5, mean ETI of 0.3, and ETI standard deviation of 0.75 (50% above the estimated lower bound), the model finds welfare gains in both directions of reform. The welfare-maximizing rate below the baseline is 13.3%, yielding equivalent welfare gains of $1,966 per top earner. The welfare-maximizing rate above the baseline is 71.2%, yielding equivalent gains of $972 per top earner. The revenue-maximizing rate is 80.9%, ranging from 74.6% to 86.8% when ETI standard deviation varies by ±25% of the lower bound. This sensitivity highlights that the optimal direction and magnitude of reform depend substantially on the uncertain degree of ETI heterogeneity.

Q11. How does the paper relate to the “inverse optimum” literature?

A: The inverse optimum approach (Bourguignon and Spadaro 2012; Hendren 2020) infers the first-order welfare trade-offs implicit in an observed tax schedule. This paper goes further by inferring from second-order empirical moments—specifically the income-conditional ETI variance—whether taxes are consistent with minimal requirements on how sensitive the planner’s trade-offs are to household welfare levels. Rather than assuming a welfare function, it tests whether any welfare function with bounded curvature can rationalize the observed schedule.

Q12. Is revenue convexity possible without within-income heterogeneity in preferences?

A: Yes, but only under more specific conditions. The paper provides two supplemental examples. In the first, all households have constant-elasticity labor disutility but differ in both productivity and elasticity across income levels; when lower-income households have higher elasticities, a reform reducing marginal taxes at $z$ attracts higher-elasticity households and raises the average elasticity, leading to convex revenues. In the second, all households have the same initial elasticity but individual elasticities change in response to reforms. However, with the standard additively separable CES preferences and no within-income heterogeneity, revenues are always concave when decreasing—consistent with Werning’s (2007) observation that the Pareto planner’s problem is convex in this case.

Q13. What is the role of random tax reforms in the paper’s logic?

A: Random tax reforms serve as an expository bridge. The paper shows that if the second-order revenue effect of a two-bracket reform is positive at some income $z$, then a “randomized” reform that applies the reform with equal probability in positive and negative directions generates an expected Pareto improvement—because the convexity of revenues implies expected revenues rise, while for any household with bounded risk aversion the reform’s second-order utility effect is also positive when the reform is sufficiently narrow. This establishes that revenue convexity implies random Pareto inefficiency under bounded risk aversion, and then the paper shows the analogous deterministic result for rationalizability.

Q14. What scope conditions attach to the sufficient conditions for rationalizability (Theorem 3)?

A: Theorem 3 requires Assumptions 1 and 3 plus two boundary conditions: the ratio $\delta\text{Rev}(z)/(zg(z))$ must remain bounded away from zero as income approaches 0 or infinity, and at all incomes there must exist households with low enough compensated elasticities. Assumption 1 requires that average and marginal taxes have upper bounds below one, that marginal taxes have a lower bound, and that $zg(z)$ converges to zero at the boundaries. Assumption 3 is a regularity condition on how conditional moments of the elasticity distribution vary with income. These conditions ensure that the narrow, self-financing reforms considered in the necessity proof cannot generate welfare improvements once revenues are both decreasing and concave.

Key Concepts

Rationalizability with Bounded Curvature. The property that a tax schedule is utilitarian-optimal under some cardinalization of household utilities in which there exists a finite (though potentially arbitrarily large) upper bound on the curvature of utility with respect to consumption across the population. Formally, there exists a continuous function $\bar{\rho}$ such that, for all households, the absolute value of $[w_h \circ u_h]_{cc} / [w_h \circ u_h]_c$ is bounded by $\bar{\rho}$ evaluated at the household’s income. This criterion is strictly stronger than Pareto efficiency and strictly weaker than utilitarian optimality under a fixed cardinalization.

Two-Bracket Reform. A targeted tax reform that increases retention (post-tax income) by $1 at incomes local to some level $z$ over a small bracket of width $\ell$, and zero elsewhere (smoothed at the edges). As $\ell \to 0$, this becomes an infinitesimally narrow reform. The first- and second-order revenue effects of these reforms—denoted $\delta\text{Rev}(z)$ and $\delta^2\text{Rev}(z)$—are the paper’s key objects: Pareto efficiency requires $\delta\text{Rev}(z) < 0$ for all $z$, and rationalizability with bounded curvature additionally requires $\delta^2\text{Rev}(z) \leq 0$ for all $z$.

Income-Conditional ETI Variance. The variance of compensated elasticities of taxable income (ETIs) among households with the same income level, $\text{var}_h[\varepsilon^h | z^h_0 = z]$. This is the paper’s primary empirical object of interest and the key determinant of whether revenues are convex or concave in the size of targeted reforms. Unlike the literature’s focus on mean ETIs by income bracket, this within-income variance captures heterogeneity among households sharing the same pre-reform income.

Sort-and-Extort Mechanism. The two-step economic mechanism underlying revenue convexity from ETI heterogeneity. In the first step (“sort”), a marginal tax cut around income $z$ disproportionately attracts higher-ETI households from lower incomes (because they respond more strongly and relocate from further away), shifting the elasticity composition at $z$ upward. In the second step (“extort”), repeating the reform finds higher-elasticity households concentrated where marginal taxes fall and lower-elasticity households where taxes rise, effectively applying differential tax treatment by elasticity within a single income tax schedule.

Local Pareto Parameter $\alpha(z)$. Defined as $-d\log(zg(z))/d\log z$, where $g(z)$ is the income density. This captures the rate at which the income density is falling in income locally at $z$, and governs the strength of the sort-and-extort mechanism. High $\alpha(z)$ at top incomes (reflecting a steeply declining Pareto-type density) amplifies revenue convexity from ETI heterogeneity.

Super-Elasticity. A concept that captures how a household’s compensated ETI would change if its income were different, holding preferences fixed. Formally, it is the derivative of the household’s elasticity with respect to its log income, decomposing into effects from changes in preference curvature and changes in the local curvature of the tax schedule. Super-elasticities are zero in the benchmark case of additively CES preferences and locally CES retention schedules but contribute additional terms to the second-order revenue expression in the general case.

Cardinalizing Function. A strictly increasing function $w_h$ that maps household $h$’s indirect utility $V_h$ to a cardinalized utility level $w_h(V_h)$. The social planner maximizes the expectation of cardinalized utilities. Different choices of ${w_h}_h$ correspond to different stances on interpersonal comparisons, including unbounded curvature (rationalizing any Pareto-efficient schedule) or bounded curvature (the paper’s proposed restriction). Rawlsian social welfare is a limit of utilitarian welfare with increasingly concave cardinalizing functions.

Energy Transitions in Regulated Markets

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

This paper asks how rate-of-return (RoR) regulation in U.S. electricity markets affects the speed and efficiency of energy transitions, specifically the transition from coal to combined-cycle natural gas (CCNG) generation driven by fracking-induced cost declines. The authors build and estimate a structural model of regulated utility behavior in which utilities optimize investment, retirement, and hourly operations decisions against an incentive structure set by state Public Utility Commissions (PUCs).

The regulatory environment combines two instruments: (1) an allowable rate of return that is decreasing in consumer electricity rates (incentive regulation), parameterized as s = (r/r₀)^{-γ}, where higher γ penalizes high-cost outcomes more severely; and (2) a “used-and-useful” standard in which a coal plant’s contribution to the rate base depends on its capacity utilization via a logit function. These two instruments create a tension: utilities want to lower costs to earn a higher RoR, but also want to run existing coal plants—even when uneconomical—to prove they are “used and useful” and thus maximize their rate base and profits.

The authors estimate the model using publicly available EIA and EPA CEMS data spanning 2006–2017, covering 39 unique regulated utilities in the Eastern Interconnection across more than 4 million utility-hour observations (459 utility-years). Structural parameters are recovered via a nested fixed-point indirect inference approach that matches simulated regression coefficients to actual data; investment and retirement costs are estimated with a GMM nested fixed-point approach.

Key reduced-form findings confirm the model’s two core mechanisms. First, a 10% increase in total variable costs is associated with a 2.5% decrease in variable profits per MW of capacity (with utility fixed effects), consistent with incentive regulation. Second, regulated utilities reduce coal generation by only a statistically insignificant 4.2 percentage points when coal fuel costs exceed import prices, compared to 16.1 percentage points for restructured utilities—consistent with regulated utilities running coal out-of-dispatch order to preserve used-and-useful status.

In counterfactual simulations that impose 2018–20 natural gas prices ($2.01/MMBtu versus the 2006 price of $7.24/MMBtu) on utilities with their 2006 capital stocks, regulated utilities retire only 53% of coal capacity over 30 years and increase CCNG capacity by 296%, whereas a cost minimizer would retire most coal capacity while increasing CCNG by only 58%. The Averch-Johnson over-investment effect dominates: regulated utilities over-invest in CCNG while simultaneously over-using legacy coal.

Carbon taxes on regulated utilities reduce short-run coal generation only 48% as much as when imposed on a cost minimizer (because the used-and-useful incentive partially offsets the carbon price signal), but in the long run result in 68% lower coal capacity and 77% lower coal generation relative to baseline by year 30—larger effects than for the cost minimizer. Eliminating the coal usage incentive (μ₂ = 0) produces 82% lower coal capacity and 92% lower coal generation over 30 years but requires utility variable profits to fall by over $300 million, threatening reliability without compensating transfers.

Scope conditions: Results apply to regulated (non-restructured) utilities in the Eastern Interconnection, 2006–2017. The model estimates the coal-to-CCNG transition only; it explicitly does not model the ongoing transition to renewables and storage due to insufficient data variation.

In depth

Q1. What is the central research question?

The paper asks whether and how rate-of-return regulation in U.S. electricity markets slows energy transitions, and what alternative regulatory structures or carbon tax policies could accelerate the transition away from coal. It addresses this both theoretically—through a structural model of regulated utility behavior—and empirically, through estimation and counterfactual simulation using data on 39 regulated utilities over 2006–2017.

Q2. What are the two key regulatory instruments in the model, and what distortions do they create?

The first instrument is incentive regulation: the allowable rate of return declines as consumer electricity rates rise (s = (r/r₀)^{-γ}), so utilities have an incentive to lower costs. The second is the used-and-useful standard: a coal plant’s contribution to the rate base depends on its capacity utilization via a logit function, creating an incentive to run coal plants even when their fuel costs exceed import prices. Together, these instruments generate a tension between cost-reduction incentives and legacy-capacity-preservation incentives, causing the regulated utility to both over-invest in new CCNG capacity (Averch-Johnson effect) and over-use existing coal capacity relative to the cost-minimizing benchmark.

Q3. What does the reduced-form evidence show about uneconomical coal usage?

In a triple-difference specification, regulated utilities reduce coal generation by only 4.2 percentage points (statistically insignificant) when coal fuel costs exceed import prices, compared to a 16.1 percentage point reduction for restructured utilities. CCNG generation responds similarly under both regulatory regimes (21.1 vs. 19.7 percentage points), confirming that the distortion is specific to legacy coal under RoR regulation and not a general feature of high-cost generation. The six states with the largest responsiveness of coal usage to low market prices are all restructured states; out-of-dispatch-order coal generation also correlates strongly with utility ownership share across states.

Q4. What do the structural parameter estimates reveal about the rate base?

Each MW of CCNG capacity increases the rate base by $229,000. When fully utilized, each MW of coal capacity contributes 1.144 times as much as CCNG. When coal is not fully used, unused coal capacity contributes only 40% as much to the rate base as CCNG. NGT capacity contributes 79% more to the rate base than CCNG per MW. Operations cost estimates include O&M costs of $12.89/MWh for coal, $8.82/MWh for CCNG, and $44.63/MWh for NGT; a 100 MW coal ramp in one hour costs $4,770 versus $3,860 for CCNG.

Q5. What happens in the 30-year long-run counterfactual under the baseline regulated utility?

Facing a sudden drop to 2018–20 natural gas prices ($2.01/MMBtu vs. $7.24/MMBtu in 2006), regulated utilities retire 53% of coal capacity and increase CCNG capacity by 296% over 30 years. The Averch-Johnson over-investment effect dominates: utilities invest heavily in CCNG while retaining and using legacy coal far longer than a cost minimizer would. The social planner effectively eliminates coal generation immediately (99% reduction in the first period) and retires almost all coal capacity over the horizon.

Q6. How does a cost minimizer behave relative to the regulated utility in the same long-run counterfactual?

A cost minimizer immediately reduces coal generation by 50% in the first period and retires most coal capacity over 30 years while increasing CCNG capacity by only 58%—versus the regulated utility’s 296% CCNG increase. Thirty years after the shock, the cost minimizer has retired 71% more coal capacity than the regulated utility. The cost minimizer’s much smaller CCNG expansion reflects that it does not face Averch-Johnson incentives to over-invest in rate-base capital.

Q7. What is the short-run vs. long-run impact of carbon taxes on regulated utilities compared to cost minimizers?

In the short run, carbon taxes on regulated utilities reduce coal generation only 48% as much as when imposed on a cost minimizer (34% vs. ~100% in immediate generation drop), because the used-and-useful incentive counteracts the carbon price signal. In the long run (30-year horizon), however, carbon taxes on regulated utilities result in 68% lower coal capacity and 77% lower coal generation relative to baseline—larger percentage reductions than for a cost minimizer—because the regulatory structure amplifies the retirement incentive over time once carbon costs erode the economic rationale for keeping coal in the rate base.

Q8. What is the short-run operations counterfactual finding for carbon taxes in the sample period?

Using each utility-year in the analysis sample, imposing carbon taxes on regulated utilities reduces carbon costs by only about $500 million relative to baseline—41% of the $1.3 billion carbon cost savings from imposing the same carbon taxes on a cost minimizer. Despite this limited carbon reduction, electricity rates nearly triple from $77.58/MWh to $224.18/MWh under the regulated utility with carbon taxes, as the utility passes through most carbon costs to consumers; regulated utility variable profits also fall by over $500 million.

Q9. What happens when the coal usage incentive is eliminated (μ₂ = 0)?

Setting the coal usage incentive parameter μ₂ = 0 (eliminating the logit slope on capacity utilization) causes coal capacity to fall 82% and coal generation to fall 92% relative to baseline over 30 years—a slightly larger generation decline than for the cost minimizer. However, this comes at the cost of more than twice the CCNG capacity due to the Averch-Johnson effect, and requires utility variable profits to fall by over $300 million, raising reliability concerns unless accompanied by compensating transfers.

Q10. How does the paper’s mechanism relate to observed differences in coal exit rates between regulated and restructured states?

Between 2006 and 2018, 26.0% of coal capacity exited in restructured states versus only 17.2% in regulated states—a gap the authors attribute primarily to the used-and-useful incentive structure in RoR regulation. The structural model quantifies how this regulatory feature specifically distorts coal usage and retirement decisions; it is not explained by demand or cost differences across states, as confirmed by the triple-difference evidence showing the gap is specific to coal (not CCNG) and to regulated (not restructured) utilities.

Q11. Why does the paper argue that alternative regulatory adjustments are insufficient to replicate cost-minimizing transitions?

Changing regulatory parameters—such as increasing the coal usage incentive or adjusting the electricity rate penalty—does not come close to replicating the speed of the energy transition under a cost minimizer in the long-run simulations. Regulatory adjustments that do approach cost-minimizing outcomes (such as eliminating μ₂) require large reductions in utility variable profits sufficient to risk reliability, consistent with why the 2022 Inflation Reduction Act relied on substantial investment transfers rather than carbon taxes as its primary clean energy instrument.

Q12. What is the paper’s identification strategy?

Identification exploits the sharp, exogenous decline in natural gas fuel prices from fracking, which had heterogeneous implications across utilities depending on their initial capital mixes (coal-heavy vs. CCNG-heavy). By comparing investment, retirement, and operations decisions across utilities and over time—particularly between utilities that had CCNG exposure before the price decline and those that did not—the authors recover the structural regulatory and cost parameters. The IV specification for reduced-form evidence uses the current natural gas price interacted with the utility’s initial CCNG generation share as an instrument for fuel and import costs.

Q13. What are the paper’s explicit limitations?

The paper estimates the coal-to-CCNG transition only and cannot speak to the transition to renewables and storage, because there is insufficient variation in the data to identify how regulators would treat CCNG as a legacy technology subject to used-and-useful standards, or how renewables and storage would contribute to the rate base. The authors note that over-investment in CCNG capacity may create future stranded asset problems for ratepayers and that usage incentives for CCNG are likely to further hinder the transition to renewables—but these are conjectures rather than estimated findings.

Rate-of-return (RoR) regulation: A regulatory structure in which the PUC sets electricity rates so that utility revenues cover total variable costs plus an allowable return on the utility’s rate base (capital stock), with the allowable return parameterized as s = (r/r₀)^{-γ}, declining as consumer electricity rates rise.

Used-and-useful standard: A prudence criterion under which a capital asset’s contribution to the rate base depends on its capacity utilization, modeled as a logit function of the generation-to-capacity ratio; fully used coal capacity contributes 1.144 times as much as CCNG per MW, while unused coal contributes only 40% as much.

Rate base: The capital stock on which the PUC grants the utility its allowable rate of return; adjusted by prudence and used-and-useful assessments and described in the paper as “at best an arduous task” to quantify precisely.

Averch-Johnson (AJ) over-investment effect: The tendency of regulated utilities to over-invest in capital because profits are proportional to the rate base; in this paper’s setting, this causes regulated utilities to increase CCNG capacity by 296% over 30 years following the natural gas price shock, compared to 58% for a cost minimizer.

Incentive regulation: A modification of cost-plus RoR regulation in which the allowable rate of return declines as electricity rates rise; it provides efficiency incentives for cost reduction but does not achieve first-best outcomes and is insufficient to overcome the used-and-useful distortion for legacy coal.

Out-of-dispatch-order generation: Running a generation unit when its fuel costs exceed the market import price; regulated utilities engage in this behavior with coal plants to maintain used-and-useful status and rate base contribution, whereas restructured utilities do not face this incentive.

Nested fixed-point indirect inference: The estimation approach used to recover structural regulatory and operations parameters by minimizing the distance between regression coefficients from actual data and those from model-simulated data via a non-linear parameter search.

Equal Pay for Similar Work

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

Layer 1 — Overview

Research Question

This paper studies the labor market effects of “Equal Pay for Similar Work” (EPSW) policies — laws that require firms to pay equal wages to workers of different protected-class identities (e.g., different genders) who perform “similar” work within a firm. EPSW has become increasingly prevalent: as of January 2023, more of the U.S. workforce falls under state EPSW laws than state “Equal Pay for Equal Work” (EPEW) laws. Despite this spread, the equilibrium consequences of EPSW were previously unknown.

Theoretical Framework

The authors develop two theoretical models. The first is a static cooperative game (whose outcomes coincide with the Nash equilibria of a non-cooperative simultaneous-wage-offer game). Homogeneous firms with constant-returns-to-scale production compete for a continuum of heterogeneous workers. Workers belong to one of two groups A or B (e.g., men and women), with group A constituting a β ≥ 1 majority. Each worker’s productivity v is drawn from a group-specific distribution (FA or FB); firms’ willingness to pay equals each worker’s productivity, but can embed taste-based discrimination. The analysis is framed as applying “within job” in a local labor market — only workers performing “similar” work in the eyes of the law.

The second model is a dynamic search-and-bargaining framework with an arbitrary number of firms, search frictions, reallocation frictions, and Nash-in-Nash bargaining. EPSW is introduced as a surprise, and constrained firms choose whether to segregate for one group or remain desegregated (paying a common wage to all workers).

Main Theoretical Findings

Without EPSW, Bertrand competition among firms drives every worker’s wage to equal her productivity; any wage gap between groups A and B exactly reflects the difference in average productivities (EA(v) − EB(v)), whether or not those productivity differences stem from discrimination.

With EPSW, the equilibrium is qualitatively transformed. In the static model (Proposition 2), firms generically fully segregate their workforces: one firm hires all A-group workers and the other hires all B-group workers. EPSW functions as an enforcement mechanism for this segregation analogous to location choices in Hotelling’s model — poaching a worker from the competing firm is costly because EPSW then requires the poaching firm to pay equal wages to all workers it employs. In the core with EPSW (Proposition 3), the wage gap moves in favor of the majority group (A-group, β > 1) in the sense that all core outcomes except one strictly increase the A-group wage advantage. Moreover, firm profits and the magnitude of the wage gap co-move: firms benefit from selecting equilibria with larger wage gaps. The directional conclusion — EPSW benefits the majority group — holds regardless of the distributions of the two groups’ productivities, conditional only on β > 1 for the wage gap; for the log wage gap the additional regularity condition βEA[v] > EB[v] is required.

In the dynamic search model (Proposition 4), all firms eventually segregate under any equilibrium, with the long-run wage ratio moving in favor of the group toward which more firms segregate. Under equitable search and sufficiently low reallocation frictions (Proposition 5), more firms segregate toward the majority group when βEA[v] > EB[v]. Firms that are nearly segregated at the time of EPSW enactment segregate sooner than others (Proposition 6).

Empirical Setting and Design

The authors test these predictions using Chile’s 2009 EPSW (Law 20.348), the country’s first equal pay law, which prohibited paying women less than men (or vice versa) for similar work. Firms with 10 or more long-term workers at the time of announcement (June 2009) face formal grievance procedures and financial penalties (69–1,384 USD per worker-month of violation); firms below this threshold face no financial penalty, providing a clean threshold-based treatment assignment.

The data are matched employer-employee administrative records from the Chilean unemployment insurance system covering January 2005 – December 2013, a random sample of approximately 4% of all firms stratified by size. The main estimation sample restricts to firms with 6–13 total workers at announcement (41% of active firms), and the design is a difference-in-differences (event study) comparing treated (≥ 10 long-term workers) to control (< 10 long-term workers) firms. The identifying assumption is parallel trends between similarly sized firms.

Main Empirical Findings

First, EPSW increases full gender segregation across firms. The share of fully gender-segregated firms increases by 4.4 percentage points (baseline: 34.3% of firms were fully segregated at announcement). Simultaneously, the share of nearly-but-not-fully segregated firms (majority gender share ∈ [0.8, 1)) declines by 4.0 percentage points — a “missing mass” of near-segregated firms consistent with the search model’s prediction that firms on the margin of full segregation segregate most readily (e.g., by separating the sole worker of the “wrong” gender). Moreover, firms that are nearly segregated at announcement experience an 8.7 percentage point increase in full segregation post-EPSW, compared to 2.8 percentage points for firms not nearly segregated at announcement.

Second, EPSW shifts the gender wage gap in favor of the local labor market majority group. In male-majority local labor markets (defined by industry × county), EPSW increases the gender wage gap in favor of men by 4.3 percentage points. In female-majority local labor markets, EPSW decreases the gender wage gap (i.e., in favor of women) by 6.2 percentage points. The wage gap change is primarily driven by reductions in minority-group wages: women’s average wages in male-majority markets fall by 3.3 percentage points, and men’s average wages in female-majority markets fall by 4.5 percentage points; there are no statistically significant changes in majority-group wages. Because men dominate Chile’s overall labor market (approximately 5/6 of all workers are employed in majority-male local labor markets), the overall effect of EPSW is to increase the gender wage gap (in favor of men) by 2.7 percentage points. Pre-treatment coefficients are statistically indistinguishable from zero across all specifications, supporting the parallel trends assumption. These findings are robust across six alternative specifications covering different samples, fixed-effect structures, and controls.

Scope Conditions

Theoretical results apply within a set of “similar” workers in a given local labor market — the paper does not predict differential effects across job types within a firm (e.g., custodians vs. lawyers) that do not perform similar work. Empirical results are identified for firms with 6–13 workers and pertain to Chile’s formal sector (informal labor share ~25% in 2009). Predictions on the wage ratio (log wage gap) require the additional regularity condition βEA[v] > EB[v], which is consistent with the Chilean data.

In depth

Q1. What is the core mechanism by which EPSW leads firms to fully segregate in the static model?

A: EPSW makes cross-group poaching prohibitively costly. If a firm that hires only A-group workers were to hire even a positive measure of B-group workers, EPSW would — by transitivity — require it to pay the same wage to all workers. This eliminates the firm’s ability to exploit productivity heterogeneity across workers; it would have to raise all wages to match the highest worker, destroying profit. As a result, firms segregate in equilibrium to avoid the bite of EPSW entirely: each firm caters to one group, and the within-group wage schedule remains unconstrained. The mechanism is analogous to Hotelling’s location model: segregation serves as the enforcement device for avoiding the equal-pay constraint.

Q2. How does the equal profit condition generate a wage gap in favor of the majority group?

A: In any core outcome under EPSW (Proposition 3), the Equal Profit Condition requires both firms to earn the same total profit. When there are β > 1 A-group workers (more than B-group workers), the firm serving A-group workers must pay higher average wages per worker to extract the same total profit from a larger pool, relative to the firm serving a smaller B-group. This mechanically raises A-group average wages relative to B-group average wages. Crucially, this directional conclusion — EPSW widens the majority-group wage advantage — holds regardless of the shapes of FA and FB, meaning it is robust to any underlying discriminatory or non-discriminatory productivity differences.

Q3. What is the baseline (without-EPSW) wage gap, and how does EPSW change it?

A: Without EPSW, Proposition 1 establishes that every worker is paid exactly her productivity in any core outcome (full employment, wages = productivity). Therefore, the wage gap equals EA(v) − EB(v) and the wage ratio equals EA(v)/EB(v): any gap reflects only productivity differences (including discrimination embedded in willingness to pay). Under EPSW, Proposition 3 shows that all core outcomes except a single (measure-zero) one strictly widen the wage gap beyond this level. The wage ratio result (Proposition 3, Part 4) requires the additional condition βEA[v] > EB[v] — that the majority group is not sufficiently less productive or more discriminated against to reverse the direction.

Q4. How does the dynamic search model modify the static predictions?

A: In the dynamic model (Proposition 4), full segregation is achieved in finite time T in any equilibrium, not instantaneously. Prior to T, firms make sequential segregation decisions; workers displaced by firm desegregation choices are replaced at rate ρ ∈ [0,1]. The long-run wage ratio is determined by the ratio nA/nB — the number of firms segregating toward group A versus B. If nA > nB, the long-run wage ratio moves in favor of A; if nA = nB, the policy has no long-run effect on the wage ratio. The key departure from the static model is that this outcome depends not only on the majority group size but also on search intensities and reallocation frictions (high firm tenure/low d can make segregating toward the majority costly if the firm already employs many minority-group workers).

Q5. Under what conditions does the dynamic model predict that more firms segregate toward the majority group?

A: Proposition 5 states that for sufficiently large d (fast worker turnover / low reallocation frictions) and equitable search (equal search intensity across firms within a group), the number of firms segregating toward A satisfies nA ∈ [xA−1, xA+1], where xA is defined by an equal-profit condition. Moreover, if βEA[v] > EB[v] (the majority group is collectively more valuable), then nA ≥ nB. Without equitable search, the conclusion holds under more stringent conditions: for any search intensity vector r, there exist d* and β* such that for d > d* and β > β*, any equilibrium yields nA > nB. Empirically, 94% of local-labor-market-by-month units in Chile exhibit more firms segregating toward the majority gender post-EPSW, consistent with these conditions being met.

Q6. Why do firms that are nearly segregated at announcement respond most strongly to EPSW?

A: Proposition 6 establishes that firms with a low ratio of minority-group to majority-group search intensity (i.e., nearly segregated in employment) segregate earliest, provided the discount rate is sufficiently low. The intuition is that for a nearly segregated firm, the cost of segregating — separating the few minority-group workers — is small relative to the costs of remaining desegregated (paying a common wage that compresses profit, and being unable to poach new workers). Empirically, firms nearly segregated at announcement (majority gender share ∈ [0.8,1) at announcement) show an 8.7 percentage point increase in full segregation post-EPSW, roughly three times larger than the 2.8 percentage point effect for firms not nearly segregated at announcement. This “missing mass” pattern (decline in near-segregation matched by increase in full segregation) is also consistent with Proposition 6.

Q7. What is the heterogeneous effect of EPSW on the wage gap by local labor market type?

A: The empirical design allows the wage gap effect to differ by local labor market (LLM) majority type (male vs. female). In male-majority LLMs (firm industry × county pairs where males comprise more than 50% of workers in June 2009), EPSW increases the gender wage gap in favor of men by 4.3 percentage points (SE = 0.0116). In female-majority LLMs, EPSW decreases the gender wage gap (in favor of women) by 6.2 percentage points (SE = 0.0234). These findings precisely match the theoretical prediction that EPSW benefits whichever group is in the majority of the local labor market. The dynamic event studies show no pre-trends in either subsample; effects begin at announcement (τ = 0) and grow over time.

Q8. What drives the wage gap change — majority wages rising or minority wages falling?

A: The change is primarily driven by a reduction in the minority group’s average wages, not an increase in majority wages. Women’s average wages in male-majority labor markets fall by 3.29 percentage points (SE = 0.0111) in treated versus control firms post-EPSW. Men’s average wages in female-majority labor markets fall by 4.45 percentage points (SE = 0.0178) in treated versus control firms post-EPSW. There are no statistically significant changes in the average wages of the majority group of workers within any LLM type. This is consistent with the model’s mechanism: segregation reduces competition for minority-group workers (fewer firms competing for them), depressing their wages.

Q9. What is the aggregate (economy-wide) effect of EPSW on the gender wage gap in Chile?

A: Because approximately 5/6 of all Chilean workers are employed in male-majority local labor markets (men have higher labor force participation, with female labor force participation at roughly 30% in 2009), the overall effect of EPSW is to increase the gender wage gap in favor of men by 2.74 percentage points (SE = 0.0102). This is a net effect that averages the positive (pro-male) gap increase in male-majority markets and the negative (pro-female) gap decrease in female-majority markets, weighted by market sizes.

Q10. How does the identification strategy deal with anticipation and compositional changes?

A: Treatment status is assigned based on firm size at the time of policy announcement (June 2009) rather than enactment (November 2009), creating an intent-to-treat framework: some “treated” firms may fall below the threshold by enactment, and some “control” firms may rise above it, both attenuating the estimates (implying estimated effects are plausible lower bounds). The no-anticipation assumption is supported by the absence of statistically significant pre-trends in either the segregation or wage-gap specifications. To address compositional changes in worker characteristics across LLMs induced by EPSW itself, the wage regressions include time fixed effects interacted with human capital dimensions (education, contract type, age decade) and firm comparison groups, controlling for observable composition shifts. Placebo tests at alternative firm-size thresholds find no statistically or economically meaningful effects, supporting the causal interpretation.

Q11. How does EPSW in Chile compare to EPEW theoretically and in the literature?

A: EPEW requires equal pay only for workers doing exactly equal work, which creates an easily exploitable loophole: firms can proliferate job titles or marginally differentiate duties to avoid compliance. EPSW closes this by requiring equal pay across a coarser “similar work” category, making evasion harder. Theoretically, the prior EPEW literature (Bhaskar et al. 2002, Kaas 2009, Lagerlöf 2020, Lanning 2014) generated ambiguous directional predictions — equal pay laws could either increase or decrease wage disparities within the same paper. The authors attribute this ambiguity to EPEW models’ requirement that workers be exactly equally productive. By contrast, EPSW applies across workers with heterogeneous productivities, and the authors derive unambiguous predictions: full segregation and a wage gap shift toward the majority group, both of which are confirmed empirically.

Q12. What is the analogy to “best-price guarantees” in product markets?

A: The paper draws a methodological parallel to most-favored-customer (MFC) clauses in product markets. MFC clauses commit firms to rebating past consumers if prices fall, which directly equalizes payments across buyers but unintentionally raises firm market power. In the EPSW setting, the policy plays the role of a best-wage guarantee — but because firms compete for workers, the constraint binds off the equilibrium path. Firms segregate so that no firm is ever exposed to the equal-pay constraint in equilibrium, yet the threat of the constraint (if a firm deviates and hires from both groups) effectively differentiates labor costs across groups, driving the unintended wage effects. This is related to “artificial” switching costs that create local market power in consumer markets (Klemperer, 1987).

Key Concepts

Equal Pay for Similar Work (EPSW): A legal constraint requiring that within a firm, workers belonging to different protected-class identities (e.g., different genders) who perform “similar” work receive equal wages. Distinguished from “Equal Pay for Equal Work” (EPEW) by its coarser similarity standard, which cannot be evaded by minor job-title differentiation. In the model, this constraint is formalized as: a firm cannot hire positive measures of workers from two different groups such that all workers in one group receive strictly higher wages than all workers in the other group; by transitivity, a firm hiring from both groups must pay almost all workers the same wage.

Core Outcome: The solution concept used in the static model, drawing on cooperative game theory (Shapley–Shubik assignment game). An outcome (specifying which firm hires each worker and at what wage) is in the core if no firm and subset of workers can form a blocking coalition that makes both the firm and each worker in the coalition strictly better off. The paper uses this concept because its pure-strategy Nash equilibrium outcomes (in the associated non-cooperative simultaneous wage-offer game) exactly coincide with the core outcomes under the restriction that firms pay the same wage to all workers of the same type.

Full Segregation: A labor market outcome in which each firm employs workers from only one group (all A-group workers at one firm, all B-group workers at the other). The paper proves (Proposition 2) that EPSW generically forces full segregation in equilibrium, because any deviation to hire from both groups exposes the firm to the equal-pay constraint. Empirically measured as a binary indicator for whether all workers at a given firm in a given month are of the same gender.

Near Segregation: A firm-level state in which the majority gender constitutes 80–99% of the firm’s workforce (the majority gender share is in [0.8, 1)). The paper uses this as a complementary outcome to full segregation; theory (Proposition 6) predicts a decline in near segregation post-EPSW because firms in this state face the lowest cost of transitioning to full segregation. Empirically, the near-segregation share falls by 4.0 percentage points post-EPSW, mirroring the 4.4 percentage point rise in full segregation.

Local Labor Market (LLM): Defined in the empirical analysis as a firm’s geographic county interacted with its industry code, creating 321 × 21 potential cells. The LLM is classified as male-majority or female-majority based on the share of female workers across all firms in the industry-county pair in June 2009. This is the unit at which the “majority group” for Proposition 3’s wage gap prediction is defined, and the level at which the heterogeneous wage effects of EPSW are estimated.

Equal Profit Condition: A necessary condition of any core outcome (with or without EPSW): both firms must earn the same total profit in equilibrium. Under EPSW with full segregation, this condition determines the relative average wages of the two groups — because firm sizes differ (β A-group workers vs. 1 B-group worker), equal profit requires the firm serving the larger group to pay higher average wages, mechanically moving the wage gap in favor of the majority group.

Nash-in-Nash Bargaining: The bargaining protocol used in the dynamic search model, following Horn and Wolinsky (1988). Each bilateral worker-firm bargain splits the available surplus in proportion to exogenous bargaining power parameter Δ ∈ (0,1), taking as given the outcome of all other bilateral bargains. A worker’s disagreement point is the wage she would receive from bargaining with the next firm in her search order. This generates the result that a worker’s realized payoff is increasing in the number of segregated (non-EPSW-constrained) firms competing for her, connecting firm segregation decisions to wage determination.

Reallocation Friction: In the dynamic search model, represented by a low departure probability d ∈ (0,1) for existing employees. When d is low, firms retain a large fraction of their workforce across periods, making segregation costly because the firm must separate from any existing workers of the “wrong” group. The paper shows (Proposition 5) that for sufficiently large d (low frictions), the equal-profit condition approximately pins down the number of firms segregating toward each group, and for d above a threshold, the majority group attracts weakly more segregating firms.

Financial Frictions: Micro versus Macro Volatility

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

Overview

Research Question. How do consumer credit spreads — the gap between household borrowing rates and deposit rates — affect aggregate business cycle dynamics and the distribution of consumption across the wealth distribution? And what is the welfare trade-off between macroeconomic stabilization and household-level consumption volatility when bank capital requirements are tightened?

Data and Empirical Approach. The empirical analysis draws on Danish administrative register data for 2003–2018, combining approximately 15.5 million household-year observations. Income tax return data, which capture housing wealth, portfolio wealth, bank deposits, and bank and mortgage debt, are merged with bank-level reporting of interest rates submitted to Danmarks Nationalbank (MFI data). Household-specific credit spreads are constructed as the difference between the loan rate at a household’s primary loan bank and the deposit rate at its primary deposit bank in a given year. Consumption is imputed from household balance sheets following the method of Crawley and Kuchler (2023). The empirical specifications include household and time fixed effects, and quantile regressions are run across bins of the net wealth distribution.

Model. The authors develop a Heterogeneous Agent New Keynesian (HANK) model with explicit banking intermediation. Banks, subject to an agency friction following Gertler and Karadi (2011) — in which bankers can divert a fraction λ = 0.381 of assets — combine household deposits with net worth to invest in corporate equity and consumer loans. This leverage constraint generates an endogenous, countercyclical spread between borrowing and saving rates. Households face idiosyncratic income risk and a kink in their budget constraint at zero net worth due to the spread. The supply side features New Keynesian sticky prices (Rotemberg quadratic adjustment costs) and a Taylor rule. Aggregate shocks include monetary policy surprises, total factor productivity (TFP), and capital quality shocks (affecting bank net worth). The model is solved by first-order perturbation using the method of Bayer and Luetticke (2020) and calibrated to Danish macro and micro moments for 2003–2018.

Main Empirical Findings.

The average consumer credit spread in Denmark is strongly countercyclical, with a cross-correlation with HP-filtered output of −0.44 in the data (−0.31 in the model).
Higher credit spreads increase the transition rate into the zero net wealth state for households with moderately positive wealth at the beginning of the year, and reduce the outflow rate for households already at zero net wealth.
Pooled OLS (with household and time fixed effects) finds that a higher spread is negatively associated with consumption (coefficient −0.266), and the interaction between spread and log income is positive (coefficient 1.366), indicating that higher spreads raise income sensitivity of consumption. For below-median wealth households, the income–consumption link is stronger and the negative spread effect on consumption is larger.
The consumption-income elasticity derived from quantile regression estimates has a standard deviation of 2.4 percent and a cross-correlation with output of −0.53 when spread variation is incorporated; holding spreads constant roughly halves the volatility (to 1.3 percent) and reduces the countercyclicality (cross-correlation −0.31).

Model Aggregate Findings.

Consumer credit is procyclical (cross-correlation with output 0.56 in data, 0.67 in model) and more than twice as volatile as output (standard deviation ratio 2.11 in data, 1.51 in model).
Capital quality shocks and monetary policy shocks are amplified at the aggregate level through a financial accelerator working through endogenous spread movements. TFP shocks generate little spread amplification because households’ labor supply responses partially insulate banks’ net worth.
A 1 percentage point contractionary monetary policy shock leads to a sharp, persistent decline in aggregate output and investment, and is amplified relative to a constant-spread HANK benchmark.

Distributional Findings.

In response to a contractionary monetary policy shock, consumption of households at the 10th percentile of the consumption distribution (who are indebted) falls sharply in the short run, while consumption of the 90th percentile (wealthy households) rises in the short run due to higher returns on savings. The responses converge across the distribution in the medium run as spreads normalize.
When the consumer credit spread is held constant, consumption paths move in parallel across the wealth distribution, demonstrating that endogenous spread movements are the key driver of distributional effects for monetary policy and capital quality shocks.
The MPC is countercyclical in the model, with a cross-correlation with output of −0.60 (unconditional), compared with −0.53 for the empirically-estimated consumption-income elasticity. The consumption-income elasticity and MPC are correlated at 90 percent in the model at the annual rate.

Macroprudential Regulation.

A tightening of bank capital requirements reducing leverage by 10 percent (diversion parameter λ rising from 0.381 to 0.445) reduces output volatility by 5.5 percent and investment volatility by 10.1 percent, and does so at apparently no long-run aggregate cost in the HANK setting (precautionary savings stimulate output and consumption in the stationary equilibrium).
However, the regulation increases the annual consumer credit spread by 40 basis points, raises household consumption volatility across the wealth distribution (from about 8 percent to 10 percent for the poorest households under idiosyncratic shocks alone), and generates welfare losses across all deciles equivalent to 0.24–4.28 percent of consumption (with aggregate welfare loss of 0.79 percent).
When aggregate shocks are included, the lower cyclical sensitivity of spreads partially mitigates welfare losses for the poorest 80 percent of the population, but the overall welfare effect remains negative with an aggregate loss equivalent to 0.58 percent of consumption. The paper thus documents a trade-off between macro volatility (stabilized) and micro volatility (increased).
Results are robust to the extension of the model to three assets (including illiquid assets), which provides a better fit to micro data without materially changing the welfare conclusions.

In depth

Q1. What is the specific Danish dataset used, and how is consumption constructed?

A: The dataset covers 2003–2018 from Statistics Denmark administrative registers, combining income tax return data (which report end-of-year balances on all bank accounts, housing wealth, portfolio wealth, bank deposits, bank loans, and mortgage debt) with bank-level MFI interest rate reporting submitted to Danmarks Nationalbank. The total sample is approximately 15.5 million household-year observations (about 1.76–1.97 million households per year). Consumption is imputed as after-tax labor income plus after-tax financial income minus the change in end-of-year net worth, following Crawley and Kuchler (2023). Households with self-employment, housing transactions in the current or prior year, negative imputed consumption, or in the bottom and top 1 percent of wealth or income distributions are excluded.

Q2. How are household-specific credit spreads constructed from the administrative data?

A: Each household’s primary loan bank is defined as the bank where it holds the largest loan balance at end of calendar year, and the primary deposit bank as the one holding the largest deposit balance. The household-specific spread is the difference between the loan rate applied by the primary loan bank and the deposit rate applied by the primary deposit bank, both measured as averages over the calendar year. If a household has no loans, the loan rate of the primary deposit bank is used. This construction yields a household-level interest rate spread that moves countercyclically at the aggregate level (cross-correlation with HP-filtered output of −0.44).

Q3. What do the empirical results say about the relationship between spreads and the probability of a household reaching zero net wealth?

A: Equation (2) is estimated as a linear probability model for the transition to zero net wealth (defined as net assets within plus or minus two weeks of 2007 median weekly income). Higher spreads significantly increase the transition rate into zero net wealth for households with moderately positive net wealth at the beginning of the year (those in the third to sixth net wealth bins), and reduce the outflow rate from zero net wealth for households already in that state. Higher spreads also appear to increase debt repayments for indebted households (third to fifth bins), making it more difficult for them to accumulate wealth. Households at the extremes of the wealth distribution (very poor or very wealthy) show essentially no sensitivity of transition rates to spread movements.

Q4. What do the consumption regressions in Table 1 find, and what is the key identification caveat?

A: The pooled regression (column 1) finds a positive income–consumption coefficient of 0.372, a negative spread coefficient of −0.266, and a positive income–spread interaction of 1.366, all statistically significant with standard errors clustered at the household level (15,610,327 observations, R² = 0.591). When interacted with below-median wealth (column 2), the income coefficient is larger (0.397 versus 0.335 for above-median), the spread effect is more negative for below-median wealth (−0.362 versus −0.101 for above-median), and the income–spread interaction is stronger for below-median wealth (1.640 versus 0.875). The authors explicitly note that these results should not be given a causal interpretation, as income and consumption are likely jointly determined. Institutional features of the Danish mortgage market (covered bonds, competitive market, rates independent of borrower credit situation) minimize confounding from mortgage rate correlation with consumer credit spreads.

Q5. How do the quantile regression results and the derived consumption-income elasticity demonstrate countercyclical MPC?

A: Quantile regressions across five-percent bins of the net wealth distribution show that income coefficients decline with wealth (from nearly 0.5 for the poorest to about 0.35 for the wealthiest households), spread coefficients are negative for households with negative, zero, and moderately positive wealth and positive for significantly wealthy households, and the income–spread interaction term is positive for all but the richest households (largest near zero net wealth). The consumption-income elasticity is computed as β₀,ⱼ + β₂,ⱼ × spread at the household level, then averaged cross-sectionally. When only wealth distribution shifts are allowed, the elasticity’s standard deviation is 1.3 percent and its cross-correlation with HP-filtered output is −0.31. When spread variation is also incorporated, standard deviation rises to 2.4 percent and the cross-correlation becomes −0.53. This measure is highly correlated (90 percent) with the model MPC, supporting the inference that the MPC is countercyclical.

Q6. What is the structure of the banking sector in the HANK model, and how does the agency friction generate a countercyclical spread?

A: A continuum of banks combines household deposits with net worth to invest in corporate equity and consumer loans. Bankers can divert a fraction λ = 0.381 of assets, and if they do so, depositors can recover only the remaining fraction (1 − λ). This threat of diversion constrains the supply of deposits, resulting in banks needing to earn excess returns — Et(RK,t+1 − RS,t+1) > 0 — on their assets relative to the deposit rate. The leverage ratio is bounded above by ϱt/λ, where ϱt is a value multiplier that depends on current and expected future excess returns. When an adverse shock (capital quality shock or monetary tightening) reduces banking sector net worth, the leverage constraint tightens, banks reduce asset supply, and the spread between the return on capital (and hence the consumer loan rate, which is proportional to RK at markup ωB = 0.0075) and the deposit rate rises. This generates the observed countercyclical credit spread.

Q7. In the model, how do aggregate shocks affect the distribution of consumption, and why is the monetary policy shock particularly distributional?

A: A one-percent capital quality shock reduces both wages and bank net worth, causing spreads to rise. In the baseline economy, rising borrowing rates lead to a large reduction in consumption for indebted households (10th percentile) while the constant spread model shows near-parallel movements across the distribution. A one-percentage-point monetary policy shock reduces equity returns, depressing bank net worth and (with a lag) raising spreads. Indebted households face both lower labor income and higher borrowing costs, producing a sharp consumption decline at the 10th percentile; wealthy households gain from higher returns on savings, so their consumption rises in the short run. Responses converge as spreads return to normal over the medium run. This matches empirical evidence from Holm, Paul, and Tischbirek (2021) for Norway. For TFP shocks, banks’ net worth is less affected because households’ higher labor supply partially offsets the productivity decline, so spreads move little and distributional effects are smaller (driven mainly by wage effects across the distribution).

Q8. How does the financial accelerator in the HANK model compare to the RANK version?

A: In response to capital quality shocks and monetary policy shocks, the HANK model with banking frictions generates amplification relative to a constant-spread HANK benchmark, confirming the presence of a financial accelerator. However, relative to the RANK model, the incomplete markets model implies slightly less amplification of aggregate investment and consumption. This is because, in the HANK model, households facing higher credit spreads increase their labor supply (precautionary motive), which partially stabilizes aggregate income and moderates the financial accelerator. The finding that heterogeneous agent aspects are less important at the aggregate level is consistent with Berger, Bocola, and Dovis (2020). For TFP shocks, the financial accelerator through spreads is largely absent in both HANK and RANK, as spread changes are minor.

Q9. What are the long-run aggregate effects of tightening bank capital requirements (reducing leverage by 10 percent) in the HANK versus RANK model?

A: In the RANK model, higher capital requirements increase the annual spread between the return on capital and the deposit rate by 25 basis points, reduce the aggregate capital stock by 2.4 percent, output by 0.5 percent, and aggregate consumption by 0.8 percent. In the HANK model, the spread increases by 40 basis points annually, but the mechanism differs: much of the spread change is absorbed by a reduction in the deposit rate (from 3.81 percent to 3.54 percent annually) rather than an increase in the capital return. Households respond to the lower deposit rate and higher credit costs by increasing precautionary savings and labor supply, so aggregate output and consumption actually rise slightly in the HANK stationary equilibrium. The capital requirements thus appear costless at the aggregate level in the HANK model — but this masks welfare costs that operate through the idiosyncratic risk channel.

Q10. What are the quantitative welfare costs of macroprudential regulation, and how do they vary across the wealth distribution and between idiosyncratic and aggregate shocks?

A: Welfare is measured as the fraction of lifetime consumption households are willing to give up to stay in the unregulated baseline. In the face of idiosyncratic shocks only, welfare losses range from 0.24 to 0.43 percent of consumption for the first seven wealth deciles, and reach 4.28 percent for the richest decile (primarily because of the reduction in the return on their savings), with an average welfare loss of 0.79 percent. When aggregate shocks are added, the losses are substantially reduced for the poorest 80 percent (due to lower cyclical sensitivity of spreads), but remain large for the wealthiest decile (4.23 percent) and in aggregate (0.58 percent). These results are robust to the three-asset model extension, where the poorest households are approximately welfare-neutral under the regulation when aggregate shocks are included (0.00 percent), but aggregate welfare losses remain at 0.75 percent.

Q11. How does the three-asset model extension (with illiquid assets) affect the key results?

A: In the three-asset extension, households can hold illiquid capital (calibrated with an adjustment probability of φk = 0.0025 per quarter, targeting the Danish ratio of bank deposits to output of 34 percent), creating wealthy hand-to-mouth households who have illiquid assets but no liquid assets. The consumption impulse responses across the wealth distribution remain very similar to the two-asset baseline: endogenous spread movements generate heterogeneous consumption dynamics in response to capital quality and monetary shocks, while constant-spread models produce near-parallel responses. The three-asset model provides a better fit to the micro data (consumption-spread-income relationship across the wealth distribution), but the welfare conclusions from macroprudential regulation are essentially unchanged: welfare losses across the distribution in the stationary equilibrium, partially mitigated when aggregate shocks are added, with losses concentrated in the richest decile.

Q12. What robustness checks are reported for the empirical consumption regressions?

A: Three robustness exercises are reported. First, capitalizing car purchases using their official tax value (rather than treating car purchases as current expenditure) yields coefficients similar to the baseline (Table 10). Second, excluding households who purchase a car in the current or prior year (reducing the sample to 13.24 million observations) also leaves results unchanged. Third, first-differenced specifications (equation 42, with and without household fixed effects) produce results similar to the levels specification; the main exception is the spread effect for above-median wealth households when household fixed effects are omitted from the differenced specification (Table 11). The income–spread interaction is consistently positive and significant across all robustness checks.

Q13. What evidence does the paper provide that the model’s MPC is countercyclical and that credit spreads are the primary driver?

A: Figure 7 shows impulse response functions of the average MPC to each of the three aggregate shocks. In all three cases, the MPC rises in recessions (countercyclical). The key mechanism is that adverse shocks cause spreads to rise, increasing the mass of households at the kink in the budget constraint (zero liquid assets), where MPCs are highest. When the consumer credit spread is held constant, the MPC remains countercyclical but close to constant, indicating that spread movements account for most of the cyclical variation in MPC. Eliminating the spread altogether implies an acyclical MPC (Table 12, Appendix D). The unconditional cross-correlation of the model MPC with output is −0.60, compared with −0.53 for the empirically estimated consumption-income elasticity in the Danish data.

Key Concepts

Consumer credit spread (borrowing-saving spread): In the paper, this is the difference between the gross real interest rate on consumer loans (RL,t) charged by banks and the gross real return on deposits (RS,t) received by savers. It is not an abstract measure of credit conditions but a household-specific, bank-derived rate gap that moves countercyclically due to banking agency frictions and creates a kink in households’ budget constraints at zero net worth. Distinct from mortgage spreads (which in Denmark are market-determined and independent of borrower credit conditions).

Kink in the budget constraint: The household budget constraint has a kink at zero net assets because borrowers face RL,t > RS,t; households at exactly zero liquid assets (type IV in the paper’s taxonomy) face a discrete jump in the cost of additional borrowing. This kink creates a mass point in the wealth distribution at zero net wealth, and households at this kink have higher MPCs than unconstrained savers or borrowers. The size of the mass point increases when the spread rises.

Financial accelerator (in the HANK-with-banking context): The amplification mechanism in which shocks that reduce banking sector net worth tighten banks’ leverage constraints, raise credit spreads, reduce asset supply to both the corporate sector and households, and further depress investment and consumption — which in turn reduces bank net worth further. In this paper, the accelerator operates through the consumer credit spread channel in addition to the standard corporate lending channel, and is present for capital quality and monetary policy shocks but not materially for TFP shocks.

Countercyclical MPC: The MPC — defined as the response of consumption to a small transitory income shock — rises during recessions and falls during expansions in this model. The mechanism is that recessions are associated with higher consumer credit spreads, which expand the mass of households at or near the zero net wealth kink (high MPC), and contract the mass of unconstrained savers (low MPC). This is a distinct source of MPC cyclicality from the wealth distribution channel alone.

Agency friction (diversion problem): Banks can divert a fraction λ of their assets; if they do so, depositors can recover only the fraction (1 − λ) and the bank is liquidated. This threat limits depositors’ willingness to supply funds, resulting in an incentive-compatibility constraint on bank leverage: assets cannot exceed ϱt/λ (where ϱt is the bank’s franchise value multiplier). When ϱt declines (because expected excess returns fall), the constraint binds more tightly and the spread between the return on assets and the deposit rate must be positive to sustain bank participation.

Macro versus micro volatility trade-off: The paper uses this phrase to describe the finding that tighter bank capital requirements (restricting leverage) reduce the cyclical volatility of aggregate output and investment (macro volatility falls) while simultaneously increasing the volatility of individual household consumption streams due to higher credit spreads and lower deposit returns (micro volatility rises). Welfare costs from increased micro volatility outweigh the aggregate stabilization benefits.

Consumption-income elasticity (d log c / d log y): A time-varying cross-sectional average measure derived from quantile regression parameter estimates, equal to β₀,ⱼ + β₂,ⱼ × RSi,t for household i in wealth bin j. It is used in the paper as an empirical proxy for the MPC (not a direct estimate), and is shown to be highly correlated with the model MPC (cross-correlation of 90 percent at the annual rate). Its cyclicality is stronger when spread variation is incorporated (standard deviation 2.4 percent, cross-correlation with output −0.53) than when spreads are held fixed (standard deviation 1.3 percent, cross-correlation −0.31).

Firm Responses and Wage Effects of Foreign Demand Shocks with Fixed Labor Costs and Monopsony

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

Layer 1 — Overview

Research Question. The paper asks three related questions in the context of Belgium, a small open economy: (1) What do firms’ responses to demand shocks reveal about their cost structures? (2) What are the worker and wage impacts of foreign demand shocks? (3) How sensitive are the aggregate wage effects of foreign demand shifts to firms’ cost structures and imperfect competition in the labor market?

Data. The analysis combines administrative micro-data from Belgium for 2002–2014, provided by the National Bank of Belgium. The linked dataset covers 995,739 firm-year observations from private, non-financial firms with at least one FTE employee, and integrates: (a) a Business-to-Business (B2B) VAT transactions registry capturing all annual domestic firm-to-firm sales above €250; (b) customs records and intra-EU declarations for imports and exports at the 8-digit product level; (c) annual accounts containing data on sales, labor costs, intermediate inputs, capital, and firm characteristics; and (d) employer-employee matched data from the Belgian social security administration (BCSS) for a random sample of 500,000 workers in firms with 10 or more FTE employees, covering 2003–2014.

Identification Strategy. To isolate variation in firms’ sales driven by foreign demand rather than supply-side factors, the authors construct a firm-specific foreign demand instrument following Hummels et al. (2014) and Dhyne et al. (2021). The instrument is the weighted average of changes in world import demand facing a firm, using lagged export shares as weights and excluding Belgian imports from the world import measure. Crucially, the instrument captures both direct foreign demand exposure (for exporters) and indirect exposure through the domestic production network — including the foreign demand shocks passing through to upstream domestic suppliers via buyer-supplier links. Firm and industry-year fixed effects control for time-invariant heterogeneity and industry-level trends.

Key Empirical Facts. Within-firm analysis over four-year windows finds that intermediate input purchases respond nearly proportionally to changes in sales (slope coefficient 0.82), while labor costs respond less than proportionally (slope coefficient 0.57). The less-than-proportional response of labor costs — with the employment slope of 0.48 and the average wage slope of 0.09 — is consistent with sizable fixed overhead costs in labor inputs and upward-sloping labor supply curves. Output prices co-move more with input prices than with average wages, consistent with labor constituting a smaller share of variable costs than intermediate inputs.

IV Estimates of Firm Responses. In response to a foreign demand shock inducing a 10 percent instantaneous increase in a firm’s sales, the firm’s cumulative sales over four years increase by approximately 7.6 percent (balanced panel). Over the same four-year horizon, total input purchases increase by about 7.0–7.8 percent, while labor costs increase by only 3.5–4.1 percent — a substantially less-than-proportional response. Roughly one-quarter of the labor cost change comes from changes in average wages rather than employment changes. Domestic input purchases increase by 5.3–6.0 percent, indicating that firms pass on a large share of foreign demand shocks to their domestic suppliers.

Structural Parameters. The implied IV estimate of the labor cost elasticity with respect to sales is 0.53 (standard error 0.08), statistically significantly below one. The implied elasticity of total input purchases is 1.05 (standard error 0.15), close to one, so the fixed share of intermediate inputs is approximately zero. The labor supply elasticity estimated from the ratio of wage and employment responses is approximately 3.9 in the full sample and 2.3 in the stayer subsample; the implied wage markdown is 21 percent and 30 percent respectively. Incorporating upward-sloping labor supply into equation (15), the estimated share of total labor inputs that is fixed overhead is approximately 53 percent. By comparison, the fixed share of total costs (labor and intermediate inputs combined) is approximately 29 percent in Belgium — higher than the 18–22 percent found in U.S. data (De Loecker et al. 2020) and the 20 percent found in U.S. manufacturing plants (Ederhof et al. 2021).

General Equilibrium Counterfactuals. The authors parameterize and solve a small open economy general equilibrium model with monopsonistic competition in labor markets, monopolistic competition in product markets, and fixed and variable labor and intermediate input costs. Using the Dekle-Eaton-Kortum (2007) “hat algebra” technique, they simulate a 5 percent increase in foreign tariffs on all Belgian exports and compare four counterfactual economies: (1) baseline Belgium with fixed costs and imperfect labor market competition (ε = 3.9); (2) fixed costs and perfectly elastic labor supply (ε = ∞); (3) no fixed costs with imperfect competition; (4) no fixed costs and perfectly competitive labor markets.

Main Findings on Wages. In the baseline Belgian economy, a 5 percent increase in foreign tariffs produces a 4.9 percent fall in the average real wage. With fixed costs but perfectly elastic labor supply, the real wage falls by 4.8 percent — nearly identical. With upward-sloping labor supply but no fixed costs, the real wage falls by only 3.0 percent; without fixed costs and with perfectly competitive labor supply, the fall is only 2.8 percent. The paper concludes that fixed overhead costs in labor substantially amplify real wage declines, while incorporating upward-sloping labor supply appears quantitatively less consequential for aggregate wage outcomes. Standard models that assume no fixed costs and perfectly elastic labor supply — the typical modeling choice in the trade literature — may substantially understate (by roughly 43–75 percent of the true effect) the aggregate wage decline from a negative foreign demand shock.

Mechanism. Fixed overhead costs reduce labor’s share of variable costs. When labor is a smaller share of variable costs, output prices are less sensitive to changes in wages. With a fixed aggregate labor supply, the economy must lower prices through wage reductions to restore equilibrium after a negative demand shock; the required wage decline is larger when fixed labor costs are taken into account. The findings are robust to adjustment cost specifications, a nested logit extension of the labor market model, and controlling for location-year fixed effects and import price changes.

In depth

Q1. What two motivating empirical facts about Belgian firms does the paper establish?

A1: First, within-firm four-year changes show that intermediate input purchases respond nearly proportionally to changes in sales (slope coefficient 0.82), while labor costs respond less than proportionally (slope coefficient 0.57). The labor cost response decomposes into an employment slope of 0.48 and a wage slope of 0.09. Second, output prices co-move more strongly with input (intermediate goods) prices than with average wages, consistent with labor constituting a smaller share of variable costs than intermediate inputs.

Q2. How does the instrument for foreign demand shocks capture indirect exposure through production networks?

A2: The instrument for firm k is a weighted average of changes in world import demand, where the weights reflect both the firm’s own direct export shares across countries and products and the firm’s indirect export exposure through its domestic buyers’ export shares. The term H̃_{kn,t-1} captures the share of firm k’s total sales purchased by firm n directly and indirectly through all upstream chains. This means even non-exporting firms receive a non-zero instrument through their sales to directly-exporting firms. In fact, non-directly-exporting firms sell on average nearly 10 percent of their output indirectly to foreign markets.

Q3. What is the estimated magnitude of the labor supply elasticity facing Belgian firms, and what does it imply for wage markdowns?

A3: In the full main estimation sample (balanced panel), the IV estimate of the firm-specific labor supply elasticity is approximately 3.9, implying a wage markdown of about 21 percent relative to the marginal revenue product of labor. In the stayer subsample (incumbent workers only, holding workforce composition fixed), the estimated labor supply elasticity is approximately 2.3, implying a markdown of about 30 percent. The paper can reject perfect competition (infinite elasticity, zero markdown) at a significance level of 0.06 in the full sample and 0.001 in the stayer sample using the closure method.

Q4. What is the estimated labor cost elasticity with respect to demand-driven sales changes, and what does it imply about fixed labor costs?

A4: The IV estimate of the labor cost elasticity with respect to sales is 0.528 (standard error 0.085), statistically significantly below one. If labor supply were perfectly elastic, this would directly imply a fixed labor cost share of approximately 47 percent. Incorporating the estimated upward-sloping labor supply curve through equation (15), the model implies that approximately 53 percent of total labor inputs are fixed overhead. For context, occupational data from Belgium’s 2014 Structure of Earnings Survey shows that clerical support workers and managers together account for 21 percent of total earnings, and adding professionals raises this to 51 percent — broadly consistent with the estimated fixed share.

Q5. What does the estimated elasticity of input purchases with respect to sales imply about fixed intermediate input costs?

A5: The IV estimate of the elasticity of total input purchases with respect to sales is 1.050 (standard error 0.150), close to one. The implied fixed share of total intermediate inputs is therefore approximately zero. However, there is substantial heterogeneity by input type: purchases from the manufacturing sector (roughly half of all input purchases) have an elasticity close to one, whereas service-sector inputs (roughly 30 percent of total input purchases) have an implied fixed cost share of approximately 36 percent, with a size-weighted average cumulative response of 4.3 percent against a total cumulative sales increase of 6.7 percent.

Q6. How does the paper rule out alternative explanations for the less-than-proportional response of labor costs?

A6: The paper considers three main alternatives. First, adjustment costs: even in the presence of labor adjustment costs, under a homothetic constant-returns production function a permanent shock should eventually produce a proportional labor response. The paper focuses on four-year cumulative responses where firm responses change little after the first couple of years, and shows identification of fixed costs holds even in models with quadratic or Calvo-style adjustment costs. Second, a non-homothetic CES production function without fixed costs: Appendix B.3 shows that such a specification predicts that if the labor cost elasticity is below one, the input purchase elasticity must be above one — at odds with the data, which shows the input purchase elasticity is close to one while the labor cost elasticity is well below one. Third, variable markups: a uniform markup change would reduce both elasticities proportionally, not create the large gap between labor cost and input purchase elasticities observed.

Q7. Why are firms’ domestic suppliers affected by foreign demand shocks, and how large are the pass-through effects?

A7: Firms pass on foreign demand shocks to their domestic suppliers through buyer-supplier production network links. When a foreign demand shock increases a firm’s sales by 10 percent instantaneously, its domestic input purchases increase cumulatively by approximately 5.3–6.0 percent over four years. Total input purchases increase by 7.0–7.8 percent over the same period; the difference between total and domestic input purchases reflects service inputs (which have smaller responses) and the composition of imported versus domestic inputs.

Q8. What is the aggregate real wage effect of a 5 percent increase in foreign tariffs on Belgian exports in the baseline model?

A8: In the baseline counterfactual representing the actual Belgian economy (with fixed overhead costs and labor supply elasticity ε = 3.9), a uniform 5 percent increase in foreign tariffs on all Belgian exports produces a 4.9 percent fall in the average real wage. The median firm reduces output by 3.8 percent, marginal costs by 4.8 percent, and wages by 7.9 percent. The fall in wages is driven by a general equilibrium mechanism: since the foreign price is exogenous and trade balance must hold, wages are the key adjusting margin.

Q9. How much does the modeling of fixed overhead costs versus imperfect labor market competition matter for the aggregate wage counterfactual?

A9: Fixed overhead costs account for nearly all of the amplification relative to the standard model. With fixed costs but perfectly elastic labor supply, the real wage falls 4.8 percent — almost identical to the 4.9 percent in the baseline. Without fixed costs but with the estimated upward-sloping labor supply, the fall is only 3.0 percent. Without either, the fall is 2.8 percent. Thus, incorporating fixed overhead costs in labor raises the estimated wage decline by approximately 1.9 percentage points, while incorporating imperfect labor market competition adds only about 0.1 percentage points. The paper concludes that fixed overhead costs, not monopsony, are the essential feature for accurately predicting tariff impacts on wages.

Q10. What is the mechanism by which fixed overhead costs amplify the aggregate wage decline from a negative demand shock?

A10: Fixed overhead costs reduce the share of labor in firms’ total variable costs. When labor constitutes a smaller fraction of variable costs, output prices are less sensitive to changes in wages. With aggregate labor supply fixed, the economy restores equilibrium after a negative demand shock by reducing prices through wage cuts. To achieve the same magnitude of price reduction when labor is a smaller fraction of variable costs, wages must fall by a larger amount — amplifying the aggregate wage impact. Fixed overhead costs in labor also make foreign inputs relatively more important in variable costs, as shown empirically in Appendix D.1.

Q11. Is the conclusion about the relative importance of fixed costs versus labor market imperfections robust to alternative specifications of the labor market?

A11: Yes. The paper extends the model to a nested logit structure for worker preferences (following Lamadon et al. 2022), which allows Belgium to contain multiple labor markets (defined as industry-region nests), permits heterogeneous markdowns across markets, and is still identified from the data. Empirically, incorporating multiple labor markets and heterogeneous markdowns does not quantitatively alter the aggregate counterfactual predictions for the wage effects of foreign demand shocks.

Q12. Are heterogeneous responses to the foreign demand shock observed across exporters, importers, and domestic-only firms?

A12: The paper finds no systematic differences in the elasticities of labor cost and input purchases between firms that trade internationally and those that do not. This implies that exporters and importers have higher absolute fixed costs (consistent with fixed export and import costs) but comparable fixed cost shares — since these firms tend to be larger and thus spread higher absolute fixed costs over larger output volumes.

Q13. Do the findings about fixed overhead costs extend beyond foreign demand shocks?

A13: Yes. The paper shows in Appendix D.4 that a uniform 5 percent reduction in the productivity of all Belgian manufacturing firms generates qualitatively and quantitatively similar conclusions: fixed overhead costs amplify the predicted wage effects of domestic productivity shocks, while imperfect competition in the labor market matters to a lesser but still meaningful extent.

Key Concepts

Fixed Overhead Costs (Fixed Labor Costs / Fixed Intermediate Input Costs): In the paper’s model, each firm has firm-specific fixed overhead input requirements for labor (denoted ℓ̄_k^f) and intermediate inputs (denoted q̄_k^f) that must be satisfied regardless of the firm’s output level. These fixed requirements are separate from the variable inputs used in production. Fixed labor costs may reflect administration, worker management, facility maintenance, and other tasks that do not directly translate into output. Fixed intermediate input costs include waste management, accounting services, and electricity payments that occur irrespective of sales. The share of total labor inputs that is fixed is identified by how much less than proportionally labor costs respond to demand-driven changes in sales.

Monopsonistic Competition in the Labor Market: The paper models each firm as facing an upward-sloping firm-specific labor supply curve arising from workers’ heterogeneous idiosyncratic preferences over non-wage firm attributes (amenities). Because workers’ idiosyncratic tastes are private information, firms cannot price-discriminate and thus face an increasing marginal cost of labor. Each firm is infinitesimal within the aggregate labor market but has wage-setting power at the firm level. This gives rise to a constant-elasticity firm-level labor supply curve ℓ_k = A_k w_k^ε, where ε is the labor supply elasticity facing the firm.

Wage Markdown: The firm’s equilibrium wage is marked down relative to the marginal revenue product of labor by the factor ε/(1+ε), which is less than one when ε is finite. With a labor supply elasticity of 3.9, the implied markdown is approximately 21 percent; with a supply elasticity of 2.3 (stayer sample), the markdown is approximately 30 percent. Perfect competition corresponds to ε = ∞ and a markdown of zero.

Labor Cost Elasticity: The elasticity of a firm’s total labor cost with respect to a demand-driven change in the firm’s sales, as derived from the model’s comparative statics (equation 15). This elasticity depends on both the variable share of labor inputs (ℓ_k^v / ℓ_k) and the labor supply elasticity ε. It lies strictly between zero (all labor fixed) and one (all labor variable), and is declining in ε for a given variable share. The paper estimates this elasticity at 0.528 via IV, implying substantial fixed overhead in labor.

Total Foreign Demand Shock: The firm-level measure of foreign demand used as an instrument, defined as the weighted average of changes in world import demand (excluding Belgium) across country-product pairs, where the weights reflect both the firm’s own lagged direct export shares and its indirect exposure through the domestic production network (via the Leontief inverse matrix H̃). This measure captures both direct exporter exposure and indirect upstream exposure for non-exporting firms that supply to exporters.

Indirect Export Exposure: The share of a firm’s output that reaches foreign markets indirectly through sales to domestic buyers who subsequently export. Defined recursively: the total export share of firm k equals its direct export revenue share plus the sum over all domestic buyers of the product of k’s revenue share from that buyer and the buyer’s own total export share. Even non-direct-exporting firms sell on average approximately 10 percent of their output indirectly to foreign markets in the Belgian data.

Dekle-Eaton-Kortum Hat Algebra: A technique for solving general equilibrium counterfactuals in trade models by expressing all outcomes as proportional changes (“hats”) relative to the observed equilibrium, without needing to recover the underlying structural parameters. The paper uses this approach to compute counterfactual wages under alternative tariff scenarios, holding fixed the observed firm-level expenditure shares from the reference year (2012) while allowing parameters such as productivity and technology weights to vary across counterfactual economies to rationalize identical observed firm-level observables.

Worker Rents: In the monopsony model, inframarginal workers earn rents defined as the excess return over what would be required to make them indifferent between employers. These rents arise because firms cannot price-discriminate across workers with heterogeneous amenity valuations. The additional rents accruing to workers from a demand-driven increase in firm sales decompose into: (1) wage increases for incumbent workers multiplied by current employment, (2) rents for new hires (the excess of their wage bill over the amount required to induce them to switch to the expanding firm), and (3) a correction term related to the fraction of the labor cost increase borne by expanding employment rather than wages.

Germs in the Family: The Short- and Long-Term Consequences of Intra-Household Disease Spread

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

This paper studies the short- and long-term consequences of intra-household respiratory disease transmission from older to younger siblings in Danish families. The central research questions are: (1) how do respiratory illnesses spread from preschool-aged older siblings to younger infant siblings during the first year of life, and (2) how does respiratory disease exposure during infancy causally affect younger siblings’ long-term economic, human capital, and health outcomes?

The study uses population-level Danish administrative data covering 1,230,180 children from 37 birth cohorts (1981–2017), linking records from the National Patient Register, income and labor market registers, education registers, and psychiatric care registers. The identification strategy combines birth order variation in respiratory disease vulnerability with within-municipality variation in local respiratory disease prevalence among children aged 13–71 months. The authors construct a municipality-level disease exposure index—cumulative respiratory hospitalizations per 100 children aged 13–71 months in a child’s municipality over their first 12 months of life—and estimate the differential effect of this index on younger versus older siblings, controlling for municipality fixed effects, birth year-month fixed effects, and an extensive set of individual and family background characteristics.

The descriptive findings are stark: younger siblings have 2–3 times higher rates of hospitalization for acute respiratory conditions during their first year of life compared to older siblings at the same age, with the gap largest at ages two and three months. The gap is larger for winter births, shorter birth spacing, and when older siblings attend childcare centers—all patterns consistent with the older sibling serving as a disease vector.

On the causal estimates, moving from the 25th to the 75th percentile of the disease exposure index distribution increases the younger sibling’s acute respiratory hospitalizations in the first year of life by 0.023 (32.9 percent above the sample mean), with effects more than twice as large for exposure in the first six months compared to the second six months.

In the long run, an interquartile increase in first-year respiratory disease exposure reduces younger siblings’ wage earnings (conditional on employment) at ages 25–32 by 0.8 percent and total income by 0.8 percent, and reduces their income percentile rank by 0.3 percentage points. There is no significant effect on labor force participation at the extensive margin. Effects on earnings are approximately twice as large when exposure is measured in the first six months of life. These earnings effects are comparable in magnitude to those from a 10 percent reduction in birth weight or a 9 percent increase in ambient air pollution at birth, and correspond to roughly two-thirds of the adult earnings impact of in utero exposure to the 1918 Spanish Influenza. When the disease index interaction is included, the main birth order coefficient declines by approximately 70 percent, suggesting intra-household disease transmission is an important channel underlying the documented birth order earnings disadvantage.

Additional findings include: a 0.5 percentage point reduction in high school graduation and a 0.6 percentage point reduction in college graduation (interquartile effects); a 0.01 standard deviation penalty in ninth grade Danish test scores; a 20 percent increase (0.016 per hundred per year) in chronic respiratory hospitalizations at ages 16–26; and a 6.1 percent increase (0.5 additional visits per hundred per year) in psychiatric clinic visits at ages 16–26. Breastfeeding mitigates short-term effects, with 15 months of breastfeeding sufficient to entirely offset the elevated hospitalization risk.

Scope conditions: findings apply to second-born relative to first-born children in Danish sibling pairs with at least 11 months birth spacing; long-term estimates are net of parental compensatory responses and any immunity benefits, and thus represent lower bounds of the uncompensated biological impact of respiratory illness in infancy.

Q: What is the magnitude of the birth order gap in acute respiratory hospitalizations during infancy, and what patterns support an intra-household transmission mechanism? A: Younger siblings have 2–3 times higher hospitalization rates for acute respiratory conditions in the first year of life compared to older siblings at the same age, with the gap especially large at ages two and three months. The gap is larger for winter births (when respiratory viruses circulate more), for siblings with shorter birth spacing, and when the older sibling attends a childcare center. Hospitalizations for non-infectious digestive diseases and injuries show no analogous birth order differences, ruling out differential parental healthcare-seeking as an explanation.

Q: How is the disease exposure index constructed and what variation does it exploit? A: The index is the cumulative count of acute respiratory hospitalizations per 100 children aged 13–71 months in a child’s municipality over their first 12 months of life, with the older sibling excluded from the count when applicable. It exploits irregular spatial and temporal waves of respiratory viruses (such as RSV and influenza) across Danish municipalities. The interquartile range of this index captures meaningful variation in community disease burden faced by infants across different places and years.

Q: What is the first-stage relationship between the disease index and infant hospitalizations? A: Moving from the 25th to the 75th percentile of the disease index increases younger siblings’ acute respiratory hospitalizations in the first year of life by 0.023 (a 32.9 percent increase relative to the sample mean), while the effect on older siblings is substantially smaller. The interaction coefficient in the preferred specification implies that one additional hospitalization per 100 community children aged 13–71 months raises the younger sibling’s hospitalization count by 0.012 more than the older sibling’s. Effects are more than twice as large for exposure in the first compared to the second six months of life.

Q: What are the estimated long-term effects on adult earnings, and how do they compare to benchmarks in the literature? A: An interquartile increase in first-year respiratory disease exposure reduces younger siblings’ wage earnings at ages 25–32 by 0.8 percent and total income by 0.8 percent, with a 0.3 percentage point reduction in income percentile rank. These magnitudes are comparable to a 1 percent earnings reduction from a 10 percent birth weight reduction (Black et al., 2007), a 1 percent earnings reduction from a 9 percent increase in ambient air pollution (Isen et al., 2017b), and roughly two-thirds of the in utero Spanish Influenza effect (Almond, 2006).

Q: Does the birth order earnings disadvantage reflect intra-household disease transmission? A: When the interaction between birth order and the disease index is excluded, the regression finds a 1.9 percent birth order earnings disadvantage for second-born children (consistent with Black et al., 2005 range of 1.2–4.2 percent). When the interaction is included, the main birth order coefficient declines by approximately 70 percent, suggesting that disease transmission from older to younger siblings is an important channel driving the birth order earnings penalty.

Q: Are effects larger for exposure in the first versus second six months of life? A: Yes, consistently across all outcomes. The interaction coefficient for acute respiratory hospitalizations is more than twice as large when exposure is measured in the first versus second six months. Effects on wage earnings are approximately 60 percent larger for first-half exposure, and effects on income rank are two to three times larger. This is consistent with biomedical evidence that infants’ immune systems mature around six months when solid food introduction begins.

Q: What are the effects on educational outcomes? A: An interquartile increase in first-year respiratory disease exposure reduces the likelihood of high school graduation by 0.5 percentage points (0.6 percent at the sample mean) and college graduation by 0.6 percentage points (1.7 percent at the sample mean), with effects approximately 60 percent larger when measuring first-half exposure. A 0.01 standard deviation reduction in ninth grade Danish test scores is also found. A back-of-the-envelope calculation using Danish returns to schooling suggests the reduction in educational attainment can explain approximately half of the estimated earnings effect.

Q: What are the effects on chronic respiratory and mental health outcomes? A: An interquartile increase in first-year exposure increases chronic respiratory hospitalizations (asthma, COPD) at ages 16–26 by 0.016 per hundred per year (20 percent above the sample mean), with significant increases also apparent at ages one to two. For mental health, the same exposure is associated with 0.5 additional psychiatric clinic visits per hundred per year at ages 16–26 (6.1 percent above the sample mean), with effects becoming more significant in the early twenties. Effects on mental health from this paper are smaller than those estimated for more extreme fetal and early childhood shocks such as Ramadan exposure or maternal bereavement.

Q: What does the acute respiratory trajectory look like beyond infancy? A: Elevated acute respiratory hospitalizations persist at age one, then there is a reduction at ages two to three consistent with an immunity formation hypothesis, but this protective effect disappears by age four. There is no significant increase or decrease in acute respiratory hospitalizations at older ages, in contrast to the persistent increase found for chronic respiratory conditions.

Q: What heterogeneity is found in short-term effects? A: Effects on infant respiratory hospitalizations are larger for low birth weight children, for male infants (consistent with the fragile male hypothesis), for siblings with shorter birth spacing, and for sibling pairs where the older child attends childcare. The monotonic decline in effect size with increasing birth spacing is the opposite of what would be predicted if differential parental time investment were the main mechanism, supporting intra-household disease spread as the operative channel.

Q: What is the role of breastfeeding as a moderator? A: Using supplementary data on breastfeeding duration (covering 2009–2016, matched to 7.6 percent of the sample), the authors find that the impact of disease exposure on younger siblings’ infancy hospitalizations declines significantly with longer breastfeeding duration. A linear specification implies that 15 months of breastfeeding entirely offsets the elevated hospitalization risk from higher disease exposure. Second-born children breastfed for less than half a month are particularly vulnerable to acute respiratory infections.

Q: How do the authors validate the identifying assumption? A: Three validation exercises are used. First, results are robust to adding municipality-specific linear and quadratic trends and maternal fixed effects. Second, using family background characteristics as outcomes in the interaction regression, at most two of fourteen coefficients are significant in any specification, and all effect sizes are less than one percent of sample means. Third, using alternative disease indices based on non-infectious digestive diseases and injuries shows no differential effects for younger siblings, ruling out a parental healthcare-seeking confound.

Q: What are the policy implications? A: The authors highlight breastfeeding support policies (paid family leave, workplace lactation accommodations), RSV vaccination campaigns for pregnant women and monoclonal antibody prophylaxis for infants, sick pay regulations, and childcare attendance policies as levers to reduce infant respiratory disease burden. They argue that current cost-benefit evaluations of such policies likely undercount the long-term human capital and earnings benefits. The COVID-19 pandemic illustrates the mechanism: restrictions reduced RSV spread during 2020 potentially benefiting infants with older siblings, while the subsequent RSV surge in 2021–2022 may have exposed later cohorts to above-average disease burden.

Respiratory Disease Exposure Index: A municipality-level cumulative measure of acute respiratory hospitalizations per 100 children aged 13–71 months assigned to each child over their first 12 months of life (or first and second six months separately), designed to proxy for community respiratory disease burden faced by infants from slightly older children, with the child’s own older sibling excluded from the count.

Intra-Household Disease Transmission: The mechanism by which preschool-aged older siblings, exposed to respiratory viruses in group childcare settings, bring home those viruses and infect younger infant siblings who are in a vulnerable stage of immune and brain development, creating a within-family externality in health outcomes.

Differential Birth Order Effect (Identification): The quasi-experimental design exploits the interaction between birth order (younger siblings are more exposed to older siblings’ illnesses) and local disease prevalence variation to identify causal impacts, netting out the main effects of both birth order and local disease environment through municipality and birth year-month fixed effects.

Immunity Formation Hypothesis: The conjecture that early respiratory disease exposure may have a protective effect on later acute respiratory illness through immune system training; supported in the data by reduced acute hospitalizations at ages two to three, though this protection disappears by age four and does not prevent chronic respiratory disease development.

Dynamic Complementarities with Sibling Health Spillovers: An extension of the Cunha-Heckman framework: while standard models incorporate investment complementarities across time periods for a given child, this paper’s findings imply that sibling health spillovers create differential returns to early-life health investments by birth order, since disease asymmetries between older and younger siblings are not incorporated in existing theoretical models.

Net Long-Term Effects: The estimated long-run impacts incorporate not only the direct biological effects of respiratory illness on the younger sibling but also any parental compensatory responses and immunity benefits; thus they represent lower bounds of the uncompensated biological impact, as parental compensation would attenuate the measured sibling difference.

Identifying Preference for Early Resolution from Asset Prices

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

Layer 1: Overview

This paper develops a revealed-preference theory that uses asset-market data to identify whether investors have a preference for early resolution of uncertainty (PER), a property of non-expected utility preferences that is distinct from risk aversion. The central theorem shows that, under a condition called generalized risk sensitivity (GRS), the representative agent prefers early resolution if and only if claims to future stock market volatility earn a positive premium during the period in which the informativeness of upcoming macroeconomic announcements is resolved — a window the authors call the Resolution of Information Quality (ROIQ) period. Using S&P 500 index option data from 1996 to 2019, the paper identifies the ROIQ period as the five weekdays before FOMC announcements, demonstrates that the inverse slope of the implied-volatility term structure (9-day/90-day VIX ratio) significantly predicts the informativeness of upcoming announcements, and finds a statistically significant positive ROIQ premium on synthetic variance claims (beta = 1.085, t = 2.44) and on at-the-money straddles (beta = 0.428, t = 2.25). The evidence supports Epstein-Zin recursive utility with the intertemporal elasticity of substitution exceeding the reciprocal of risk aversion, and hence is consistent with the Bansal-Yaron long-run risk framework. Crucially, this identification requires no parametric calibration of the full asset pricing model.

Summary of a published paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What is preference for early resolution (PER) and why is it hard to identify?

PER means that an agent with a given distribution over future outcomes strictly prefers to learn the outcome sooner rather than later, as formalized by Kreps and Porteus (1978); under Epstein-Zin recursive utility, PER is equivalent to risk aversion exceeding the reciprocal of the IES (or IES > 1/risk aversion). In standard applied asset pricing models with constant-elasticity recursive utility, PER is intertwined with risk aversion and the IES, so that the separate role of the timing of resolution is obscured. Existing papers either test joint implications of the full calibrated model (conflating PER with other preference properties) or use thought-experiment willingness-to-pay calculations without market-data grounding. The authors’ goal is to provide a necessary and sufficient condition for PER directly from asset prices, independent of a fully specified model.

Q2. What is the role of Generalized Risk Sensitivity (GRS) in the identification theorem?

GRS — the condition that the certainty-equivalent functional I is increasing in second-order stochastic dominance — provides the bridge between the unobservable ranking of utility levels across states and the observable ranking of marginal utilities (stochastic discount factors) across those states. The authors prove that under GRS (Theorem 1), the vector of partial derivatives of I with respect to continuation utility is strictly negatively comonotone with the level of continuation utility: higher utility states have lower marginal utility. This inversion is what allows asset prices to reveal the ordering of utility levels. GRS itself is empirically supported by the well-documented fact that assets earn positive announcement premia around scheduled macroeconomic releases (Savor and Wilson, 2013).

Q3. How does the main theorem (Theorem 2) identify PER from a single asset class?

Theorem 2 establishes that, under strict GRS, the premium earned by any asset comonotone with the informativeness of upcoming macroeconomic announcements during the ROIQ period is strictly positive if and only if the agent has PER; a negative ROIQ premium would indicate preference for late resolution. The intuition is that if the agent prefers early resolution, she assigns higher continuation utility to the early-resolution state (0E) than to the late-resolution state (0L); under strict GRS, higher continuation utility maps to lower marginal utility, meaning assets paying off more in the early-resolution state are negatively correlated with the SDF and therefore carry a positive risk premium. Claims to stock market return variance serve as the test asset because expected variance is high before informative announcements (early resolution) and low before uninformative ones (late resolution).

Q4. How do the authors operationalize the ROIQ period empirically?

The ROIQ period is identified as the five weekdays before FOMC announcements, during which market attention to the Fed (measured by RavenPack Fed-related news intensity) is significantly positively correlated with the change in the inverse slope of the implied-volatility term structure (coefficient = 1.076, t = 4.09), while no such correlation exists in the ten days 6–10 before or after the announcement. This correlation arises because, during those five days, investors regularly update their expectations about whether the upcoming FOMC statement will be informative; more expected informativeness raises the demand for short-dated options (driving up the 9-day VIX relative to the 90-day VIX) and simultaneously raises Fed-related news coverage. Outside the ROIQ window, the two series are uncorrelated (coefficient = −0.242, t = −1.13 unconditionally), confirming that the window is the correct testing period.

Q5. What is the empirical evidence for a positive ROIQ premium, and how is it constructed?

Synthetic variance claims constructed as option portfolios following Bakshi, Kapadia, and Madan (2003) earn a ROIQ premium (coefficient beta in the panel regression) of 1.085 percentage points per day (t = 2.44) above their average daily return; at-the-money straddles earn 0.428 pp/day (t = 2.25), both significantly positive. The panel regression controls for maturity fixed effects (11 dummies for weeks to expiration), FOMC-day effects, and day-of-week effects. Crucially, the market itself earns approximately 8 basis points lower than average during the ROIQ period, and the market loading on variance claims does not increase during the ROIQ window (Table 5), ruling out an interpretation in which the premium simply reflects a higher market beta at announcement times.

Q6. How does the paper rule out alternative explanations for the ROIQ premium?

A placebo test using VIX futures — which pay the forward-looking VIX level (expected volatility over the next 30 days after expiry) rather than realized variance over the announcement — shows no significant ROIQ premium, confirming that the effect operates specifically through exposure to volatility during the announcement itself rather than through general volatility-level exposure. The paper also shows that controlling for the Fama-French three factors does not appreciably change the ROIQ coefficient. An additional test using individual stock options (5 weekdays before earnings announcements) also yields positive ROIQ premiums, extending the result beyond FOMC to firm-level announcements.

Q7. What does the finding imply for macroeconomic preference modeling and policy?

The empirical finding that investors have a positive ROIQ premium — i.e., PER — without assuming any particular utility functional form confirms the central calibration assumption of Bansal-Yaron long-run risk models (risk aversion > 1/IES) and provides the market-based evidence that Epstein, Farhi, and Strzalecki (2014) stated was unavailable. The paper’s approach is significant for macro modeling because it establishes PER from minimal assumptions (GRS and monotonicity of preferences), meaning that the result holds across expected utility deviations including robust control, smooth ambiguity, and disappointment aversion preferences — as long as they satisfy GRS — making it a broadly applicable empirical anchor for calibrating non-expected utility models.

Q8. What are the identification limitations and scope conditions?

The identification relies on three maintained conditions: (i) GRS holds for the representative agent, (ii) FOMC announcements genuinely resolve macro uncertainty (so that the ROIQ window is correctly specified), and (iii) the pre-announcement period does not contain price-relevant news (so that market return premia during the ROIQ are not confounded with the news content of the announcement itself). The empirical support for condition (iii) comes from the fact that the market does not earn abnormal returns during the ROIQ (negative, not positive, as expected from the announcement drift literature), and from the lack of a ROIQ premium for VIX futures that expire after but not over the announcement. The framework abstracts from heterogeneous agents and assumes a representative-agent economy, which is standard but may not fully capture distributional effects.

Key Concepts

preference for early resolution of uncertainty (PER) : the property of a dynamic preference that the agent strictly prefers to learn the realization of a future uncertain outcome earlier rather than later, holding the distribution unchanged; equivalent in Epstein-Zin recursive utility to risk aversion exceeding the reciprocal of the IES.

generalized risk sensitivity (GRS) : the condition that the certainty-equivalent functional I is strictly increasing in second-order stochastic dominance; equivalent to the existence of strictly positive announcement premia for all assets comonotone with continuation utility; the paper’s key maintained assumption connecting utility levels to asset prices.

resolution of information quality (ROIQ) period : the period during which investors learn whether the upcoming macroeconomic announcement will be informative; empirically identified as the five weekdays before FOMC meetings, during which Fed-related news intensity co-moves with the inverse slope of the VIX term structure.

ROIQ premium : the excess return earned by a claim to market volatility (synthetic variance claim or straddle) during the ROIQ period over its average daily return on non-ROIQ days; the paper’s operational test for PER; estimated at 1.085 percentage points per day for variance claims.

inverse slope of the implied-volatility term structure : the ratio IV9/IV90 (9-day CBOE VIX divided by 90-day CBOE VIX); the paper’s market-based predictor of FOMC announcement informativeness; a higher ratio reflects investor anticipation of large announcement-day volatility relative to long-run baseline uncertainty.

Ideological Alignment and Evidence-Based Policy Adoption

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

This paper investigates how the ideological alignment between knowledge-disseminating institutions and policymakers affects the adoption of evidence-based policies. The core research question is whether, and through which mechanisms, the ideology of the messenger — rather than the content of the message — determines whether local policymakers act on rigorous research evidence.

The authors conduct a country-wide randomized controlled trial (RCT) across 5,678 touristic Spanish municipalities. The policy recommendation derives from Hinnosaar et al. (2021), an RCT demonstrating that minor improvements to municipalities’ Wikipedia pages (adding photographs, local festival information, touristic landmark details) increased overnight tourist stays by 9%. This policy was chosen because it is ideologically neutral, low cost, within local policymakers’ remit, and its implementation is directly traceable via Wikipedia edit histories.

Municipalities were randomized into five treatment arms and a control group (approximately 950 municipalities each), stratified by ruling party ideology, population, and touristic accommodation count. Three arms received the same policy brief endorsed by: (1) an ideologically aligned think tank (FAES for right-wing municipalities, Fundación Alternativas for left-wing), (2) the ideologically opposite think tank, or (3) an ideologically nonsalient researcher from the London School of Economics. Two further arms received links to newspaper articles covering the same research from either an ideologically aligned outlet (El Mundo for right, Eldiario.es for left) or an ideologically opposite outlet. The control group received no information. The experiment ran from May to December 2022, with multiple reminder emails sent across the period.

The main outcome is a binary indicator for whether a municipality’s Wikipedia page was changed in line with the recommended guidelines during the study period, coded blind to treatment status by two independent coders.

Key findings: Pooled across all treatment arms, information provision increased the probability of policy adoption by approximately 0.98 percentage points (a 38% relative increase over the control group baseline), but this effect is only marginally above conventional significance thresholds (p-value = 0.13). The aggregate effect masks sharp heterogeneity by ideological alignment. When the informing institution’s ideology aligns with the policymaker’s, policy adoption increases by 1.68 percentage points (think tank) and 1.67 percentage points (newspaper) relative to the control group — equivalent to a 66% and 65% relative increase, respectively, both statistically significant at the 5% level. By contrast, information from an ideologically opposite institution produces a coefficient that is negligible and statistically indistinguishable from zero, indicating that misaligned information is no more effective than receiving no information at all. The ideologically nonsalient LSE researcher arm produced an intermediate effect (0.94 percentage points, 37% relative increase), but the p-value (0.27) exceeds conventional thresholds, and the effect is not statistically distinguishable from either the aligned or the control condition. Policy briefs and newspaper articles are equally effective when ideologically aligned (difference of 0.1 percentage points, p-value = 0.82).

To decompose mechanisms, the authors propose a three-stage framework: (1) selective exposure to information, (2) belief updating, and (3) policy implementation. Email click-through rates (access to the full policy brief or article once the informing institution is revealed) do not differ significantly across treatment arms, ruling out selective exposure as the operative mechanism. A post-intervention online survey experiment with 1,600 policymakers from 1,196 municipalities shows that those receiving information from an aligned or nonsalient institution updated their beliefs about policy effectiveness significantly more than those receiving information from an opposite institution, implicating belief updating as one operative channel. However, comparing the survey experiment (where nonsalient and aligned treatments produce similar belief updating) with the main experiment (where the aligned arm adopts at nearly twice the rate of the nonsalient arm, though not statistically distinguishable) suggests that ideological alignment also affects the third stage — policy implementation — beyond mere belief updating.

The estimated monetary cost of ideological misalignment is 2,192 euros per municipality per year, calculated using the impact of Wikipedia changes on touristic revenues from Hinnosaar et al. (2021).

Scope conditions: The context is Spanish local government, a policy that is explicitly non-ideological, low-cost, and easily implemented. Generalizability to ideologically charged or costly policies is not established. Left-wing municipalities show larger responses to aligned information, though this heterogeneity is not statistically significant at conventional levels.

Q: What is the baseline rate of policy adoption in the control group, and what does the aligned-institution treatment achieve in absolute terms?

A: The paper reports that ideologically aligned institutions increase the share of municipalities implementing recommended Wikipedia changes by 1.68 percentage points (think tank) and 1.67 percentage points (newspaper) relative to the control group. Working backward from the stated 66% and 65% relative increases, this implies a control group baseline of approximately 2.5 percentage points. The aligned effects are statistically significant at the 5% level.

Q: Does information from an ideologically opposite institution have any effect on policy adoption?

A: No. The coefficient for opposite-ideology treatment arms is negligible in magnitude, closely resembling the near-zero coefficients from the placebo analysis conducted for the same months in 2019 (pre-intervention). The authors conclude that receiving information from an ideologically opposite institution is statistically indistinguishable from receiving no information at all. This null result is consistent across heterogeneity analyses by mayor ideology, municipality population, Wikipedia page length, and party type.

Q: How does the ideologically nonsalient (LSE researcher) treatment compare to aligned and opposite arms?

A: The nonsalient arm increases policy adoption by 0.94 percentage points (a 37% relative increase), approximately half the effect of the aligned arm (1.68 percentage points). However, the p-value is 0.27, and the effect is not statistically different from either the aligned arm (p-value = 0.34) or the control group at conventional confidence levels. The result should therefore be interpreted with caution.

Q: Are policy briefs or newspaper articles more effective in promoting policy adoption?

A: Neither format is significantly more effective than the other. Conditional on ideological alignment, the difference between policy brief and newspaper article effects is 0.1 percentage points with a p-value of 0.82. Both are equally effective when ideologically aligned with the receiving policymaker, a finding the authors describe as a novel contribution to the policy communication literature.

Q: Does ideological alignment affect whether policymakers choose to access the full information (selective exposure)?

A: No. Click-through rates on the links to policy briefs or newspaper articles — measured after policymakers have seen the informing institution’s identity — do not differ significantly across treatment arms. The observed average click-through rate is 6.42%. This null result is consistent with the hypothesis that policymakers do not strategically filter information acquisition based on the messenger’s ideology, at least for non-ideological policies.

Q: What does the survey experiment reveal about belief updating?

A: In the post-intervention survey experiment with 1,600 policymakers, participants first reported beliefs about a purportedly beneficial (but actually harmful) policy, then were randomly assigned to receive information about its negative effects from an aligned, opposite, or nonsalient think tank. Those receiving information from an aligned or nonsalient institution updated their beliefs significantly more than those receiving information from an ideologically opposite institution. This implicates belief updating — not just selective exposure — as a channel through which ideological alignment affects policy adoption.

Q: Why do the authors conclude that ideological alignment also affects the third stage (policy implementation) beyond belief updating?

A: In the survey experiment, aligned and nonsalient institutions produce statistically similar belief updating. Yet in the main field experiment, the aligned arm adopts policy at nearly twice the rate of the nonsalient arm (1.68 vs. 0.94 percentage points), although this difference is not statistically significant. The authors interpret this gap as suggestive evidence that ideological alignment affects policy implementation through channels beyond belief updating — such as career concerns, party cues, or the political economy of implementation — though they acknowledge the evidence is indirect and the treatment difference is not statistically distinguishable.

Q: What is the estimated economic cost of ideological misalignment?

A: The authors estimate a cost of 2,192 euros per municipality per year attributable to ideological misalignment between the informing institution and the receiving policymaker. This calculation uses the estimated impact of Wikipedia changes on touristic revenues from Hinnosaar et al. (2021) and reflects not the cost of not implementing the policy, but the marginal cost of using an ideologically opposite rather than aligned institution to disseminate the research evidence.

Q: How did outside researchers’ predictions compare to actual results?

A: Researchers surveyed on the Social Science Prediction Platform correctly anticipated the rank ordering of treatment effectiveness (aligned > nonsalient > opposite > control) but substantially overestimated adoption rates in every arm. They predicted relative increases of 144%, 103%, and 48% for aligned, nonsalient, and opposite conditions respectively, compared to actual relative increases of roughly 65%, 37%, and ~0%. Email opening rates were the most accurately predicted (49% predicted vs. 38% actual). The results highlight the difficulty of translating evidence into policy even for simple, low-cost interventions.

Q: What are the main threats to validity and how are they addressed?

A: Three main threats are considered. First, differential email opening rates across treatment arms: addressed by showing the informing institution was revealed only after email opening, and confirmed by finding no significant differences in opening rates across groups. Second, spillovers between municipalities: the endline survey shows only 5 of 236 control-group respondents reported receiving any information from external sources; spillover distance analyses in Table D.II find no significant effect on control municipalities’ adoption rates. Third, contamination bias in multi-arm RCTs with strata fixed effects: addressed by replicating main results using the Goldsmith-Pinkham et al. (2022) method, yielding nearly identical estimates.

Q: What heterogeneity is observed across left- and right-wing municipalities?

A: The positive effect of receiving information from an ideologically aligned institution appears larger for left-wing municipalities, with coefficients approximately three times larger than for right-wing municipalities, but this difference is not statistically significant at conventional confidence levels. The authors caution that the strength of ideological alignment may differ systematically between the partner think tanks on the left and right, making direct comparisons between left- and right-wing effects difficult to interpret cleanly.

Q: How does the paper relate to prior work on evidence-based policymaking?

A: The closest prior work is Hjort et al. (2021) and Mehmood et al. (2024), which examine the impact of scientific evidence access on actual policy adoption, and DellaVigna and Kim (2022), which identifies ideology as a factor in the diffusion of innovative policies across governments. The present paper’s main contribution is being the first to isolate the causal effect of ideological alignment on policy adoption using a large-scale field experiment with real, authoritative ideological institutions — rather than surveys or hypothetical scenarios — while using a non-ideological policy recommendation to avoid confounding messenger ideology with policy ideology.

Ideological alignment: In this paper’s usage, the congruence between the political ideology of the institution disseminating research evidence (think tank or newspaper) and the political ideology of the local government receiving that information. Alignment is operationalized by matching right-wing municipalities with right-leaning institutions (FAES, El Mundo) and left-wing municipalities with left-leaning institutions (Fundación Alternativas, Eldiario.es).

Evidence-based policy adoption: The actual implementation by local policymakers of a policy recommendation derived from published peer-reviewed research — measured here as whether a municipality’s Wikipedia page was edited in line with specific recommended guidelines during the study period, not merely expressed intention or stated support.

Knowledge brokers: Institutions, such as think tanks, that serve as intermediaries between academic researchers and policymakers, translating and disseminating research findings in accessible formats (policy briefs) to bridge the gap between evidence and policy.

Nonsalient ideology: A condition in which the informing institution carries no salient or recognizable partisan affiliation, operationalized here by a foreign research university professor (LSE) whose institutional identity does not carry a clear left-right signal in the Spanish political context.

Three-stage policy adoption framework: The authors’ conceptual structure positing that ideology can interfere at three sequential stages: (1) selective exposure — whether policymakers choose to access information once the messenger’s ideology is revealed; (2) belief updating — whether policymakers revise their assessment of a policy’s effectiveness upon receiving evidence; and (3) policy implementation — whether policymakers act on updated beliefs to adopt the policy.

Selective exposure: The tendency of individuals to avoid information from sources whose ideology conflicts with their own prior beliefs; in this paper, operationalized as differential click-through rates on links to policy briefs or news articles after the informing institution’s identity is revealed.

Motivated reasoning: A documented tendency, also observed in policymakers, to reject or discount evidence that contradicts ideologically held prior beliefs — the mechanism proposed to explain why opposite-ideology information fails to update beliefs as effectively as aligned-ideology information.

Inflation Expectations and the Slope of the Phillips Curve: Evidence from Firm Surveys

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

Do the inflation expectations of firms — rather than households or financial markets — shift the slope of the Phillips curve? Using a new panel of firm-level surveys matched to price-setting behavior, the authors find that firms with higher expected inflation adjust prices more aggressively in response to demand shocks, steepening the local Phillips curve slope. The effect is concentrated among firms that review prices frequently, suggesting a mechanism through the frequency of price adjustment rather than through the level of markups.

Summary of a forthcoming paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What is the main empirical finding on expectations and the Phillips curve slope?

Firms with higher measured inflation expectations exhibit a steeper relationship between demand conditions and price adjustment — the estimated Phillips curve slope is roughly 40% larger in the high-expectations tercile than in the low-expectations tercile, conditional on the authors’ controls and sample. The authors interpret this as evidence that expectations are not merely a level shift in inflation but alter the sensitivity of prices to real activity, consistent with forward-looking pricing theories.

Q2. What is the mechanism, and how do the authors identify it?

The authors argue that expectations work through the frequency of price review: firms expecting higher inflation are more likely to be in an active review window, and so respond more to a given demand shock within that window. Identification relies on cross-firm variation in survey-measured expectations within narrow industry-time cells, so that aggregate demand shocks are held approximately fixed. The authors acknowledge this strategy absorbs industry-specific inflation trends and may understate the full expectational effect.

Q3. What does this imply for monetary policy?

If the Phillips curve slope varies with expectations, then a credible disinflation — by lowering expected inflation — flattens the curve and makes the output cost of reducing inflation larger, not smaller. The authors present this as a potential mechanism behind the observed flattening of the curve in low-inflation regimes, though they stop short of a structural welfare calculation.

Key concepts

Phillips curve slope: The coefficient linking excess demand (or unemployment gap) to inflation in the short-run Phillips curve — steeper means a given demand shortfall has a larger disinflationary effect.
price review frequency: How often a firm actively reconsiders its prices; firms that review more often are more likely to adjust in response to new information within any given period.
firm-level survey expectations: Inflation expectations measured directly from firms (rather than households or markets), which may better capture the beliefs that drive actual price-setting decisions.

Intergenerational Impacts of Secondary Education: Experimental Evidence from Ghana

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

This paper provides experimental evidence on the intergenerational impacts of secondary education subsidies in a low-income context, leveraging a randomized controlled trial (RCT) conducted in rural Ghana with a 15-year longitudinal follow-up. The study exploits a 2008 scholarship lottery in which 682 students — drawn from 2,064 rural youth who had been admitted to public senior high school but had not enrolled due to financial constraints — were randomly selected to receive four-year secondary school scholarships covering full tuition and fees. Scholarship receipt increased senior high school completion by 27–28 percentage points for both men and women (from 39.8% to 67.2% for women; from 49.7% to 77.9% for men), and raised average years of education by 1.33 years.

The central research question is whether secondary education subsidies generate intergenerational benefits — specifically, whether children of scholarship recipients have better survival and cognitive development outcomes — and what mechanisms drive any such effects.

For female scholarship recipients, the scholarship significantly altered fertility timing and partnership. By 2013, female recipients were 6.9 percentage points less likely to have ever been pregnant (on a control-group base of 48.3%), with the decline driven almost entirely by a 7 percentage point (17%) reduction in unwanted pregnancies. Though total fertility eventually caught up by 2022, recipients were still less likely to be married or cohabiting as of 2019 and were significantly more likely to have a partner with tertiary education.

Children of female scholarship recipients experienced substantially lower mortality. Among control-group female respondents, 3.5% of children died before age one and 4.0% before age three. These rates fell to 1.7% (p=0.028) and 2.2% (p=0.065) respectively among children of female recipients — a roughly 45–51% reduction in under-one and under-three mortality.

Child cognitive development gains emerge only once children reach school age. Children of female recipients show no significant cognitive score differences at 18 months, 2.5 years, or 3.5 years, but score 0.238 standard deviations higher at age five (p=0.005) and 0.252 standard deviations higher at age seven (p=0.035). Effects span language, math and numeracy, spatial reasoning, and executive function, but not socio-cognitive development. These effect sizes fall between the 75th and 80th percentile of RCT-based educational intervention effect sizes in low- and middle-income countries.

The primary mechanism is not higher income or greater monetary investment in children. The study finds no significant treatment effect on household SES index (0.107 SDs, p=0.103), no impact on formal schooling inputs, and no difference in parental aspirations or knowledge of child stimulation’s importance. Instead, more-educated mothers seek more prenatal care, engage in more preventive health behaviors, and — critically — spend more time interacting with their children in stimulating ways. Day-long LENA (Language Environment Analysis) recordings at 18 months confirm 20% more adult-child conversational turns per minute (effect size 0.068, p=0.005) and 17% more child vocalizations per minute (effect size 0.32, p=0.014) for children of female recipients.

For male scholarship recipients, no analogous intergenerational benefits appear. Their partners are not more educated (in fact slightly less educated on tertiary rates), their children show no mortality improvement, and cognitive scores are if anything negative at age five (point estimate -0.22, p=0.069). The absence of effects is attributed to male scholarship recipients having caregivers — overwhelmingly mothers — with no more education than in the control group, and to children of male recipients being 8.7 percentage points less likely to live with their father.

A cost-benefit analysis finds internal rates of return (IRR) of 27%–76% for a female-only means-tested scholarship program and 20%–51% for a mixed-gender program. The cost per under-three death averted ($15,184 for female-only) places the scholarship program within the range of the 10th-percentile most cost-effective WHO-recommended child health interventions.

Scope conditions: the study estimates effects for students who qualified for senior high school but faced binding financial constraints in rural Ghana in 2008 — a population that is well-prepared academically but economically disadvantaged. Results may not generalize to students who would not have qualified for secondary school or to contexts where financial barriers are not binding.

Q: What was the experimental design and who was in the study sample? A: In 2008, 2,064 rural Ghanaian students who had been admitted to senior high school (SHS) but had not enrolled — typically due to inability to pay fees — were sampled. After a baseline survey, 682 were randomly selected (approximately one-third) by lottery to receive a four-year scholarship covering full tuition and fees for a day (non-boarding) student, stratified by district, school, gender, and exam-year cohort. The two-thirds comparison group received no scholarship. Students were on average 17 years old at baseline and just over 31 at the last follow-up in Spring 2023.

Q: How large was the scholarship’s effect on educational attainment? A: Scholarship receipt raised SHS completion from 39.8% to 67.2% among women (a 69% increase) and from 49.7% to 77.9% among men (a 57% increase). Overall, the scholarship led to an average of 1.33 more years of education. For women only, it also significantly raised tertiary education: by 2023, scholarship receipt increased tertiary completion by 10.8 percentage points for women, but had no significant tertiary effect for men.

Q: What were the effects on fertility and family formation for female scholarship recipients? A: By 2013, female recipients were 6.9 percentage points less likely to have ever been pregnant (base: 48.3% in control), driven almost entirely by a 7 percentage point (17%) reduction in unwanted pregnancies. By 2019, recipients were still 6 percentage points less likely to have started childbearing and had 0.152 fewer children on average (p=0.065). Total fertility eventually caught up by 2022. By 2016, female recipients were 12.1 percentage points (24% of control mean) less likely to have ever lived with a partner, and by 2019 were 6.2 percentage points less likely to be married or cohabiting. Conditional on having a partner, they were significantly more likely to have a partner who completed tertiary education (p=0.071).

Q: What were the effects on fertility and family formation for male scholarship recipients? A: Male recipients showed few changes in fertility or marriage behavior. They were 7.8 percentage points (30% of control mean) more likely to still be living with their parents as of 2019. Their partners were not more educated; in the cognitive games subsample, treatment actually reduced the share of partners with tertiary education by 3.6 percentage points from a control base of 4.3%.

Q: What were the child mortality results for children of female scholarship recipients? A: Among children of female control respondents, 3.5% died before age one and 4.0% before age three. These fell to 1.7% (p=0.028) and 2.2% (p=0.065), respectively, among children of female recipients — approximately a halving of under-one and under-three mortality. These point estimates are robust to varying the covariates (linear vs. fixed effects for birth year, dropping or adding controls). After multiple-hypothesis testing adjustment using the Romano-Wolf step-down procedure, the p-value for survived-to-one rises from 0.028 to 0.119.

Q: What were the child mortality results for children of male scholarship recipients? A: The estimated effects for children of male recipients were smaller and statistically insignificant: a 1.4 percentage point increase in survived-to-one (p=0.161) and 0.9 percentage points in survived-to-three (p=0.549). These estimates are not significantly different from those for female recipients. Results were sensitive to sample perturbations given the smaller sample: only 26 of 1,016 children of male respondents died before age one.

Q: What child cognitive development gains did children of female scholarship recipients show, and at what ages? A: No significant differences emerged at 18 months (-0.066 SDs, p=0.489), 2.5 years (-0.024 SDs, p=0.850), or 3.5 years (0.026 SDs, p=0.736). Significant gains appeared at age five (0.238 SDs, p=0.005) and age seven (0.252 SDs, p=0.035). Effects span language (0.15 SDs at five; 0.27 SDs at seven), math and numeracy (0.15 SDs; 0.26 SDs), spatial reasoning (0.20 SDs; 0.12 SDs), and executive function (0.25 SDs; 0.20 SDs), but not socio-cognitive development. These effect sizes fall between the 75th and 80th percentile of educational RCT effect sizes in low- and middle-income countries.

Q: What cognitive development effects did children of male scholarship recipients show? A: No significant positive effects emerged at any age. Point estimates were negative at all ages except 18 months, and marginally significantly negative at age five (-0.22 SDs, p=0.069). The difference in treatment effects between children of male and female recipients is statistically significant at age five (p=0.005).

Q: Why do cognitive gains appear only at age five and not earlier? A: The authors offer three interpretations: first, that the cognitive tests for younger children are noisier instruments (cross-sectional and longitudinal correlations within domains are much lower for 1.5-year tests than 5-year tests); second, that impacts on cognitive development may take time to materialize; third, that marginal survivors in the treatment group may start with a cognitive deficit (e.g., surviving a cerebral malaria episode), and maternal education effects require time to overcome this initial handicap. Gains concentrate on skills underlying literacy and numeracy, consistent with more educated mothers bridging home and school environments.

Q: What is the primary mechanism driving intergenerational effects? A: The primary mechanism is changes in parenting behaviors, not income. Female recipients do not invest more money in children (no significant difference in SES index or child investment index). Instead, they seek more prenatal care, engage in significantly more preventive health behaviors, and interact more with their children in cognitively stimulating ways. Day-long LENA recordings at 18 months show 20% more conversational turns per minute (effect size 0.068, p=0.005) and 17% more child vocalizations per minute (effect size 0.32, p=0.014). Caregiver reports confirm more playing, singing, and doing simple mathematics with children.

Q: Does the income effect of scholarship receipt explain the child outcomes? A: No. Duflo et al. (2024) find no significant earnings impacts until 2019 or later, meaning children tested at ages five and seven by 2023 largely grew up before their mothers’ earnings improved. The household SES index shows only a 0.107 SD gain (p=0.103), indistinguishable from the effect for children of male recipients. There is also no evidence of a quality-quantity trade-off: caregivers of scholarship recipients do not have fewer children to care for.

Q: Does the increase in maternal age at birth explain the child mortality reduction? A: It is not the primary driver. Maternal age at birth increases by only 0.349 years on average (p=0.142) for children of female recipients, and 0.64 years for first-born children (p=0.040). Point estimates on mortality for first-born children are somewhat smaller than for the full sample, suggesting maternal age is not the main channel. Moreover, maternal age at birth falls for children of male recipients yet their survival point estimates are positive, which further argues against maternal age as the primary mechanism.

Q: How does the education of the primary caregiver mediate the results? A: For 84% of children in the sample, the primary caregiver is the child’s mother. Children of female scholarship recipients have caregivers who are 25 percentage points more likely to have completed secondary school and 5 percentage points more likely to have completed tertiary education. Children of male scholarship recipients have caregivers with no more education than the control group, because the recipients’ partners — the typical caregivers — are not more educated. Treatment effects for female recipients are not altered when father’s education is added as a control, confirming maternal education as the main driver.

Q: What threat to validity arises from co-residence of the father? A: Children of male scholarship recipients are 8.7 percentage points less likely to live with their father (p=0.024), compared to no such effect for children of female recipients (92% of whom live with their scholarship-recipient mother). LENA recordings show negative treatment effects for children of male recipients — fewer adult words and conversational turns — consistent with father absence mechanically reducing auditory engagement and possibly leaving single mothers less time to verbally interact with each child.

Q: How are multiple-hypothesis testing concerns addressed? A: The pre-analysis plan pre-specified child survival and child cognitive development as primary outcomes. The authors apply the Romano-Wolf step-down procedure for multiple hypothesis testing adjustment. After adjustment, the p-value for survived-to-one for children of female recipients rises from 0.028 to 0.119; the cognitive development effects at age five and seven remain significant.

Q: How does the study address potential sample selection bias in the child outcomes sample? A: The authors use entropy balancing (Hainmueller, 2012) to reweight observations so that baseline (2008) characteristics are balanced between treatment and control within the subsample of recipients who had children. Results are qualitatively unchanged for both female and male recipients. The authors also note that children of female recipients are younger on average (4.71 months, p=0.067), which is why the study collects data at fixed age windows (14-22 months, 2.5 years, 3.5 years, 5 years, 7 years) rather than in a single cross-sectional wave.

Q: What is the cost-effectiveness and cost-benefit result for secondary school scholarships? A: Social costs are estimated at $585 per recipient for a mixed-gender program and $505 for a female-only program (combining school fees, materials, and foregone wages). The cost per under-three death averted is $23,582 for mixed-gender and $15,184 for female-only — placing the female-only program within the range of the 10th-percentile most cost-effective WHO-recommended child health interventions. The IRR is 27%–76% for a female-only means-tested scholarship program and 20%–51% for a mixed-gender program. These are likely conservative, as they exclude welfare gains from avoiding unwanted pregnancies, greater female agency, and recipient health benefits.

Q: What is the scope of the experiment and to what population do findings generalize? A: The study estimates ITT effects for students in rural Ghana who qualified for SHS on exam performance but faced binding financial constraints in 2008 — a population that is academically prepared but economically disadvantaged. Results do not directly apply to students who would not have qualified, to contexts without binding financial barriers, or to settings where secondary school quality or the marriage market differs substantially. The study also cannot yet observe complete fertility, since scholarship-lottery participants were only 31 years old on average at last follow-up.

LENA (Language Environment Analysis): A day-long recording device worn by a child that uses speech recognition software to generate count-based metrics — adult word count, adult-child conversational turns, and child vocalizations per minute — providing an objective measure of the child’s auditory environment and caregiver engagement quality without reliance on self-report.

IRT Score (Item Response Theory Score): A latent-trait measure of child cognitive ability estimated from a one-parameter logistic model applied to binary correct/incorrect responses across cognitive game questions, assigned a difficulty level to each question and a latent ability to each child, then standardized. Used as the primary cognitive development outcome across age windows.

Incarceration Effect: The hypothesis that education delays fertility mechanically only while students are in school (analogous to incarceration preventing activity), with no persistent effect once they exit. The authors rule this out by showing that the fertility gap between female treatment and control groups persists well after the majority of scholarship recipients have graduated.

Quality-Quantity Trade-off (Becker 1991): The economic framework predicting that more educated parents, facing higher opportunity costs of children and lower costs of investing in child quality, will have fewer but better-invested-in children. The authors find delayed and reduced fertility but do not find that recipients have fewer children to care for in the cognitive assessment sample, suggesting the child quality gains operate primarily through parenting practices rather than resource concentration.

Intent-to-Treat (ITT) Effect: The treatment effect estimated by comparing all lottery winners to all losers regardless of whether winners actually enrolled, which captures the effect of the scholarship offer (including compliance costs). The cost-benefit analysis uses ITT estimates, so the cost of subsidizing inframarginal students who would have attended anyway is incorporated.

Entropy Balancing: A reweighting procedure (Hainmueller, 2012) that assigns weights to observations in the control group so that the weighted distribution of baseline covariates matches that of the treatment group, used to assess whether imbalances in the subsample of participants who had children drive the results. The authors apply this as a robustness check for both mortality and cognitive development outcomes.

Unwanted Pregnancy: A pregnancy reported by the respondent as unplanned at the time of conception, which the authors use to distinguish fertility reduction from a change in desired fertility versus a reduction in unintended out-of-wedlock pregnancies. The scholarship’s early fertility impact is almost entirely a reduction in unwanted pregnancies (7 percentage point decline, 17% reduction).

International Trade Responses to Labor Market Regulations

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

Overview

Research Question. This paper asks whether differences in labor market regulations — specifically payroll taxes and minimum wages — shape countries’ comparative advantage in the cross-border provision of labor-intensive services. The question has broad policy relevance: if lower labor standards confer a systematic trade advantage, countries may face pressure to race to the bottom in labor protections, and political support for economic integration may erode.

Setting and Identification. The paper exploits the EU “posting policy,” a large trade program established in 1959 that allows firms in one EU member state to temporarily send their employees to perform service contracts in another member state. In 2017, posting accounted for roughly one-third of all within-EU trade in services (approximately 2% of EU GDP), involving about 2 million workers (in full-time equivalents) in 2019. The setting is analytically attractive because competing foreign and domestic firms serve the same customers at the same physical location using shared capital, holding most determinants of comparative advantage constant while labor market regulations vary by the firm’s country of origin.

Under posting rules, payroll taxes are generally origin-based (exporting firms pay their home country’s tax rate) but become destination-based when contracts exceed a regulatory duration threshold (12 months pre-2010, 24 months from 2010–2020, 18 months from 2020 onward). Minimum wages are destination-based: foreign firms must match the importing country’s statutory minimum wage floor when it exceeds the workers’ home-country wage level. This generates the paper’s key identifying variation — payroll taxes and minimum wages vary across countries, over time, and within countries across sectors.

Data. The author uses administrative A1 social security forms filed for every EU posting contract from 2007–2018, collected from 25 EU member states, supplemented by micro-level national posting registries in Belgium (LIMOSA), France (SIPSI), and Luxembourg (matched employer-employee data). Labor cost data (wages, payroll tax rates, minimum wages) come from Eurostat and the OECD Taxing Wages Dataset.

Methodology. The paper proceeds in three steps. First, it documents steady-state cross-sectional correlations between bilateral posting flows and labor cost differentials. Second, it estimates difference-in-differences (DiD) elasticities from four quasi-natural experiments. Third, it estimates a theory-consistent gravity model using all sources of variation across 25 EU countries from 2009–2018.

Main Findings.

Steady-state correlation: A strong negative relationship exists between bilateral posting flows and labor cost differentials, with a cross-sectional elasticity of approximately –0.58 (SE 0.08). In sharp contrast, the relationship between bilateral goods trade and labor cost differentials is weak and if anything marginally positive (point estimate +0.13), confirming that labor cost differences are a distinctive driver of trade specifically in labor-intensive services rather than goods.
Belgian tax shift (2016–2018): When Belgium cut employers’ social security contributions from 33% to 25%, imports of posting services into Belgium slowed relative to France (a neighboring control country on parallel pre-reform trends). The reduced-form elasticity of posting imports with respect to the payroll tax rate is 1.45 (SE 0.3).
Luxembourg EU regulation reform (2010): A new EU regulation required temporary employment agencies in border regions to pay destination-based payroll taxes, raising statutory rates faced by Luxembourgish exporters from 15% to 44%. Posting exports from Luxembourg’s temporary employment sector fell by 40% relative to the pre-reform level and relative to the domestic (control) sector, while the sheltered road transportation sector showed no response. The reduced-form elasticity with respect to the statutory payroll tax rate is –1.55 (SE 0.24), and the triple-difference estimate is –1.37 (SE 0.08).
Bunching at duration thresholds: The distribution of posting contract lengths in France (which has the EU’s highest payroll taxes) shows a sharp spike just below the 24-month payroll tax threshold. When the threshold was moved to 18 months in 2020, excess mass migrated to the new threshold, confirming that bunching reflects behavioral responses to the tax notch rather than reference-point effects. This documents that payroll tax differentials shape not only the quantity (extensive margin) but also the length (intensive margin) of posting contracts.
German minimum wage reform (2015): Germany’s introduction of a national minimum wage of €8.50 per hour — which was already binding on construction workers through a sectoral minimum, but not on foreign firms providing non-construction services — caused postings to Germany in manufacturing to fall by approximately 60% relative to the construction (control) sector. The reduced-form elasticity is –1.34 (SE 0.43). Heterogeneity analysis shows that export declines were monotonically larger for low-wage origin countries where the new minimum wage was binding, and placebo estimates using Germany’s high-wage neighboring countries (where minimum wage requirements did not change) are statistically indistinguishable from zero.
Gravity estimates: The preferred specification (PPML with origin-year, destination-year, and pair fixed effects, exploiting bilateral variation in minimum wage bindingness across origin countries) yields a model-implied trade elasticity θ of –1.2 (SE 0.2). The range across specifications is –1.2 to –2.4. These estimates are smaller than the goods trade elasticity (typically estimated around 5) and below the medium-run reduced-form elasticities from the DiD case studies, consistent with short-run gravity estimates capturing only partial adjustment while DiD designs measure longer-run equilibrium responses.

Policy Counterfactual. The paper’s estimates imply that the Bolkestein Directive — which proposed exempting foreign firms from all destination-country labor regulations — would have doubled exports of physical services from Eastern European countries (upper bound), as their cost advantage would have been dramatically amplified by removal of minimum wage requirements. Counterpart to this export boom, average posted workers’ wages would have fallen by approximately 16%, since workers would lose their entitlement to destination-country minimum wages. The paper documents that the Bolkestein controversy — sparked by the “Polish plumber” debate in early 2005 — coincided with a sharp and persistent drop in French voter support for the EU constitutional treaty, which was subsequently rejected.

Scope Conditions. Results apply specifically to trade in physical (labor-intensive) services traded via temporary worker posting within the EU, where productivity differences across countries for these tasks are plausibly small (Balassa-Samuelson), making institutional factors a primary driver of wage differences. The paper estimates intent-to-treat effects, assuming perfect compliance by exporting firms. The paper does not perform a comprehensive welfare analysis covering consumer price effects or general equilibrium wage and trade-balance responses.

In depth

Q1. What is the EU posting policy and why does it provide an unusually clean setting for identifying the causal effect of labor regulations on trade?

The EU posting policy, established in 1959, allows firms in one EU member state to temporarily send employees to perform service contracts in another member state. The policy keeps most determinants of comparative advantage constant — competing foreign and domestic firms serve the same customers at the same physical location using shared capital — while labor market regulations vary by the firm’s country of origin. Productivity differences for physical services across countries are also plausibly limited (Balassa-Samuelson), making institutional wage differences the primary cost driver. Enforcement is facilitated by the on-site nature of the service, and administrative A1 forms create a direct measure of the number of workers involved in cross-border transactions without a minimum reporting threshold.

Q2. What are the three sources of labor cost differences the paper identifies and quantifies?

Foreign firms competing for posting contracts face different costs through three channels: (i) equilibrium gross wages differ across origin countries, reflecting both productivity differences and institutional/information frictions that allow wage discrimination between posted and domestic workers; (ii) payroll tax rates are origin-based and differ substantially across countries (for example, France’s employer payroll tax is approximately 40% versus approximately 15% for Luxembourg before the 2010 reform); and (iii) destination-specific minimum wages impose a “posting allowance” on firms from countries with lower wages, equal to the shortfall between the firm’s home-country wage and the importing country’s minimum wage floor. Micro-level wage data from France confirm that most posted workers from low-wage countries are paid exactly at the French minimum wage, demonstrating the bindingness of the third channel, while French workers performing the same tasks receive wages near the French average (approximately €21.1 per hour versus a minimum wage of approximately €10 per hour in 2018).

Q3. What does the cross-sectional evidence show about the relationship between labor cost differentials and posting flows, and how does this compare to goods trade?

Bilateral posting flows and bilateral labor cost differentials have a tight negative cross-sectional relationship with an estimated elasticity of –0.58 (SE 0.08), indicating that countries export more posting services when their labor costs are substantially below those of the destination country. The same exercise applied to bilateral goods trade yields a coefficient of +0.13 (SE 0.07) — weak and marginally positive — consistent with goods trade being driven by capital, technology, and scale rather than labor cost differentials. The gap confirms that labor cost differences are a distinctive comparative advantage mechanism for labor-intensive services but not for less labor-intensive goods.

Q4. What does the Belgian tax shift reform demonstrate, and how is identification established?

Belgium cut employer social security contributions from 33% to 25% between 2016 and 2018 in a revenue-neutral reform (financed by VAT, excise duties, and dividend taxes). The DiD compares posting imports into Belgium with those into France (a neighboring, similarly sized importer on parallel pre-reform trends). Belgium and France imported posting services at similar rates before 2015; Belgian imports slowed immediately after the reform while French imports continued growing. The reduced-form elasticity of posting flows with respect to the destination payroll tax rate is 1.45 (SE 0.3). The elasticity with respect to total labor cost is 3.7 (SE 0.7). No discernible response is detected for trade in manufacturing goods, providing a within-reform placebo. A synthetic control using all available importing countries yields a smaller elasticity of 0.6 (SE 0.22).

Q5. How does the Luxembourg EU regulation reform (2010) improve on the Belgian case for identification?

The 2010 EU regulation required temporary employment agencies in border regions to pay destination-based (rather than origin-based) payroll taxes, raising statutory rates for Luxembourgish exporters from 15% to 44%. Unlike the Belgian reform, this created within-country variation: the same Luxembourgish firms were exposed in the temporary employment sector but not in road transportation (which received a 10-year exemption). This within-exporter, cross-sector design controls for all Luxembourg-wide demand or supply shocks. Posting exports by the temporary employment sector fell 40% relative to pre-reform levels and relative to the domestic (control) sector, while road transportation posting showed zero response. The monthly data confirm the drop occurred in the exact month following the regulation with no anticipation. The triple-difference elasticity (with respect to the payroll tax rate) is –1.37 (SE 0.08).

Q6. What does the bunching evidence at payroll tax duration thresholds add to the DiD findings?

When posting contracts exceed a regulatory duration threshold (24 months during 2010–2020, then 18 months from July 2020), payroll taxes become destination-based. Because France has the highest payroll tax in the EU, all exporting firms face strong incentives to avoid crossing the threshold. The distribution of posting contract lengths in France shows sharp excess mass just below 24 months in 2017. When the threshold moved to 18 months in 2020, the excess mass migrated to the new threshold while diminishing at the old one, confirming that bunching is tax-motivated rather than driven by a reference-point at 24 months. This establishes that labor tax differentials shape not only the quantity of posting contracts (extensive margin) but also their length (intensive margin).

Q7. What are the main findings from the German minimum wage reform, and how do the heterogeneity tests strengthen identification?

Germany’s January 2015 introduction of a national minimum wage of €8.50 per hour (preceded by a sectoral minimum in meat processing in August 2014) raised wage costs for foreign firms providing non-construction services, but not for construction firms already covered by a higher sectoral minimum. Postings to Germany in manufacturing fell by approximately 60% relative to the construction (control) sector, implying a reduced-form elasticity of –1.34 (SE 0.43). Two heterogeneity tests reinforce identification: (i) within the treated German sector, posting declines are monotonically increasing in the degree to which the new minimum wage is binding in the origin country, with Luxembourg (where the minimum is non-binding) showing no statistically significant effect; (ii) the same industry-by-country comparison in Germany’s high-wage neighboring countries (which did not change minimum wage rules) yields placebo estimates statistically indistinguishable from zero. The reform raised wages for German workers by an average of 6% (and up to 10% for most affected workers) but automatically raised wages for posted workers by an average of 40%, doubling them for workers from the poorest sending countries.

Q8. How do the gravity model estimates compare to the reduced-form DiD estimates, and what explains the difference?

Across gravity specifications, model-implied elasticities range from –0.75 to –2.4. The preferred specification — PPML with pair fixed effects, destination-year fixed effects, and origin-year fixed effects — yields θ = –1.2 (SE 0.2). These estimates are systematically below the medium-run reduced-form DiD estimates because: (a) the gravity model uses nationwide average tax and minimum wage measures that introduce measurement error relative to the sector-specific reforms in the case studies; and (b) the gravity model captures year-to-year (short-run) adjustments, while the DiD designs compare outcomes several years before and after the reform, picking up longer-run equilibrium reallocation. The finding that responses grow over time mirrors evidence on dynamic adjustment in goods trade (Boehm, Levchenko and Pandalai-Nayar, 2023), and contradicts the conventional belief that fiscal devaluations boost exports only in the short run.

Q9. What does the gravity model reveal about trade in goods as a function of posting-specific wage costs?

When the same gravity specification is applied to bilateral goods trade rather than posting flows, posting-specific wage costs have a positive — not negative — coefficient on goods trade. This is inconsistent with a model where unobserved shocks affect all exports symmetrically, and instead suggests a small substitution effect: as the cost to import labor services rises (due to tighter posting regulations), countries substitute toward importing goods. For some activities (such as meat processing), importing finished goods is a partial substitute for importing labor services to produce on-site.

Q10. What are the Bolkestein Directive counterfactual implications, and how do they connect to the political economy evidence?

The Bolkestein Directive (proposed 2005) would have enforced a “country of origin principle,” exempting foreign posting firms from destination-country minimum wages. Using the preferred lower-bound elasticity from the gravity model (column 5, θ = –1.2) and an upper bound averaging gravity and DiD estimates, the paper predicts this would have at least doubled exports of labor services from Eastern European countries. Tax revenues collected on posted workers in origin countries would also double. However, average posted workers’ wages would fall by approximately 16%, as workers would lose their entitlement to destination-country minimum wages. The paper documents that the Bolkestein controversy — introduced to the EU Parliament in March 2005 and popularized via the “Polish plumber” trope — coincided with a sharp and permanent drop in French voter support for the EU constitutional treaty, which was subsequently rejected in referendum. This is consistent with Rodrik’s (1998) hypothesis that voters withdraw support for economic integration when comparative advantage appears to be based on institutional choices that conflict with importing countries’ social norms.

Q11. How does the paper handle the incidence of payroll taxes — does the canonical result that payroll taxes are fully passed through to workers hold in this context?

The canonical competitive labor market model predicts full pass-through of payroll taxes to workers’ net wages, leaving firms’ labor costs unchanged. The paper finds substantial trade responses to payroll tax reforms, inconsistent with full pass-through. Nominal rigidities — including binding minimum wages that constrain downward wage adjustment — help rationalize incomplete pass-through in the EU context. The paper estimates elasticities both with respect to statutory tax rates (the reduced-form, making no incidence assumption) and with respect to total wage costs (instrumented with the reform, allowing for gross wage responses). Wage data from Belgium show no distinguishable wage response to the Belgian tax cut, suggesting the incidence fell largely on firms’ costs rather than workers’ wages in that episode.

Q12. What do the destination-based taxation counterfactual (tax cooperation proposal) calculations show?

A proposal to shift all posting payroll taxation to destination-based rates would decrease posting exports from Eastern European countries by between 10% and 25%. Despite the volume reduction, total taxes collected on posted workers would still increase under this reform even when the upper-bound elasticity (approximately –3.7 with respect to total wage cost) is used, because a 1% increase in the payroll tax rate translates to a much smaller proportional increase in total wage cost.

Key Concepts

Posted workers / posting policy: Employees temporarily sent by their employer (the “exporting firm”) to perform a service contract in another EU member state. Posted workers maintain their employment contract with the firm in the origin country but physically work in the destination country. This creates a setting where competing domestic and foreign firms serve the same customers at the same location under different labor regulations.

Posting allowance: The additional wage component that exporting firms must pay to posted workers to satisfy the destination country’s minimum legal wage when that minimum exceeds the firm’s home-country wage level. The posting allowance is zero when the exporting country’s average wage already exceeds the destination minimum wage; it can be large for low-wage origin countries. The allowance enters directly into firms’ labor costs and is the minimum-wage channel of the paper’s labor cost formula.

Origin-based vs. destination-based payroll taxation: Under posting, payroll taxes are normally assessed in the country where the exporting firm is registered (origin-based), creating tax rate differentials between competing firms in the same job site. EU regulations convert payroll taxes to destination-based when posting contracts exceed a duration threshold, eliminating the tax advantage of lower-tax origin countries for those contracts. The 2010 EU regulation additionally imposed destination-based taxation on border-region temporary employment agencies.

Trade elasticity for physical services (θ): The structural parameter from the Eaton-Kortum (2002) gravity model that governs the elasticity of bilateral posting flows with respect to changes in firms’ total wage costs when exporting services from country i to country j. The paper’s preferred estimate is –1.2 (from gravity estimation) to approximately –1.3 to –1.5 (from reduced-form DiD designs), substantially smaller in absolute value than the goods trade elasticity (typically estimated around 5).

Social standards as comparative advantage: The paper uses “standards” to refer to countries’ domestic policy choices about payroll taxes (which finance social insurance programs) and minimum wages (which set worker protection floors). The paper demonstrates that these regulatory choices — distinct from productivity differences, factor abundance, or technology — create measurable cost advantages that shape specialization in labor-intensive service sectors. This is in contrast to “benign” sources of comparative advantage.

Bolkestein Directive / country of origin principle: A 2005 EU legislative proposal that would have required posting firms to operate under the laws of their home country when supplying services in other EU member states, eliminating the hard core of destination-country regulations (including minimum wages) that the 1996 Posted Workers Directive had imposed on foreign firms. The proposal was withdrawn after a wave of protests and its association with a sharp fall in French support for the EU constitutional treaty.

Bunching / notch at duration threshold: A behavioral response in which exporting firms strategically keep posting contract lengths below the duration threshold that triggers destination-based payroll taxation, generating an excess mass in the distribution of contract lengths just below the threshold. The paper uses this bunching, together with the movement of the threshold from 24 to 18 months in 2020, as additional evidence that payroll tax differentials affect the intensive margin of posting.

Labor Market Competition and the Assimilation of Immigrants

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

Labor Market Competition and the Assimilation of Immigrants

Research Question

Why have immigrant-native wage gaps widened substantially across arrival cohorts in the United States since the 1960s, and why has the speed of wage convergence slowed? The paper argues that the existing literature, which attributes these trends entirely to declining immigrant cohort quality, omits a critical general-equilibrium channel: labor market competition arising from imperfect substitutability between immigrants and natives. The paper quantifies how much of the observed deterioration in wage assimilation profiles can be attributed to (i) increasing immigrant cohort sizes raising labor market competition, (ii) secular shifts in relative skill demand, and (iii) genuine changes in immigrant cohort quality.

Data and Methodology

The analysis uses U.S. Census microdata for 1970, 1980, 1990, and 2000, combined with American Community Survey (ACS) data pooled for 2009–2011 (labeled 2010) and 2018–2019 (labeled 2020), all drawn from IPUMS-USA. The sample covers individuals aged 25–64 who are employed in the civilian sector, not self-employed, not in group quarters, and report positive earnings. Immigrant cohort sizes grew from approximately 800,000 individuals in the 1960s cohort to 2.3 million in the 1980s cohort and 4.6 million in the 2000s cohort.

The theoretical framework is a constant elasticity of substitution (CES) production function in which workers supply two types of skills: “general” skills portable across countries and “specific” skills particular to the host country (including language proficiency and knowledge of cultural and institutional environment). Immigrants arrive with the same general skills as observationally equivalent natives but only a fraction of their specific skills; they accumulate specific skills over time. Because immigrants disproportionately supply general skills upon arrival, increasing immigrant inflows raise the relative supply of general skills, depress the relative price of general skills, and thereby widen the immigrant-native wage gap. This mechanism operates only when immigrants and natives are imperfect substitutes (elasticity of substitution σ < ∞).

The model is estimated in two steps using nonlinear least squares (NLS). First, productivity factor parameters are estimated from native wages year by year, with state dummies identifying state-level skill prices. Second, specific skill accumulation parameters and the elasticity of substitution σ are jointly identified from immigrant wage differences across labor markets (defined as U.S. states) and over time. The demand shift parameter δ_t, which captures changes in the relative demand for specific skills (e.g., technology that favors communication over manual tasks), enters as a linear time trend in the baseline specification.

Main Findings with Quantitative Magnitudes

Competition effect: Immigration-induced increases in labor market competition explain 14.2, 43.9, and 40.8 percent of the increase in the initial wage gap of the 1970s, 1980s, and 1990s cohorts relative to the 1960s cohort, respectively. Averaged across all years spent in the United States, the competition effect alone accounts for 14.1, 22.4, and 20.4 percent — approximately one fifth overall.

Competition plus demand effect: Adding secular shifts in relative skill demand raises these figures to 24.8, 68.3, and 109.5 percent at arrival and 21.2, 33.6, and 36.4 percent averaged across years — approximately one third overall.

Elasticity of substitution: The baseline estimate of σ (elasticity of substitution between general and specific skills) is 0.020 (s.e. 0.002), implying an inverse elasticity of approximately 50.5. The relative supply of general skills increased by 1.67 log points between 1970 and 2020, producing a predicted increase in the relative price of specific skills of approximately 59.6 log points. The demand shift trend is estimated at 1.3 log points per year.

Cohort quality: Once competition and demand effects are netted out, the remaining deterioration in assimilation profiles is entirely attributable to observable changes in immigrants’ educational attainment and country-of-origin composition. Conditional on these two observable characteristics, unobservable skill quality improved across cohorts (consistent with English language proficiency trends), reversing the conventional narrative of declining cohort quality.

Specific skills gap at arrival: The 1960s cohort faced a specific skills gap of approximately 52.4 percent relative to native equivalents; this narrowed to 41.8 percent for the 1970s cohort, 35.6 percent for the 1980s cohort, and 17.6 percent for the 1990s cohort, conditional on origin and education. After 20–30 years, all cohorts reach 83.7–92.0 percent of their native counterparts’ specific skill levels.

Scope Conditions

The analysis focuses on employed men in the main text (women are analyzed in an Online Appendix, showing qualitatively similar but quantitatively smaller patterns).
Labor markets are defined at the U.S. state level in the baseline; robustness checks use state-education and state-gender cells.
The decomposition covers the period from the 1960s to the 1990s arrival cohorts.
Results are robust to corrections for selective outmigration, undercounting of undocumented immigrants, immigrant network effects, alternative demand shift specifications, alternative labor market definitions, and endogenous immigrant location choice (using shift-share instruments in the spirit of Card, 2001).

In depth

Q1. What is the core theoretical mechanism by which increasing immigrant inflows widen the immigrant-native wage gap?

A: Because immigrants disproportionately supply general (country-portable) skills upon arrival, while natives disproportionately supply specific (host-country) skills, an increase in immigrant inflows raises the ratio of general to specific skills in the economy. Under imperfect substitutability (σ < ∞), this lowers the relative price of general skills and raises the relative price of specific skills, thereby widening the wage gap between immigrants (who earn predominantly from general skills) and natives (who earn more from specific skills). The effect is larger in the early years after arrival when immigrants’ specific skill endowment s is small, and diminishes as immigrants accumulate specific skills over time.

Q2. How does the paper model immigrants’ skill accumulation, and how do accumulation profiles differ across groups?

A: Immigrants’ specific skill endowment s(·) upon arrival and over time is modeled as a flexible polynomial in years since migration, interacted with dummies for region of origin, education, cohort of entry, and potential experience abroad. Mexican high school dropouts (the reference group) are estimated to arrive with approximately 80 percent of the specific skills of equivalent natives. Immigrants from Latin America, Asia, and other regions arrive with lower specific skills than Western immigrants, who arrive near native parity. Higher-educated immigrants arrive relatively less similar to equivalently educated natives than low-educated immigrants, reflecting the greater importance of language-intensive skills in high-skill occupations. Conditional on origin and education, more recent cohorts arrive with narrower specific skill deficits: the 1990s cohort faces a gap of 17.6 percent at arrival compared to 52.4 percent for the 1960s cohort.

Q3. What are the estimated technology parameters, and how are they interpreted?

A: The elasticity of substitution between general and specific skills is estimated at σ = 0.020 (s.e. 0.002), with a confidence interval of [0.017, 0.024]. This implies an inverse elasticity of approximately 50.5, meaning a one percent increase in the relative supply of general skills raises the relative price of specific skills by about 50.5 percent. The implied elasticity of substitution between natives and immigrants (evaluated at market-level averages) is approximately 0.013 in 1990, 0.020 in 2000, and 0.025 in 2010 — in the same range as the Ottaviano and Peri (2012) benchmark of 0.034 (s.e. 0.008). The demand shift trend is estimated at δ̃ = 0.013 (s.e. 0.001) log points per year, reflecting secular increases in the relative demand for specific (host-country) skills.

Q4. How does the paper identify the elasticity of substitution σ and the skill accumulation parameters separately?

A: The estimation proceeds in two steps. First, productivity factor parameters (returns to education and experience) are estimated from native wage regressions, with state-year dummies absorbing state-specific skill prices. Second, skill accumulation parameters θ are identified from wage differences between immigrants with different characteristics working in the same labor market, while σ and the demand shift δ̃ are identified from variation in immigrant wage gaps across states (which have different immigrant population shares) and over time. Specifically, states with higher immigrant shares display lower relative prices of general skills, providing the identifying variation for σ.

Q5. What are the quantitative magnitudes of the competition effect for specific cohorts at different time horizons?

A: At the time of arrival, the competition effect explains 14.2 percent (1970s cohort), 43.9 percent (1980s cohort), and 40.8 percent (1990s cohort) of the increase in initial wage gaps relative to the 1960s cohort. After 10 years, these figures are 17.1, 22.7, and 22.2 percent respectively. After 20 years, they are 12.2, 16.9, and 16.2 percent. After 30 years, 10.9, 15.3, and 13.7 percent. The declining share across years reflects the fact that as immigrants accumulate specific skills, their wages become less sensitive to equilibrium skill prices. Averaged across all years since migration, the competition effect accounts for 14.1, 22.4, and 20.4 percent for the three cohorts.

Q6. How does labor market competition affect the speed of wage assimilation, and does it prevent full convergence?

A: The effect on assimilation speed is theoretically ambiguous and depends on whether future cohorts are larger or smaller than the reference cohort, and whether immigrants fully converge to native skill levels. In the stylized examples, a one-time permanent increase in competition raises both the initial wage gap and the speed of subsequent convergence (since the gap between immigrant and native skill levels is larger and therefore more responsive to changes in skill prices). However, continuous inflows of increasingly large cohorts counteract this speedup by continuously shifting the wage profile downward — the “dynamic competition effect.” For immigrants who fully converge (s → 1), competition delays but does not prevent convergence; for those who only partially converge (s → < 1), competition permanently widens the long-run wage gap. Quantitatively, the paper finds the effect on assimilation speed to be small in the full-sample decomposition.

Q7. What do the illustrative examples for specific immigrant groups reveal about heterogeneous competition effects?

A: For a Mexican male high school dropout (1960s cohort skills), facing the same competition level as the 1990s cohort would widen the initial wage gap by 10.2 log points; facing 2010 competition levels would widen it by 21.1 log points. However, because this group fully converges (s → 1), the effect dissipates entirely after approximately 25 years, and long-run wage assimilation is not prevented. For a Latin American male high school graduate who only partially converges (s → < 1), facing 1990s competition would widen the initial gap by 17.4 log points and leave a 3.8 log-point larger long-run wage gap. For a Western college graduate who arrives near native skill parity, competition effects are negligible throughout.

Q8. What are the changes in absolute wage gaps documented in the baseline data?

A: The 1960s cohort arrived with an initial wage gap of approximately 17.2 log points relative to natives. The 1970s cohort arrived with a gap of 30.1 log points, the 1980s cohort 29.2 log points, and the 1990s cohort 20.8 log points. Under the no-competition counterfactual, these initial gaps narrow to 13.6, 24.7, 20.3, and 15.7 log points respectively. Removing both competition and demand effects further narrows them to 13.7, 23.4, 17.5, and 13.3 log points.

Q9. What does the paper find about the role of observable versus unobservable immigrant quality?

A: Once competition and demand effects are accounted for, all remaining cohort differences in assimilation profiles are attributable to observable changes in immigrants’ educational attainment and country-of-origin composition. Conditional on these two observable characteristics, immigrants in more recent cohorts display higher levels of unobservable skills (smaller specific skill deficits conditional on origin and education), consistent with rising English language proficiency across cohorts. This reverses the standard interpretation that unobservable immigrant quality has declined.

Q10. How do aggregate skill supplies and relative skill prices evolve over the sample period?

A: Between 1970 and 2020, the total supply of general skills from immigrants grew by a factor of 16.3, while the supply of specific skills grew by a factor of 15.0. The resulting increase in the relative supply of general skills caused the relative price of general skills to fall from 0.89 to 0.38. Accounting for growing relative demand for specific skills (the δ_t trend), the ratio of relative skill prices fell further to 0.20 by 2020. At the state level, relative prices of general skills are well below 0.3 in high-immigration states like California, Florida, and New York, and approach 1.0 in states with low immigrant shares.

Q11. Are the results robust to selective outmigration, undocumented immigrants, and alternative specifications?

A: Yes. Across twelve robustness checks covering selective outmigration corrections (using Borjas and Bratsberg 1996 or Rho and Sanders 2021 outmigration rates, and synthetic cohort reweighting), undocumented immigrant undercounting corrections, immigrant network controls (share and stock of compatriots in the same state), alternative demand shift specifications (quadratic and time dummies), alternative labor market definitions (state-education and state-gender cells), and endogenous immigrant location choice (GMM with shift-share instruments), the estimated elasticity of substitution σ ranges from 0.017 to 0.033 and the average competition effects remain stable. Averaged across all robustness checks, competition effects are 1.3 log points (1960s cohort), 3.0 log points (1970s), 5.2 log points (1980s), and 4.3 log points (1990s), compared to baseline values of 1.4, 3.1, 5.5, and 4.6 log points.

Q12. What are the policy implications highlighted by the authors?

A: First, since assimilation and competition effects are intertwined, the wage impact of immigration on natives is intrinsically dynamic: newly arrived immigrants initially compete relatively little with natives but increasingly substitute for them as their specific skills grow. Second, labor market competition may reduce immigrants’ incentives to invest in host-country-specific skills, a channel not modeled in most existing structural models. Third, dispersal policies (such as those used during refugee crises) that reallocate immigrants across regions will affect local skill price ratios and therefore alter wage assimilation trajectories — a potentially unintended consequence of geographic allocation policies.

Key Concepts

General skills: Skills that are portable across countries and can be used productively in any labor market. In the paper’s framework, general skills are those required for tasks (such as manual or physical labor) that are similar across national contexts. Upon arrival, immigrants are assumed to supply the same amount of general skills as observationally equivalent natives, making immigrants’ relative supply of general skills high at arrival.

Specific skills (host-country-specific skills): Skills particular to the host country, including language proficiency (English in the U.S. context) as well as familiarity with the institutional and cultural environment. Immigrants arrive with only a fraction s of the specific skills of comparable natives; this fraction evolves over time as immigrants spend time in the host country. The level of specific skills governs how substitutable a given immigrant worker is with native workers.

Labor market competition effect: The mechanism by which increasing immigrant inflows affect relative wages through equilibrium changes in skill prices rather than through individual skill accumulation. When immigrants and natives are imperfect substitutes, rising immigrant inflows raise the relative supply of general skills, depress the relative price of general skills, and widen the immigrant-native wage gap. This effect is larger for recently arrived immigrants (small s) and diminishes as immigrants assimilate.

Dynamic competition effect: The combined effect on a given cohort’s observed assimilation profile of continuous, growing immigrant inflows over its time in the country. Unlike a one-time permanent increase in competition (which would raise both the initial gap and assimilation speed), continuously growing inflows both widen the initial gap and exert a continuous downward shift on the cohort’s wage profile, with an ambiguous net effect on the speed of convergence.

Demand shift (δ_t): A time-varying parameter in the CES production function capturing secular changes in the relative demand for specific versus general skills beyond what is explained by standard skill-biased technological change. A positive trend in δ_t (estimated at 1.3 log points per year in the baseline) reflects technological change that favors communication-intensive (specific-skill-intensive) tasks over manual (general-skill-intensive) tasks, and amplifies the competition effect.

Elasticity of substitution between general and specific skills (σ): The key technology parameter governing the degree of imperfect substitutability between natives and immigrants in equilibrium. Estimated at σ = 0.020 in the baseline. When σ = ∞, immigrants and natives are perfect substitutes and labor market competition has no effect on relative wages. As σ decreases, the competition effect on relative wages becomes stronger for a given change in relative skill supplies.

Specific skill accumulation function s(·): A flexible parametric function of years since migration, interacted with region of origin, education level, cohort of entry, and potential experience at arrival, that governs the rate at which immigrants acquire host-country-specific skills over time. The intercept of s(·) at arrival (relative to a native s = 1) measures the initial specific skill deficit; the polynomial in years since migration captures how quickly this deficit closes.

Wage assimilation profile: The trajectory of the immigrant-native log wage gap as a function of years spent in the host country, conditional on a cohort of arrival. The paper distinguishes between changes in the level of the profile (the initial wage gap) and changes in its slope (the speed of convergence), and decomposes both dimensions into competition effects, demand effects, and cohort quality effects.

Manipulation-Robust Prediction

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

This paper addresses the problem of algorithmic manipulation: when consequential decisions are encoded in machine learning algorithms, individuals strategically alter their behavior to achieve desired outcomes, undermining the predictive validity of the algorithm. The authors develop a “strategy-robust” approach to training decision rules that explicitly models the incentives and costs of manipulation, producing rules that remain stable even when fully transparent. They then deploy and evaluate this approach in a large field experiment in Kenya — the first real-world implementation and evaluation of such a strategy-robust empirical decision rule.

The theoretical framework considers a policymaker who observes training data with features x_i and optimal decisions y_i, and wishes to estimate a decision rule to apply to new instances where behavior may be manipulated. While the standard approach (OLS or LASSO) selects a rule optimal for the training distribution, the strategy-robust approach models how individuals will adjust behavior in response to the incentive structure implied by any given rule. Under linear decision rules and quadratic manipulation costs, each individual shifts behavior by C_i^{-1} * beta away from their “bliss level,” where C_i captures individual- and behavior-specific manipulation costs. The strategy-robust estimator finds the rule that minimizes prediction error in the counterfactual world where people manipulate — a “Stackelberg” solution that commits the policymaker to a rule while anticipating equilibrium behavioral responses. Unlike LASSO, which penalizes all features equally without regard to their manipulability, the strategy-robust approach attenuates the weight on features that are both easily manipulated and subject to manipulation noise.

The empirical setting is a smartphone app (“Smart Sensing”) deployed to 1,557 participants in Nairobi, Kenya, in collaboration with the Busara Center. The app passively collected over 1,000 behavioral indicators (calls, texts, app usage, mobility, etc.) and delivered weekly financial “challenges” that rewarded participants based on decision rules randomly assigned to them. Average weekly payouts were calibrated to approximate typical digital credit loan amounts in Kenya at the time (approximately $4.80). The experiment has two phases: a training phase using control (beta = 0) and simple single-behavior incentive rules to estimate manipulation cost parameters via GMM, and an implementation phase using complex multi-feature decision rules to compare strategy-robust versus LASSO classifiers.

The main findings are as follows. First, participants demonstrably manipulate behavior: a joint F-test that incentive diagonals all equal zero is rejected with p < 0.001. The number of texts sent was 49 times more responsive to incentives than the number of people called during the workday. Outgoing communications are cheaper to manipulate than incoming, and simple behaviors (e.g., average talk time) more manipulable than complex ones (e.g., standard deviation of talk time). Individuals who self-report higher tech skills find manipulation 9% easier on average, and the 90th percentile of gaming ability finds manipulation twice as easy as the 10th percentile.

Second, in the implementation phase, strategy-robust decision rules outperform LASSO when the decision rule is made transparent to participants. Across all pooled outcomes, strategy-robust rules reduce RMSE by 11% (p = 0.024) relative to LASSO under transparency. For the single income-prediction outcome alone, the improvement is 5% ($0.19 RMSE reduction) but not statistically significant (p = 0.507).

Third, the framework enables estimation of the “cost of transparency.” Making naive LASSO rules transparent lowers performance by 23%. Switching to strategy-robust rules under full transparency reduces that performance decline to 9.2% — a 60% reduction in the cost of transparency. The model predicts this cost to be 9.8%, close to the implemented value of 11.3%.

The scope of the findings is bounded by the linear model with quadratic manipulation costs, a particular population of Kenyan smartphone users, and financial incentive magnitudes comparable to small digital credit loans. The mechanism relies on experimentally estimating manipulation cost parameters, though the authors also show that expert elicitation provides a correlated but noisier substitute (correlation 0.30 with experimental estimates).

Q: What is the core market failure the paper addresses, and why do standard fixes fail?

A: Standard machine learning training assumes the relationship between observed features and outcomes is stable, but implementing a consequential decision rule creates incentives for individuals to manipulate the features on which the rule is based (Goodhart’s Law; Lucas critique). The two common industry responses — restricting to “stable” predictors and keeping rules secret — are inadequate: restricting predictors amounts to a dogmatic prior that manipulation costs are either infinite or zero, while secrecy is increasingly at odds with demands for algorithmic transparency and fails anyway when sophisticated actors reverse-engineer the rule. Periodic retraining treats manipulation as generic covariate shift, can produce non-converging oscillations, and requires observing mistakes before learning from them.

Q: How does the strategy-robust estimator differ from OLS and LASSO?

A: OLS maximizes fit within the unincentivized training sample but ignores that implementing beta will shift behavior; LASSO adds a regularization penalty but still assumes behavior remains fixed at bliss levels and so penalizes all features equally regardless of manipulability. The strategy-robust estimator replaces each individual’s observed behavior x_i with their anticipated counterfactual behavior x_tilde_i(beta) = x_i + C_i^{-1} * beta, and finds the beta that minimizes prediction error in this manipulated distribution — a Stackelberg equilibrium. It attenuates features that are easily manipulated or subject to high manipulation noise, shifting weight toward harder-to-manipulate features even when the latter are less predictive in the training data.

Q: What are the three ways the strategy-robust estimator differs from standard estimators?

A: First, it anticipates level shifts in behavior: behaviors respond to beta, so observed training behaviors are replaced by counterfactual manipulated behaviors. Second, it accounts for signaling and noise: when manipulation ability correlates with the outcome of interest, manipulation can be informative about type (as in Spence 1973), but unobserved heterogeneity in gaming ability that is unrelated to outcomes introduces noise that attenuates coefficients on manipulable behaviors. Third, it achieves subgame perfection by anticipating how behaviors would respond to off-path deviations in beta, rather than assuming behaviors are fixed when beta deviates — yielding a Stackelberg rather than a one-step best-response solution.

Q: How were manipulation cost parameters estimated in the Kenya experiment?

A: In the training phase, each participant was randomly assigned to simple single-behavior incentive rules (e.g., “earn 12 Ksh. per incoming call this week, up to 250 Ksh.”) or control rules (beta = 0). This random variation in per-behavior incentives identifies how sensitive each behavior vector is to incentives, enabling GMM estimation of individual and behavior-specific cost parameters C and the heterogeneity scaling parameter omega. Off-diagonal elements of C were regularized to zero due to noisy estimation; diagonal elements used LASSO penalization with lambda = 1.0 set by cross-validation. Observable heterogeneity was allowed to vary with self-reported tech skills, which explained the most variation in preliminary analysis.

Q: What patterns were found in manipulation costs across behaviors?

A: Outgoing communications are cheaper to manipulate than incoming communications. Text messages, being relatively cheap to send, are more manipulable than calls. Simple behaviors such as average call duration are more manipulable than complex behaviors such as the standard deviation of talk time. Cross-behavior elasticities exist but are mostly noisy: 94.5% of off-diagonal incentive effects are not statistically significant (p < 0.05), 3.6% are significantly positive, and 1.8% are significantly negative.

Q: How large is heterogeneity in gaming ability, and what predicts it?

A: Individuals who self-report advanced or higher tech skills find it on average 9% easier to manipulate behaviors. Including unobserved heterogeneity, the 90th percentile of gaming ability finds manipulation twice as easy as the 10th percentile. Much of the heterogeneity arises from unobservables not captured by observables in the model.

Q: What happened when the naive LASSO rule was made transparent versus when the strategy-robust rule was made transparent?

A: Under the transparent treatment, participants received the full coefficients of the decision rule plus access to an interactive earnings calculator. Making naive LASSO rules transparent lowered performance by 23% relative to the opaque naive rule (RMSE $3.780 versus $4.641 in pooled outcomes). Switching to strategy-robust rules under full transparency reduced the performance decline to 9.2% — corresponding to a 60% reduction in the cost of transparency. The model predicted this cost to be 9.8%, which is close to the implemented value of 11.3%.

Q: What does the reduced-form evidence on behavior change under complex decision rules show?

A: Under the opaque treatment, participant behavior responses to complex decision rules were largely statistically insignificant and often in the wrong direction — 38.5% of estimated behavioral effects are in the same direction as the incentivized behavior. Under the transparent treatment, 75.4% of point-estimated effects are in the same direction as the incentive, confirming that transparency is a prerequisite for meaningful manipulation in this setting.

Q: How does the paper compare strategy-robust estimation to iterative retraining?

A: Simulation results show that iterative retraining of a naive LASSO model approaches the performance of the strategy-robust method after approximately 4 iterations. However, simulated performance of iterative retraining then begins to deteriorate; for the intelligence outcome, performance eventually falls below baseline performance before any retraining began. This illustrates that myopic best responses can produce non-convergent or suboptimal dynamics, while the strategy-robust approach finds the equilibrium rule directly.

Q: How does the paper compare strategy-robust estimation to the “intuitive” approach of simply excluding highly manipulable features?

A: The intuitive approach of excluding features above a manipulability threshold reduces predicted manipulability but also discards useful predictors. In some cases, the exclusions leave LASSO with no behaviors predictive enough to include, reducing performance. The strategy-robust approach can extract signal even from manipulable behaviors by adjusting their weights to account for manipulation noise, and outperforms the intuitive exclusion approach in the simulations reported in the Supplemental Appendix.

Q: Can manipulation costs be estimated without an experiment?

A: The authors briefly explore expert elicitation as a nonexperimental alternative: 171 individuals were surveyed to predict how Kenyans would manipulate phone behaviors when incentivized. Experts generally predicted lower costs (more manipulability) than observed experimentally, but the correlation between expert predictions and experimental estimates is 0.30. Using expert-elicited costs to train the strategy-robust model improved simulated performance substantially for one focal outcome and had an inconsequential negative effect for the other. Costs can also potentially be estimated from market prices and first principles when a structural model of underlying manipulations is available.

Q: What is the paper’s interpretation of its results through the lens of the Lucas critique?

A: The paper frames its contribution as a machine learning interpretation of Lucas (1976): just as implementing an economic policy changes the behavioral relationships on which the policy was calibrated, implementing a predictive decision rule beta changes the distribution of the very features the rule is based on. The key insight is that this counterfactual world has predictable structure — including a feature in the model tends to induce manipulation in that feature of a magnitude directly related to beta — so counterfactual fit can be estimated and rules can be optimized to perform well in the equilibrium they induce.

Q: What are the policy implications for algorithmic transparency?

A: The framework allows a policymaker to quantify and reduce the performance cost of transparency. The estimated equilibrium cost of transparency is roughly 10% when using strategy-robust rules, substantially less than the approximately 23% cost of making naive rules transparent. This means that strategy-robust rules can be disclosed — satisfying demands for a “right to explanation” under regulations such as GDPR — while losing far less performance than opaque naive rules would lose if disclosed.

Strategy-robust decision rule: A decision rule trained to anticipate that individuals will manipulate the features on which it is based, by replacing observed training behaviors with anticipated counterfactual manipulated behaviors in the loss function. It yields a Stackelberg equilibrium in which the policymaker commits to a rule while correctly forecasting the equilibrium behavioral response.

Manipulation costs (C_i): Individual- and behavior-specific quadratic costs that determine how far an individual shifts behavior from their bliss level in response to the incentive implied by a decision rule’s coefficient vector beta. Higher costs imply less behavioral response; costs are parameterized to allow separable heterogeneity by person and by behavior.

Bliss level (x_i): An individual’s unincentivized behavior — the behavior they would exhibit absent any decision rule (i.e., when beta = 0). Estimated from control periods in the experiment.

Gaming ability (gamma_i): Individual-level scaling factor for manipulation costs; a higher value means lower costs and easier manipulation. Modeled as a function of observable characteristics (e.g., self-reported tech skills) and unobservable heterogeneity.

Counterfactual fit: Predictive fit evaluated in the counterfactual state of the world where the decision rule is implemented and agents manipulate their features in response. The strategy-robust approach maximizes counterfactual fit, sacrificing within-sample fit (as measured on unmanipulated training data) to improve performance in deployment.

Cost of transparency: The reduction in predictive performance of a decision rule when its coefficients are disclosed to the individuals being evaluated. In the experiment, disclosure reduces performance of naive LASSO rules by 23% and strategy-robust rules by 9.2%, implying strategy-robust rules reduce the cost of transparency by 60%.

Stackelberg equilibrium: The solution concept in which the policymaker (leader) commits to a decision rule, correctly anticipating the best-response behavior of individuals (followers), rather than taking behavior as fixed or updating myopically. The strategy-robust estimator implements this equilibrium concept.

Performative prediction: The broader phenomenon, drawing on Perdomo et al. (2020), whereby a decision rule changes the distribution of the data it is applied to. The paper’s strategy-robust approach is an empirically estimable solution within this framework.

Marriage, Fertility, and Cultural Integration in Italy

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

Bisin and Tura study the cultural integration of immigrants in Italy by estimating a structural model of marital matching embedded with intra-household decisions — fertility, socialization of children, and divorce — along cultural-ethnic lines. The central research question is how to decompose the demand for integration (from immigrants) and the supply of cultural acceptance (from natives) in explaining the pace and heterogeneity of cultural convergence.

The empirical analysis exploits administrative individual-level data from ISTAT’s ADELE Laboratory covering the universe of marriages formed in Italy from 1995 to 2012 and the universe of births and separations over the same period. After matching marriage, birth, and separation records, the final sample comprises more than 4 million marriages, representing 92.6% of all marriages celebrated in Italy over the period. Seven cultural-ethnic groups are studied: Italian (majority), Europe-EU15, Other Europe, North Africa–Middle East, Sub-Saharan Africa, East Asia, and Latin America. The model is a transferable-utility (TU) frictionless marriage market in which the joint marital surplus depends on a systematic component — itself the outcome of a collective household decision problem — and an idiosyncratic component capturing unobserved individual heterogeneity (following Choo and Siow, 2006). Parameters are estimated via method of moments, with identification drawing on cross-sectional variation across ethnic-group pairings and across Italy’s 20 administrative regions. Cultural socialization is proxied by language transmission (whether Italian is spoken at home with children).

The data confirm strong positive assortative mating along cultural-ethnic lines, with particularly high homogamy rates for Sub-Saharan African and East Asian minorities. Homogamous minority households show notably lower rates of Italian-language use at home — for East Asian parents, 20% in a homogamous marriage versus 92% in a heterogamous marriage. Heterogamous marriages have higher separation rates (7.5% for mixed families with at least one Italian spouse versus 6.4% for homogamous Italian couples) and lower fertility.

The estimated cultural intolerance parameters — measuring the psychological value a parent places on socializing a child to his/her own ethnic identity relative to a child acquiring a different identity — are strictly positive, asymmetric across directions, and highly heterogeneous across groups. North Africa–Middle East immigrants exhibit the highest minority intolerance (estimated at 97.85), more than six times that of Europe-EU15 immigrants (6.69). Latin America (93.13), Sub-Saharan Africa (87.08), and East Asia (81.22) also show high intolerance. On the native side, Italian intolerance is highest toward Sub-Saharan African immigrants (78.23) and lowest toward Europe-EU15 immigrants.

Long-run simulations over successive generations show that all minorities eventually converge to the Italian majority along the language dimension, but at heterogeneous rates. Seventy-five percent of second-generation immigrants speak Italian at home with their children (one-generation integration rate). Europe-EU15 and Other Europe minorities converge almost completely within a single generation. Latin America shows the slowest path, with only 70% integration after four generations. East Asia and Sub-Saharan Africa also integrate more slowly, driven respectively by high fertility rates and strong selection into homogamous marriages.

A counterintuitive counterfactual result is central to the paper: if Italian cultural intolerance were reduced to zero (full acceptance), cultural integration of minorities would slow by 15 percentage points over a generation (from 93% to 78% by the third generation). The mechanism is that greater native acceptance enables immigrants to sustain their own language even within heterogamous (mixed) marriages, increasing demand for such marriages and raising minority fertility, thereby preserving cultural distinctiveness.

Finally, doubling immigration inflows while holding population shares constant reduces third-generation integration from 93% to 86% (a 7-percentage-point reduction). Effects are concentrated among Sub-Saharan African (20-percentage-point reduction) and East Asian (6-percentage-point reduction) minorities, with little impact on European and North African minorities. When inflows are reweighted toward Sub-Saharan African and East Asian groups, integration losses for those minorities range from 20 to 60 percentage points by the third generation.

Q: What is the paper’s core methodological contribution? A: The paper embeds a collective household decision problem — covering fertility, socialization, and divorce — within a transferable-utility frictionless marriage matching framework. This allows marital utility to emerge endogenously from intra-household decisions rather than being specified exogenously. The key innovation is that socialization incentives and technologies differ systematically between homogamous and heterogamous marriages, and these differences feed back into marital matching and long-run cultural dynamics.

Q: What does “cultural intolerance” mean in this model, and how is it identified? A: Cultural intolerance is the psychological value a parent obtains from socializing a child to his/her own ethnic identity, relative to having a child adopt a different cultural-ethnic identity. It is the main parameter driving socialization effort and resistance to cultural integration. Identification relies on two sources of cross-sectional variation: differences in matching patterns, fertility, separation, and socialization rates across cultural-ethnic group pairings, and exogenous variation in the ethnic composition of the regional population across Italy’s 20 administrative regions.

Q: How heterogeneous are the estimated cultural intolerance parameters across minority groups? A: The parameters are highly heterogeneous. North Africa–Middle East immigrants have the highest estimated minority intolerance (97.85), more than six times the EU15 estimate (6.69). Latin America (93.13), Sub-Saharan Africa (87.08), and East Asia (81.22) are also substantially higher than EU15. The matrix is asymmetric: Italian intolerance toward Sub-Saharan Africans (78.23) is higher than toward North Africans (67.88), even though those two groups show comparable minority intolerance levels.

Q: What are the three mechanisms beyond intolerance parameters that explain heterogeneous integration dynamics? A: First, selection into homogamous marriages: Sub-Saharan Africa’s particularly strong selection into homogamy gives those households access to superior coordinated socialization technology, sustaining cultural heterogeneity despite similar intolerance levels to other groups. Second, fertility rates: East Asian minorities have particularly high estimated fertility, which amplifies the transmission of their cultural identity across generations. Third, socialization effectiveness in heterogamous marriages: Latin American immigrants are uniquely able to socialize children to their own language even when married to native Italians, making their integration the slowest despite being in many mixed marriages.

Q: What is the counterintuitive result about Italian cultural intolerance and integration speed? A: Lowering Italian cultural intolerance to zero would reduce minority integration by 15 percentage points over one generation, with third-generation integration falling from 93% to 78%. The intuition is that higher native acceptance enables immigrants to maintain their own language more effectively within heterogamous marriages, which in turn increases immigrant demand for intermarriage with natives and raises minority fertility — both of which slow cultural convergence rather than accelerating it.

Q: How do divorce dynamics differ between homogamous and heterogamous households? A: Heterogamous households exhibit higher separation rates than culturally homogeneous unions: 7.5% for mixed families with at least one Italian spouse versus 6.4% for homogamous Italian couples. In the model, divorce by heterogamous households can be a strategic choice by mothers with high cultural intolerance, since custody grants single mothers greater unilateral control over socialization. Divorce probabilities are decreasing in the number of children for both family types. Interestingly, heterogamous households invest more in socialization when divorced than when married, because the high-intolerance parent can act without spousal opposition.

Q: How well does the model fit the data? A: The raw correlation between predicted and observed gains to marriage is 0.84. The correlation between predicted and observed foreign-language socialization rates is 0.83, for both homogamous and heterogamous families. The dataset covers 92.5% of all marriages in Italy from 1995 to 2012, representing over 4 million marriages matched with birth and separation records at a 98.5% one-to-one match rate.

Q: What happens to cultural integration when immigration inflows are doubled with an overweighting of North Africa–Middle East, Sub-Saharan Africa, and East Asian immigrants? A: North Africa–Middle East immigrants reduce third-generation convergence by only 4 percentage points. By contrast, East Asian and Sub-Saharan African minorities produce integration losses ranging from 20 to 60 percentage points by the third generation. This wide range reflects how the interaction between high fertility, strong homogamy selection, and effective socialization in heterogamous marriages amplifies cultural persistence when these groups constitute a larger share of inflows.

Q: What is the one-generation cultural integration rate, and which groups diverge most from it? A: Seventy-five percent of second-generation immigrants speak Italian at home with their children, constituting the one-generation baseline integration rate. Europe-EU15 and Other Europe minorities converge almost completely within one generation, as does North Africa–Middle East. Latin America diverges most sharply downward, with only 70% integration even after four generations, and shows a partial retreat from integration in the first generation. Sub-Saharan Africa and East Asia also fall below the 75% one-generation benchmark.

Q: How does the paper relate to the debate on native labor market effects of immigration? A: The paper notes that sizeable negative labor market effects of immigration on natives are far from well-documented in the empirical literature, with results ranging from negative wage effects (Borjas) to positive or heterogeneous effects (Card, Ottaviano-Peri, Dustmann et al.). The authors therefore focus on the cultural externalities channel, which they argue better explains voter opposition to immigration, and study cultural integration structurally rather than examining wage outcomes.

Cultural intolerance: The psychological value a parent obtains from socializing a child to his/her own ethnic identity, relative to having a child adopt a different cultural-ethnic identity. It is specific to the household type (homogamous vs. heterogamous) and is the primary parameter measuring the strength of a group’s resistance to cultural integration.

Cultural socialization / language transmission: The costly investments parents make to transmit their own cultural-ethnic traits to children. In the empirical model, socialization is proxied by whether a parent speaks his/her own non-Italian language at home with children. Socialization technologies are more efficient in homogamous (same-ethnicity) marriages than heterogamous ones.

Homogamous vs. heterogamous marriage: A homogamous marriage is one in which both spouses share the same cultural-ethnic identity; a heterogamous marriage is one in which spouses differ. The distinction is load-bearing throughout the model: homogamous households have coordinated socialization incentives and superior technology, higher fertility, and lower separation rates.

Transferable utility (TU) matching: A marriage market framework in which utility is transferable between spouses, so that the equilibrium allocation maximizes aggregate marital surplus and equilibrium transfers are determined by outside options. The model is frictionless, meaning matching is driven purely by preferences over the characteristics of potential spouses.

Cultural integration (language dimension): In the paper’s long-run simulations, cultural integration is defined as the share of second- (or later-) generation immigrants who speak Italian at home with their own children. It is the empirical outcome used to track convergence to the majoritarian culture across generations.

Assortative mating along cultural-ethnic lines: The tendency for individuals to match with spouses of the same cultural-ethnic group. The paper finds positive assortative mating for all groups, with particularly strong homogamy for Sub-Saharan African and East Asian minorities, and explains it as the equilibrium outcome of the TU matching model given cultural intolerance preferences.

Socialization technology asymmetry: The model’s assumption that homogamous married parents hold a more efficient socialization technology than heterogamous parents, but that divorced heterogamous households invest more in socialization than married heterogamous ones, because the high-intolerance parent can act unilaterally without spousal opposition.

Merger Effects and Antitrust Enforcement: Evidence from US Consumer Packaged Goods

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

This paper by Bhattacharya, Illanes, and Stillerman makes two contributions to the debate over US antitrust enforcement stringency. First, it documents the price, quantity, and assortment effects of a comprehensive set of consummated mergers in US consumer packaged goods (CPG). Second, it develops and estimates a model of agency enforcement decisions to quantify antitrust stringency and simulate counterfactual outcomes under stricter regimes.

Data and scope. The analysis covers 129 product markets across 47 transactions in US CPG from 2006 to 2017, using the NielsenIQ Retail Scanner Dataset (covering 35,000–50,000 stores and 2.6–4.5 million UPCs). The sample is restricted to all deals valued at $280 million or more where both the acquirer and target sold products in at least one overlapping product market-DMA. Geographic markets are NielsenIQ designated market areas (DMAs). The sample is defined to avoid selection bias from studying only mergers that attracted press attention or were litigation targets.

Identification strategy. The empirical approach is a before-after event study within geography and product. For each merger, a brand-specific linear time trend is estimated from the 36 months prior to the merger announcement, controlling for UPC-DMA fixed effects, month-of-year fixed effects, input cost indices, and log median household income. Post-merger outcomes (24 months after completion) are measured as deviations from the extrapolated pre-merger trend. The identifying assumption is that secular demand and cost trends are gradual and well-captured by a linear trend. Pre-trend placebo tests show no significant departures from trend in the pre-period, and randomized-date placebos confirm that the linear trend is a better predictor of post-period outcomes under random merger dates than under actual merger dates, supporting the interpretation that observed post-period departures reflect merger effects.

Price effects. The average price effect of consummated CPG mergers is small: across specifications, estimates range from -0.6% to 1.0%, with a baseline mean of 0.3%. However, heterogeneity is substantial. The standard deviation of merger-level price effects is 4.0–7.5 percentage points. In the baseline specification, the first quartile of price effects is -2.1% and the third quartile is 3.7%. Merging and non-merging party price changes are positively correlated (correlation = 0.49), consistent with strategic complementarity. Thirty-six percent of mergers lead both groups to lower prices; 36% lead both groups to raise prices.

Quantity and assortment effects. Total quantities fall on average by 0.4–1.0% across specifications, with 60% of mergers producing quantity reductions. Merging parties exhibit a larger average quantity decline of 6.4%. Mergers also lead to a 2.7% average reduction in the number of stores served by merging parties, a 2.2% reduction in the number of brands sold in a DMA by merging parties, and a 3.2% reduction for non-merging parties. Brands with less than 5% of the merged entity’s sales are 6 percentage points more likely to be dropped post-merger.

Enforcement model. To interpret these outcomes relative to enforcement, the authors develop a model in which the agency receives a noisy signal of a merger’s price effect and challenges the merger if the posterior mean exceeds a threshold that is decreasing in deal size. They estimate the model by maximum likelihood using data on enforcement actions (6 mergers receiving remedies, 4 withdrawn under antitrust pressure) and realized price changes. The estimated sales-weighted average threshold is 4.8–6.3%: agencies act as if they challenge CPG mergers only when they expect a price increase exceeding this level. The posterior standard deviation of the agency’s assessment is 2.5–3.2 pp (aggregate prices) to 4.1–4.8 pp (merging-party prices).

Counterfactual stringency. Tightening the threshold from approximately 6.1% to 2.5% would roughly quadruple the challenge probability (from 0.075 to 0.30), reduce aggregate price changes of consummated mergers by approximately 1.4 pp, and lower the share of allowed anti-competitive mergers from roughly 50% to 35%. Critically, type I errors (blocking pro-competitive mergers) remain negligible at thresholds down to approximately 3%; at 0% threshold only 10% of blocked mergers would be type I errors. The primary cost of tighter enforcement is a significantly larger agency workload, not an increase in blocked pro-competitive mergers.

Scope conditions. Results pertain specifically to large CPG mergers (deal size ≥ $280 million) sold through US retail outlets, 2006–2017. Findings on structural presumptions show DHHI and merging share have predictive value for price changes, but structural metrics alone explain less than 10% of the variance in price effects (adjusted R-squared never exceeds 10% even with third-order interactions).

Q: What is the average price effect of consummated CPG mergers and how should it be interpreted? A: Across specifications, the average price effect is between -0.6% and 1.0%, with a baseline mean of 0.3%. This small average does not imply that enforcement is strict: Carlton (2009) shows that with perfect foresight, the largest observed price change — not the average — would indicate stringency. Because agencies face uncertainty, the distribution of realized price changes reflects both inframarginal approved mergers and the noise in agency forecasts.

Q: How large is the heterogeneity in merger price effects? A: The standard deviation of merger-level price effects is 4.0–7.5 percentage points across specifications. In the baseline, the first quartile of price effects is -2.1% and the third quartile is 3.7% for all parties combined. Merging parties specifically show a first quartile of -3.2% and third quartile of 3.7%, meaning a full quarter of mergers raise merging-party prices by more than 3.7%.

Q: How do merging and non-merging party prices co-move? A: Price changes for merging and non-merging parties are positively correlated (correlation = 0.49, s.e. = 0.08), consistent with strategic complementarity in pricing. Thirty-six percent of mergers lead both groups to lower prices, 36% lead both to raise prices, 13% cause merging parties to lower while non-merging parties raise, and 15% cause the reverse. The timing evidence shows merging-party prices begin changing upon merger completion, with rivals following suit.

Q: What happens to quantities following mergers? A: Total quantities fall on average between 0.4% and 1.0% across specifications, with 60% of mergers producing quantity reductions. Merging parties bear the bulk of quantity adjustment, with an average quantity decline of 6.4% and a standard deviation and interquartile range both around 30 pp. Non-merging party quantity changes are much less variable. The correlation between merging and non-merging party quantity changes is 0.36 (s.e. 0.08), which is positive — at odds with theoretical predictions from demand systems with the “type aggregation property” (Nocke and Schutz, 2018, 2024), where mergers should produce negatively correlated quantity changes.

Q: What non-price competitive responses do mergers trigger? A: Merging parties reduce the number of stores they serve by 2.7% on average, though in 38% of mergers store networks expand. Both merging and non-merging parties reduce product portfolios: merging parties drop the number of brands in a DMA by 2.2% on average and non-merging parties by 3.2%. Brands most likely to be dropped are those with less than 5% of the merged entity’s sales (6 pp more likely to be dropped), brands in small DMAs, and brands with small DMA shares.

Q: Do the Merger Guidelines’ structural presumptions (HHI, DHHI, merging share) predict price effects? A: DHHI and merging share have statistically significant but quantitatively modest predictive power. A 100-point increase in average DHHI is associated with a 0.2 pp increase in merging-party price changes and 0.3 pp for non-merging parties. Price effects are significantly larger when merging share exceeds 30%. However, structural metrics alone explain very little variance: adjusted R-squared never exceeds 10% even with third-order interactions of HHI, DHHI, merging share, private label share, and market size. Within-merger, DHHI is positively correlated with local price changes, and markets with DHHI above 200 exhibit significantly higher price effects than those below.

Q: How do the authors model antitrust enforcement and identify its stringency? A: The agency observes a noisy signal of a merger’s price effect, forms a posterior distribution combining a normally distributed prior (mean X’beta, standard deviation sigma_p*) with a normally distributed signal error (standard deviation sigma_epsilon), and challenges the merger if the posterior mean exceeds a threshold that is decreasing in deal size. The model is estimated by maximum likelihood: for approved mergers, the realized price change is observed; for withdrawn/remedied mergers, the posterior mean must have exceeded the threshold. Six mergers (from four deals) received remedies for horizontal market power concerns and four mergers (from two deals) were withdrawn under antitrust pressure, forming the challenged set.

Q: What is the estimated enforcement threshold and how does it vary across mergers? A: The sales-weighted average threshold is 4.8–6.3% using aggregate price changes and 6.6–7.8% using merging-party price changes. The threshold is lower for larger mergers: a 10% increase in merging-party sales is associated with an approximately 0.06 pp decrease in the threshold. The first quartile of thresholds across mergers is 4.5–5.6% and the third quartile is 5.6–6.9%, reflecting that the agencies apply stricter standards to larger deals.

Q: How accurate are the agencies’ forecasts of merger price effects? A: Using only the prior (structural characteristics), the agency’s accuracy in classifying mergers as anti-competitive versus pro-competitive is 56% (s.e. 3 pp). Adding the signal increases accuracy to 83% (s.e. 9 pp). The correlation between the prior mean and the true price change is 0.29 (s.e. 0.08); the correlation between the posterior mean and the true price change is 0.85 (s.e. 0.15). The posterior standard deviation is 2.5–3.2 pp for aggregate price changes and 4.1–4.8 pp for merging-party price changes.

Q: What would happen under stricter antitrust enforcement? A: Tightening the average threshold from 6.1% to 2.5% would raise the challenge probability from approximately 0.075 to 0.30 — roughly quadrupling it — and would reduce aggregate price changes of consummated mergers by approximately 1.4 pp (from roughly 0.2% to -1.2%). Moving to a 0% threshold would result in challenges to 57% of mergers, with 60–70% of consummated mergers then causing price decreases.

Q: How large are type I and type II errors at the current and counterfactual thresholds? A: At the current threshold (~6.1%), approximately 50% of allowed mergers are type II errors (anti-competitive mergers that should have been challenged). Type I errors (pro-competitive mergers wrongly blocked) are negligible at the current threshold and only become non-trivial starting around a 3% threshold. At a 2.5% threshold, the type II error share falls to 35%; at a 0% threshold, to 16%, while type I errors reach 10% of blocked mergers. The primary trade-off of stricter enforcement is therefore a larger agency workload, not an increase in blocking pro-competitive mergers.

Q: What identification strategy is used and how is it validated? A: The strategy is a within-product, within-geography before-after comparison using a brand-specific linear pre-merger trend as the counterfactual. Validation proceeds through three checks: (1) coefficient plots from an extended event study show no significant pre-trends after controlling for the linear trend; (2) a plot of brand trends against estimated price effects shows little explanatory power (statistically significant negative correlation but small magnitude, not consistent with results being driven by trend extrapolation); (3) placebo tests randomizing merger dates within the same markets yield a distribution centered at zero, narrower than the true distribution, and a significantly higher mean squared prediction error in the post-period, confirming that the linear trend is a better predictor under randomly assigned merger dates than under true dates.

Q: Why do the authors not use alternative control group approaches? A: Non-merging firms in the same market are rejected as controls because they may strategically respond to the merger. Synthetic controls using similar-industry untreated markets are rejected because deals often treat multiple similar markets (ruling out natural donors) and estimates prove sensitive to individual donors. Geographic controls (markets where merging parties have small shares) are rejected because they omit all 39 national mergers, untreated markets are not randomly selected, and regional pricing by non-merging parties could propagate effects into untreated regions, biasing estimates toward zero.

Merger retrospective. In this paper’s usage, an ex-post empirical study of the price, quantity, and assortment effects of a consummated merger, using pre-merger trends as the counterfactual, as opposed to forward-looking merger simulation.

Enforcement stringency. The marginal price increase at which the antitrust agency would expect to challenge a merger. Measured here as the sales-weighted average posterior-mean threshold: the value above which the agency acts as if it would propose a remedy, estimated at 4.8–6.3% for US CPG mergers.

Type I error (antitrust). The mistake of challenging (blocking) a merger that would have reduced prices (a pro-competitive merger). In the model, this occurs when an adverse signal causes the agency to block a merger whose true price effect is below the threshold.

Type II error (antitrust). The mistake of allowing a merger that increases prices (an anti-competitive merger). In the model, this occurs when a favorable signal causes the agency to approve a merger whose true price effect is above the threshold. Estimated at approximately 50% of allowed mergers at the current enforcement threshold.

Structural presumptions. The HHI-based rules in the 2010 and 2023 Merger Guidelines that create a presumption of competitive harm when DHHI exceeds specified thresholds (e.g., DHHI > 200 and post-merger HHI > 2,500 for the “red zone”). The paper finds DHHI and merging share have statistically significant but low explanatory power (adjusted R-squared below 10%) for actual price changes.

Prior and signal (in the enforcement model). The agency’s prior is a normal distribution over the merger’s true price effect, parameterized by structural characteristics (HHI, DHHI). The signal is a noisy draw centered on the true price effect, capturing information gathered through due diligence (e.g., evidence of efficiencies). The posterior mean — combining prior and signal — determines whether the agency challenges the merger.

Product market-deal pair (merger). The unit of observation in the empirical analysis: a specific NielsenIQ product module (e.g., soluble coffee) within a specific acquisition transaction (e.g., a food conglomerate merger). The sample contains 129 such pairs across 47 deals.

Monetary Cooperation during Global Inflation Surges

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

In a multicountry model with nominal wage rigidities, two sectors (tradable with convex supply, nontradable with flat supply), and free capital mobility, the paper studies optimal monetary policy during a global demand reallocation shock — a shift in preferences toward tradables (ω₀ > ω). Under cooperation (Proposition 1), the optimal response allows inflation to rise: higher tradable goods prices reduce real wages (restoring labor demand), generate expenditure switching back toward nontradables, and boost nontradable employment through an income effect. Cooperation achieves full employment as long as the inflation cost is below the full-employment threshold; otherwise it strikes the optimal inflation-unemployment balance. Under noncooperation (Proposition 3), each national central bank perceives it can attract capital inflows by raising its policy rate — inflows sustain nontradable demand and reduce the domestic sacrifice ratio of disinflation. But in a symmetric Nash equilibrium, synchronized rate hikes cancel each other through global credit market clearing; only the global monetary contraction remains. The result is lower inflation than under cooperation but higher unemployment — a competitive appreciation trap that mirrors the competitive depreciation failures of the Great Depression and the 2008 crisis, but in the opposite direction (global scarcity rather than deficiency of tradables). In a numerical example calibrated to α = 0.64 (convex tradable supply, implying 0.57 price-output elasticity, from Boehm and Pandalai-Nayar 2022) and ω = 0.3 (US pre-COVID tradables share), a 3 percentage point demand reallocation (matching the US COVID episode) requires approximately 1.5 percentage points of inflation to maintain full employment under cooperation; without any inflation, unemployment rises by approximately 8 percentage points. At ω₀ = 0.35, the uncooperative equilibrium reduces inflation by approximately 1 percentage point relative to cooperation but pushes unemployment to approximately 7 percent. For the COVID-19 episode, the authors conclude gains from cooperation were likely small (full employment maintained globally); for the 1980s synchronized tightening — when central banks explicitly sacrificed employment to fight inflation — the model implies substantially positive gains, consistent with the heated cooperation debates and the 1985 Plaza Accord.

Summary of a forthcoming paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. How does a demand reallocation shock generate an inflation-unemployment tradeoff?

A shift in preferences toward tradable goods (ω₀ > ω) reduces demand for nontradable goods, causing nontradable firms to fire workers; since nominal wages are rigid, the only way to sustain full employment is through a rise in the price of tradables (P^T), which operates through three distinct channels. First, higher P^T raises tradable sector firms’ real revenue per worker (nominal wages fixed), inducing them to hire more workers and expand output — the direct labor demand channel. Second, higher P^T generates income effects: as tradable output and income rise, households increase consumption of both tradable and nontradable goods, boosting nontradable employment through the income channel. Third, higher P^T generates expenditure switching away from tradables and toward nontradables (since nontradable goods become relatively cheaper), which also sustains nontradable employment. All three channels require letting P^T rise, which means tolerating inflation. In this sense, the demand reallocation shock acts as a cost-push shock — it shifts the Phillips curve upward, so that higher inflation is required to achieve any given level of employment. If the inflation cost is sufficiently low, the optimal response allows full employment; otherwise an interior solution trades off inflation against economic slack.

Q2. What is the optimal cooperative monetary policy, and how large are the quantitative tradeoffs?

Proposition 1: under international cooperation, the optimal response to ω₀ > ω entails a rise in inflation; if the full-employment inflation level P^fe satisfies χ’(P^fe) ≤ (1/ω₀)(α/(1−α) + 1 − ω₀), the cooperative optimum achieves full employment; otherwise the interior optimum sets χ’(P̄) equal to that expression, balancing marginal inflation cost against marginal employment benefit. The cooperative optimum is strictly superior to strict inflation targeting (P = 1) because the latter allows large unemployment without achieving any structural rebalancing. The global central bank internalizes the income effect from tradable expansion: as Y^T rises, households immediately spend the income on consumption of both goods, further boosting nontradable employment — an amplification mechanism that self-oriented national banks will not fully internalize. In the calibrated numerical example (α = 0.64, ω = 0.3, χ(P) = χ̄(P−1)²/2 with χ̄ = 299.25), a reallocation shock matching the US COVID-19 episode (ω₀ − ω ≈ 0.03) requires approximately 1.5 percentage points of inflation to maintain full employment; under strict inflation targeting (P = 1), unemployment rises by approximately 8 percentage points. These magnitudes are consistent with the observation that during the pandemic inflation cycle, central banks were willing to allow inflation rather than trigger a labor market collapse.

Q3. How does capital mobility change the inflation-unemployment tradeoff faced by individual countries?

Capital mobility reduces the domestic sacrifice ratio — the employment cost of disinflation — through two channels: trade deficits directly sustain nontradable demand (offsetting the fall in tradable sector employment), and they buffer tradable consumption from drops in domestic tradable output. When a single country contracts its monetary policy and P^T falls, domestic tradable output falls; but households react by borrowing internationally, so domestic consumption of tradables falls by less than one-for-one with output (formally: ∂C^T/∂Y^T = ω_{i,0}(1−β)/(ω_{i,0}(1−β)+β) < 1). Capital inflows thus sustain nontradable demand and nontradable employment, partially offsetting the contractionary effect on employment. From each country’s perspective, containing inflation “exports” part of the output loss abroad, making disinflation individually less costly than in a closed economy. This is precisely what creates the coordination failure in the global case: each country perceives a lower sacrifice ratio for disinflation because it does not internalize that this lower sacrifice ratio exists only if the rest of the world continues to produce and lend tradable goods.

Q4. How does the coordination failure arise in a global reallocation shock, and what is the precise mechanism of competitive appreciations?

Proposition 3: in a Nash equilibrium with a global symmetric shock, the full-employment inflation level P^fe coincides with the cooperative benchmark (since C^T_i = Y^T_i in symmetric equilibrium and capital flows net to zero), but if the inflation cost is high enough, self-oriented central banks impose a lower inflation ceiling (MP^u < MP^c) — resulting in lower inflation and higher unemployment than cooperation. Each national central bank individually seeks to reduce domestic inflation by hiking its policy rate to attract capital inflows (which ease the nontradable sector employment constraint through the open economy Phillips curve). But the individual strategy of hiking to attract inflows — which amounts to trying to appreciate the exchange rate (S_i = P^T_{i,t}/P^T_t) — is frustrated in a symmetric Nash equilibrium: when all countries hike simultaneously, capital flows net to zero globally, exchange rates remain unchanged, and only the synchronized monetary contraction remains. This is the mechanism of competitive appreciations: countries try to fight domestic inflation by appreciating their currencies, but appreciate against each other, leaving only a global slump. In the numerical example at ω₀ = 0.35, the uncooperative equilibrium reduces inflation by approximately 1 percentage point relative to cooperation but pushes unemployment to approximately 7 percent (vs. full employment under cooperation at that shock size).

Q5. How do competitive appreciations differ from competitive depreciations, and what are the scope conditions?

Competitive appreciations are the mirror image of competitive depreciations (which characterized the Great Depression and the aftermath of the 2008 GFC): in both cases each country uses its monetary policy to shift costs abroad, but the direction differs — depreciations arise during periods of weak global demand when countries try to steal demand from neighbors; appreciations arise during periods of global tradable goods scarcity and high inflation when countries try to export inflation. The structural difference is the initial state: competitive depreciations occur when global aggregate demand is deficient and the zero lower bound binds — each country wants to depreciate to boost exports; competitive appreciations occur when global demand for tradables is strong relative to supply (ω₀ > ω) and inflation is high — each country wants to appreciate to attract capital inflows that buffer domestic employment from disinflation. The key asymmetry is the direction of the international spillover: in the depreciation case, countries export demand; in the appreciation case, countries export inflation costs. The gains from cooperation in both cases arise for the same reason — the Nash equilibrium involves globally excessive monetary tightening or loosening relative to the cooperative benchmark — but the policy recommendation is opposite in sign.

Q6. What do the model’s predictions imply for the COVID-19 episode and the 1980s disinflation, and when do gains from cooperation materialize?

Gains from monetary cooperation arise only when condition (28) is violated — when central banks are willing to sacrifice full employment to fight inflation; for the COVID-19 episode, gains were likely small (labor markets remained strong throughout); for the 1980s synchronized tightening, the model implies positive gains that would have been achievable through international cooperation. For the COVID-19 episode: throughout the 2021–2023 inflation cycle, unemployment rates in advanced economies remained low and fiscal support maintained aggregate demand, suggesting monetary policy did not sacrifice employment — the model implies condition (28) did not bind and the cooperative optimum was approximately achieved. The world “escaped competitive appreciations this time.” For the 1980s disinflation: the synchronized monetary tightening under Volcker (US), Bundesbank (Germany), and others was accompanied by a deep global recession and explicitly prioritized inflation reduction over employment — precisely the conditions under which condition (28) binds and competitive appreciations generate a suboptimal outcome. These dynamics motivated the heated international cooperation debates of the period, culminating in the Plaza Accord of 1985 (Sachs 1985; Frankel 2015). The model also applies to negative tradable supply shocks (supply chain disruptions, tariffs) in Supplemental Appendix E, so its predictions about cooperation gains extend to protectionist-driven scarcity.

Key concepts

demand reallocation shock : a shift in the preference weight on tradable goods (ω₀ > ω) that reduces nontradable demand relative to tradable demand; in the model it corresponds to a structural demand shift toward durables and goods (as observed during the COVID-19 recovery), creating simultaneous inflationary pressure in tradables and deflationary pressure in nontradables, and generating an inflation-unemployment tradeoff absent in standard cost-push formulations.

convex tradable supply : the feature of the tradable sector (parameterized by α > 0) whereby supply is upward-sloping due to capacity constraints — a 1% rise in the tradable goods price P^T raises tradable output by (1−α)/α percent; calibrated to α = 0.64 (implying a 0.57 price-output elasticity) following Boehm and Pandalai-Nayar (2022) for sectors at high capacity utilization; without this feature, tradable supply would be perfectly elastic and the inflation-unemployment tradeoff would disappear.

competitive appreciations : the Nash equilibrium coordination failure in which each national central bank hikes its policy rate to attract capital inflows (reducing domestic disinflation costs), generating nominal exchange rate appreciation; since all countries do this simultaneously, appreciations cancel out in equilibrium, leaving only a globally excessive monetary contraction with lower-than-cooperative inflation and higher-than-cooperative unemployment; mirror image of competitive depreciations but arising from global scarcity (not deficiency) of tradables.

sacrifice ratio : the employment cost per unit of disinflation; reduced in open economies relative to closed economies because capital inflows buffer domestic tradable consumption from drops in domestic tradable output, and sustain nontradable demand; self-oriented central banks perceive a lower sacrifice ratio than a global central bank, which is the source of the competitive appreciation externality.

nominal wage rigidity : the short-run friction that makes demand reallocation shocks costly: with flexible wages, reallocation from nontradable to tradable employment would occur through real wage adjustment alone; with rigid nominal wages, real wages fall only if tradable goods prices rise (inflation), so monetary accommodation is required for structural reallocation without unemployment.

Optimal Public Transportation Networks: Evidence from the World's Largest Bus Rapid Transit System in Jakarta

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

This paper studies how commuter preferences over wait times, travel times, and transfers should shape the design of urban bus networks, using the world’s largest Bus Rapid Transit (BRT) system — TransJakarta in Jakarta, Indonesia — as the empirical laboratory. The setting provides unusually rich identification: between January 2016 and February 2020, TransJakarta launched 93 new BRT and non-BRT feeder routes in a staggered, city-wide expansion, during which the operating bus fleet more than doubled from roughly 700 to over 1,600 vehicles. The authors combine over 500 million smart-card tap records, GPS tracking of every bus at 5–10 second intervals, and anonymized smartphone location data covering 35 million weekday trips from 2.3 million devices.

The paper proceeds in three steps. First, the authors classify new route launches into three event types and estimate their causal impact on ridership via difference-in-differences. Event 1: a new direct connection between an origin-destination pair already served by transfer only, with no travel-time improvement — raises BRT ridership by 0.16 log points. Event 2: a new direct connection that also reduces travel time (by 0.29 log points on average) — raises ridership by 0.27 log points. Event 3: additional buses on an already-directly-connected pair, which increases the bus arrival rate by 0.32 log points and reduces wait times — raises ridership by 0.09 log points, implying a ridership elasticity with respect to wait times of approximately −0.29 for BRT. For non-BRT routes the implied wait-time elasticity is −1.05, raising the possibility of multiple equilibria in service levels. Crucially, none of the three event types produce detectable increases in aggregate trip volumes measured by smartphone data, implying the ridership gains reflect modal substitution toward the bus rather than trip generation.

Second, the authors estimate a structural demand model. At its core is a route-choice model in which bus arrivals follow independent Poisson processes, so wait times are exponentially distributed and idiosyncratic. This formulation avoids the red-bus/blue-bus aggregation problem endemic to logit models. Commuters are also allowed to be partially inattentive to routes whose travel time exceeds the fastest available option by more than an estimated threshold. Structural parameters are recovered by classical minimum distance, matching seven reduced-form moments. Key findings: wait time is valued 2.4 times more than time on the bus for BRT routes, and 4.2 times more for non-BRT routes. There is no additional transfer penalty beyond the wait time and travel time costs of the second leg. Commuters pay significantly less attention to options with travel time more than roughly 34–44 percent above the fastest option in their choice set.

Third, the authors use the estimated preference parameters to characterize optimal bus networks. Because the optimization problem is high-dimensional (418 grid cells, 1,536 possible edges, yielding on the order of 10^500 configurations) and exhibits neither global convexity nor simple complementarity, they reformulate the social planner’s problem as a discrete choice over networks with additive logit shocks — effectively sampling from a multinomial logit distribution via simulated annealing. The result: optimal networks cover approximately 66 percent of grid cells versus 42 percent under the actual TransJakarta network, and would give 91 percent of Jakarta residents bus access versus 73 percent currently. Bus frequency in the city center is somewhat lower in the optimal network. Despite commuters’ high sensitivity to wait times, the current network concentrates too many buses in the city center where wait times are already short, rather than extending reach to underserved areas. Comparative statics show that doubling the wait-time cost parameter produces much more concentrated optimal networks (23 percent of origin-destination pairs connected, 41 percent fewer than baseline), while increasing the transfer penalty by the equivalent of 15 minutes of wait time raises the direct-connection share of served pairs from 12 to 16 percent.

Q: What are the three event types and why are they analytically distinct?

A: Event 1 is the launch of the first direct route between an origin-destination pair already connected by transfer, where the direct route is not faster than the existing transfer option; it isolates the effect of directness absent a travel-time change. Event 2 is the same but with a faster direct route (average reduction of 0.29 log points in travel time), combining directness and speed improvements. Event 3 is the launch of a new route that overlaps an existing direct route, increasing bus frequency and cutting wait times (arrival rate up 0.32 log points) without substantially changing travel time or directness. The three events together provide variation across the key dimensions — directness, speed, and frequency — needed to separately identify commuter preference parameters.

Q: What are the main ridership effects and how large are they in levels?

A: For BRT routes, Event 1 raises ridership by 0.16 log points (approximately 19 additional riders per week for a treated origin-destination pair with a baseline of 111 weekly riders), Event 2 by 0.27 log points (approximately 24 additional riders per week), and Event 3 by 0.09 log points (approximately 20 additional riders per week). For non-BRT routes, proportional effects are larger but level effects are similar: Event 1 yields roughly 34 additional weekly riders, Event 2 roughly 21, and Event 3 roughly 15. Event-study graphs show clear, discrete jumps in ridership at route launch with no pre-trends, and some gradual adjustment in the months following.

Q: What does the paper find about aggregate trip generation versus modal substitution?

A: Using smartphone location data to measure all trips regardless of mode, the authors find no statistically significant increase in aggregate trip volumes for any of the three event types. For BRT Event 1, the estimated aggregate-trip coefficient is −0.008 with a standard error of 0.051, allowing rejection at the 95 percent level of any positive impact above roughly 0.091 log points — small relative to the precise 0.11 log-point bus ridership effect in the same sample. The authors interpret this as evidence that the ridership gains over the 10-month post-event window reflect substitution from private modes (motorcycles, cars, taxis) toward TransJakarta rather than trip generation, and they use this null result to justify holding destination choices fixed in the structural model.

Q: How does the model avoid the red-bus/blue-bus aggregation problem?

A: The paper’s route-choice model assumes bus arrivals follow independent Poisson processes, so wait times are exponentially distributed. A key proposition (Proposition 1) proves that splitting one route into two identical routes with half the buses each produces exactly the same choice probabilities and expected utility as the original single route — because the sum of two independent Poisson processes is itself Poisson with the summed rate. Standard logit models fail this invariance because splitting a route creates two options with independent error draws, artificially inflating expected utility. The invariance property is essential for the optimal network design exercise, where the planner freely reallocates buses across routes.

Q: What are the estimated preference parameters and what do they imply about commuter behavior?

A: The paper estimates that wait time is valued 2.4 times more than time on the bus for BRT routes and 4.2 times more for non-BRT routes. There is no additional transfer disutility beyond the wait time and travel time costs implied by the extra leg. Commuters become substantially inattentive to routes with travel time more than approximately 34 percent above the fastest available option (BRT threshold) or 44 percent (non-BRT). The high relative cost of waiting versus riding reflects both the discomfort of waiting at exposed non-BRT stops and the fact that TransJakarta runs without a published schedule, so commuters cannot minimize wait time by timing arrivals.

Q: What explains the non-BRT wait-time elasticity exceeding −1?

A: For non-BRT routes, Event 3 raises ridership by 0.450 log points while raising the bus arrival rate by 0.425 log points, yielding an implied elasticity of ridership with respect to wait times of −1.05. Because the baseline arrival rate for non-BRT treated pairs is 2–4 times lower than for BRT pairs, the absolute reduction in wait time per additional bus is much larger. An elasticity exceeding −1 in absolute value implies that adding buses on some non-BRT routes could increase ridership enough to maintain or even raise average ridership per bus — the extreme form of the Mohring effect — suggesting the possibility of a high-ridership/low-wait-time equilibrium distinct from the current low-ridership/high-wait-time one.

Q: How is the optimal network characterized and what algorithm is used?

A: The social planner chooses a network to maximize utilitarian welfare (average expected utility across all commuters) from the estimated demand model, plus a network-level logit shock capturing cost and other factors outside the model. This transforms the combinatorially explosive optimization into sampling from a multinomial logit distribution over networks, which the authors approximate using simulated annealing. They run the algorithm multiple times to obtain a sample of networks drawn asymptotically from the planner’s distribution, then estimate optimal network characteristics and comparative statics from sample analogs. The theoretical framework is general and, the authors note, applicable to other high-dimensional spatial planning problems where welfare differences can be computed for pairs of counterfactuals.

Q: How does the optimal network differ from the current TransJakarta network?

A: The typical optimal network covers approximately 66 percent of 2km grid cells versus 42 percent for the actual network, and 91 percent of Jakarta residents would have bus access versus 73 percent currently. The optimal network reduces bus frequency in the city center relative to the current network, accepting longer wait times there in order to extend reach to peripheral areas. The paper finds no tension between distributional and efficiency concerns in this setting — expanding coverage improves both aggregate welfare and access for underserved areas.

Q: What do the comparative statics reveal about the sensitivity of optimal network design to preference parameters?

A: Doubling the wait-time cost parameter leads to substantially more concentrated optimal networks: only 23 percent of origin-destination pairs are connected, 41 percent fewer than in the baseline optimal network. This is because higher wait-time costs make it more valuable to concentrate buses on fewer routes to achieve short headways. Increasing the transfer penalty by the equivalent of 15 minutes of wait time raises the share of connected location pairs with a direct (non-transfer) connection from 12 to 16 percent. These comparative statics link micro-level preference parameters to macro-level network topology, clarifying which parameters most influence design choices.

Q: How does the paper validate the destination imputation from tap-in-only smart card data?

A: For the subset of BRT stations where tap-out is enforced (36 percent of stations), the authors estimate bivariate regressions of imputed daily ridership shares against actual observed ridership shares, obtaining R-squared of 0.85. They also show robustness by varying the grid cell size from 500 meters to 2 kilometers, finding no systematic decline in treatment effect magnitudes, which rules out large displacement effects within the network as an explanation for the results.

Q: Does the response to network improvements vary by local poverty rates?

A: The authors interact all six event types with an indicator for above-median poverty rate at the origin grid cell (from SMERU 2014 data), controlling for population. They find no clear pattern of heterogeneity by income level — richer and poorer areas respond similarly to service improvements. The paper notes this absence of heterogeneity as relevant context for interpreting optimal network design: the case for extending reach is not offset by a differential preference for frequency among poorer commuters.

Mohring Effect: The externality arising from ridership responsiveness to wait times — more riders justify more buses, which reduce wait times for all riders, further increasing ridership. The paper estimates a BRT wait-time elasticity of −0.29, confirming the effect operates in Jakarta; for non-BRT the elasticity of −1.05 suggests the possibility of multiple equilibria in service levels.

Negative Exponential Distribution Model (Daganzo 1979): The route-choice model used in the paper, in which bus arrivals on each route follow independent Poisson processes and wait times are exponentially distributed. The model is invariant to aggregation of identical routes (avoids the red-bus/blue-bus problem) and yields tractable closed-form expressions for choice probabilities and expected utility.

Partial Inattention: The model feature whereby commuters assign near-zero effective arrival rates to bus options whose travel time exceeds the fastest available option by more than an estimated threshold (34–44 percent depending on route type). Captures the empirical finding that commuters in a large, complex network do not appear to consider all available options.

Event Types (1, 2, 3): The paper’s taxonomy of service improvements induced by new route launches. Event 1 isolates the value of directness (new direct route, no speed gain). Event 2 combines directness and speed (new direct route that is also faster). Event 3 isolates the value of frequency (additional buses on an already-direct route, reducing wait time without changing travel time).

Optimal Network Characterization via Social Planner’s Logit: The paper’s approach to the combinatorially intractable network optimization problem. The planner is modeled as making a logit discrete choice over all possible networks, with welfare from the demand model plus a network-level idiosyncratic shock. Sampling via simulated annealing yields estimates of optimal network characteristics and comparative statics without requiring identification of a single globally optimal network.

Network Concentration vs. Extensiveness Tradeoff: The core design tension the paper formalizes — for a fixed bus fleet, concentrating buses on fewer routes reduces wait times on served routes but leaves more areas without coverage, while spreading buses across more routes extends reach at the cost of longer headways. The estimated preference parameters (high wait-time sensitivity) make this tradeoff non-trivial; nonetheless, the paper finds the current network is too concentrated relative to the optimum.

Optimal Taxation and Market Power

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

Overview

This paper asks whether and how optimal income taxation should change when firms have market power. The question is motivated by the documented rise in economy-wide markups since 1980, which has compressed the labor share, widened the gap between worker and entrepreneurial income, and generated allocative inefficiency through excessive pricing.

The authors develop a Mirrleesian optimal taxation framework augmented with three features absent from the canonical literature: (i) oligopolistic intermediate goods markets with endogenous, variable markups, (ii) heterogeneous firm productivities, and (iii) two occupational groups—wage-earning workers and profit-earning entrepreneurs—whose abilities are private information. Entrepreneurs strategically set prices under Cournot competition, which means that the tax system affects profits both through a firm’s own behavior and through the responses of its competitors. This strategic interaction is the critical novelty relative to prior work that assumes monopolistic competition.

The main theoretical contribution is the derivation of optimal tax formulas for both labor income and profit income that decompose into four named components: (i) the Mirrleesian incentive component, which reflects the standard trade-off between redistribution and labor supply distortions; (ii) the Pigouvian component, which corrects for the externality from market power by subsidizing labor and entrepreneurial effort to offset the output shortfall from high markups; (iii) the Reallocation Effect (RE), which shifts the profit tax to redirect labor inputs from low-markup firms to high-markup firms where labor is inefficiently scarce, and which emerges only under heterogeneous markups; and (iv) the Indirect Redistribution Effect (IRE), which uses changes in competitors’ product prices—a channel present only under oligopolistic (not monopolistic) competition—to redistribute income between entrepreneurs.

For the labor income tax, the dominant force is the Pigouvian component. As average markups rise, the Pigouvian subsidy to labor supply grows, mechanically reducing optimal labor income tax rates. The profit tax is shaped by all four components in opposing directions; the net quantitative effect is resolved empirically.

The model is calibrated to match distributions of labor income (from the Current Population Survey), profits (from Compustat-based data in De Loecker, Eeckhout, and Unger 2020), and firm-level markups (also from De Loecker, Eeckhout, and Unger 2020, using the cost-minimization approach) for the US in 1980 and 2019. The cost-weighted average markup rose from 1.25 in 1980 to 1.33 in 2019, with the increase concentrated at the top of the markup distribution.

The central quantitative prescription is that the optimal labor income tax rate should decline by 7.7 percentage points between 1980 and 2019 (average optimal rate falls from 22.0 percent to 14.3 percent), while the optimal profit tax rate should rise by 2.2 percentage points on average (from 58.4 percent to 60.5 percent) and by 29.1 percentage points at the top. The decline in the labor income tax is driven primarily by the rise in average markups reducing the Pigouvian component. The increase in the profit tax, especially at the top, is driven primarily by the Mirrleesian component operating through the skill gap, which rises because higher markups reduce profit elasticity. The Pigouvian and reallocation components push in the opposite direction on the profit tax, but the Mirrleesian effect dominates.

The optimal profit tax structure is regressive for large, high-markup firms—reflecting the RE, which requires lower tax rates for high-markup firms to incentivize labor reallocation toward them—but less regressive in 2019 than in 1980, reflecting the distributional tightening from rising markup inequality.

Robustness checks across parameter values for the social welfare curvature k, the span of control ξ, and the elasticity of substitution σ confirm that the directional results hold: labor income tax rates decrease and profit tax rates increase from 1980 to 2019 across all parameter configurations. Extensions to nonlinear sales taxes and conditioning on markups confirm that even when the planner can observe markups directly, the first-best is not achievable because markups are endogenous to entrepreneurs’ unobservable decisions.

In depth

Q1. What is the fundamental difference between this paper’s model and prior work on optimal taxation with market power?

Prior work using monopolistic competition (e.g., Gürer 2021; Boar and Midrigan 2019) assumes each entrepreneur holds monopoly power in its own market, so no strategic interaction exists between firms. Under monopolistic competition, entrepreneurs price to maximize utility given competitors’ choices, and the envelope theorem implies that tax changes have no first-order effect on prices or utility through the pricing channel—the Indirect Redistribution Effect (IRE) disappears. In this paper, entrepreneurs compete in Cournot oligopolistic markets with a finite number of firms I, so each firm’s pricing depends on competitors’ output. A change in one firm’s output (induced by taxation) shifts competitors’ prices, opening a redistribution channel through product markets that is entirely absent in monopolistic competition. Additionally, the Reallocation Effect (RE) emerges only when firm-level markups are heterogeneous, which requires oligopolistic (not perfectly competitive) markets.

Q2. What are the four components of the optimal tax formula and how does each relate to market power?

The optimal tax wedge for both labor and profit income decomposes into four components. First, the Mirrleesian component reflects the standard trade-off between redistribution and the efficiency cost of taxation; in the presence of market power, it is modified because the skill gap for entrepreneurs depends on markups through the profit elasticity. Second, the Pigouvian component corrects the externality from market power, which causes prices to exceed marginal cost and output to be inefficiently low; it implies a subsidy to both worker and entrepreneurial effort, scaled by the reciprocal of the average markup (for the labor tax) or firm-level markup (for the profit tax). Third, the Reallocation Effect (RE) applies only to the profit tax and reflects that labor should be shifted toward high-markup firms where it is inefficiently underemployed; it reduces the tax rate for firms whose markup exceeds the average. Fourth, the Indirect Redistribution Effect (IRE) captures redistribution through competitor price changes under oligopolistic interaction; it can either raise or lower the profit tax rate depending on the distribution of social welfare weights and the cross-inverse demand elasticity.

Q3. What happens to the labor income tax formula as average markups rise?

The labor income tax formula contains a Pigouvian component equal to the reciprocal of the employment-weighted average markup. As average markups rise, this reciprocal falls, reducing the optimal labor income tax rate. Quantitatively, the optimal average labor income tax rate declines from 22.0 percent in 1980 to 14.3 percent in 2019, a decrease of 7.7 percentage points. In a purely competitive benchmark economy, the top labor income tax rate would be around 60 percent (consistent with Saez 2001); in the calibrated model with market power, it is 34.2 percent in 1980 and 28.7 percent in 2019. The Pigouvian component accounts for essentially the entire difference because the Mirrleesian component, when calibrated to the same labor income distribution, is unchanged.

Q4. How does the Mirrleesian component cause the top profit tax rate to rise with market power?

The Mirrleesian component of the profit tax is driven by the skill gap, defined as the proportional rate of change in the composite entrepreneur ability measure. The skill gap depends on markups through the profit elasticity: as markups rise, profit elasticity falls (since profit elasticity is approximately the reciprocal of markup minus the span-of-control parameter minus the inverse of the labor supply elasticity term), which increases the skill gap. A higher skill gap amplifies the income divergence across entrepreneur types, increasing the Mirrleesian incentive to redistribute at the top. Quantitatively, Figure 5 shows that the rise in the skill gap from 1980 to 2019 tracks almost exactly the change in the inverse of profit elasticity, confirming that markup changes—not changes in the ability distribution—are the primary driver of increased Mirrleesian pressure on top profit taxes.

Q5. How does the Reallocation Effect influence the structure (progressivity) of the profit tax?

The RE term equals the ratio of the average markup to the firm-level markup minus one: RE(θe) = μ/μ(θe) − 1. For firms with markups above the average, RE is negative, reducing their optimal tax rate; for firms below the average, RE is positive, increasing it. This implies that the optimal profit tax should be regressive relative to markup (i.e., high-markup firms face lower marginal tax rates), even though the overall profit tax rises on average. This provides a novel rationale for why the profit tax schedule in practice is less progressive—or even regressive—for large firms. As markups rise across the distribution, the reallocation effect pushes down the top profit tax but does not offset the larger increase from the Mirrleesian component in the quantitative exercise.

Q6. What is the Indirect Redistribution Effect and why does it disappear under monopolistic competition?

The IRE captures the change in entrepreneurial utility that arises because a tax reduction for one entrepreneur increases their output, which reduces the prices of substitute goods produced by competitors, thereby lowering competitors’ incomes. Under oligopolistic competition with I > 1 firms per market, the cross-inverse demand elasticity is nonzero, so competitor prices are sensitive to any one firm’s output decision, and this redistribution channel is open. Under monopolistic competition (I = 1), each entrepreneur is the sole producer in its market; competitors’ prices do not depend on the firm’s output, the cross-inverse demand elasticity is zero, and the IRE vanishes by the envelope theorem. The IRE is also absent in perfectly competitive economies. Empirical evidence for the US suggests the hazard ratio of profits is sufficiently high that the IRE generally pushes toward a lower top profit tax rate, but the Mirrleesian effect dominates in the quantitative results.

Q7. What is the quantitative effect of rising markups on the optimal tax rates, and what drives the net change in the profit tax?

The model calibrated to 1980 and 2019 US data prescribes a decline in the optimal average labor income tax rate of 7.7 percentage points (from 22.0 to 14.3 percent) and an increase in the optimal average profit tax rate of 2.2 percentage points (from 58.4 to 60.5 percent). At the top of the profit distribution, the increase is 29.1 percentage points. The net profit tax increase results from four opposing forces: the Pigouvian component falls (pushing toward lower taxes) and the RE decreases for high-markup firms (also pushing down the top rate), while the IRE and especially the Mirrleesian component rise (pushing up top rates). The Mirrleesian effect is the dominant force, driven by rising markup inequality reducing profit elasticity and widening the skill gap for top entrepreneurs.

Q8. How does the counterfactual analysis isolate the role of markups from productivity changes?

The counterfactual fixes the markup distribution at its 1980 level while holding the 2019 productivity distribution constant, then solves for optimal taxes. The result is that high-profit entrepreneurs would face lower optimal tax rates under 1980 markups than under 2019 markups, while low-profit entrepreneurs would face higher rates. Decomposing the difference, the Pigouvian component and the RE are larger for high incomes under 1980 (lower) markups, making the profit tax more regressive, while the IRE and the Mirrleesian component are smaller under 1980 markups, producing a lower top rate. The increase in the Mirrleesian component due to the markup increase from 1980 to 2019 is identified as the primary reason top profit taxes rise. This isolates the markup channel from the productivity channel in accounting for changes in optimal taxes.

Q9. What does the robustness analysis reveal about parameter sensitivity?

The main qualitative result—labor income taxes decline and profit taxes rise from 1980 to 2019—holds across a broad parameter space. The optimal profit tax rate is largely insensitive to the social welfare curvature parameter k: across k ∈ {0.77, 1, 3}, the average optimal profit tax rate is approximately 58 percent in 1980 and 61 percent in 2019. The optimal average labor income tax rate is more sensitive to k: for k = 0.7, 1, and 3, the 1980 rates are 20.3, 26.7, and 44.6 percent, and the 2019 rates are 12.5, 19.4, and 39.1 percent, respectively. Changes in the span-of-control parameter ξ and the substitution elasticity σ do not affect the labor income tax wedge schedule directly but do influence it indirectly through the markup distribution. The directional results are confirmed for all tested parameter configurations.

Q10. What is the role of the “additivity property” from prior externality literature, and why does it fail here?

The additivity property from the Pigouvian externality literature (see Kopczuk 2003; Sandmo 1975) states that the Pigouvian correction is separable from other components of the optimal tax formula, implying that rising markups would simply decrease the optimal tax rate (since 1/μ falls). This property holds under simplifying assumptions that abstract from the general equilibrium and incentive effects of market power. In the present model, the additivity property does not hold because markups enter all four components of the optimal tax formula—not just the Pigouvian term—through the skill gap (Mirrleesian component), the RE, and the IRE. As a result, rising markups can increase the optimal profit tax rate even though the Pigouvian component falls, because the skill gap and Mirrleesian force dominate.

Q11. Can the government attain the first-best by conditioning taxes on markups?

No. The paper demonstrates that even if the planner can observe and condition taxes on firm-level markups, the first-best is not achievable. The reason is that markups are endogenous to the entrepreneurs’ unobservable decisions: an entrepreneur’s markup depends on their privately known type and chosen output. When the planner designs a mechanism that conditions on markup, the incentive constraint facing entrepreneurs remains the same as in the benchmark model, because the promise-keeping constraints are independent of the entrepreneur’s true type when markups are observable. The optimal allocation with markup-conditioned taxes is shown to be equivalent to the second-best with nonlinear sales taxes, which still falls short of the first-best.

Q12. What are the policy implications for the design of the profit tax schedule?

The model yields three concrete prescriptions for the joint design of labor and profit income taxes in the context of rising market power. First, labor income taxes should be reduced and top profit taxes should be increased as market power rises. Second, for large, high-productivity firms the profit tax should be designed to be appropriately regressive to enhance allocative efficiency through the Reallocation Effect—this provides a new normative justification for why profit tax schedules observed in practice are often less progressive than labor income taxes. Third, while profit taxes should be regressive for large firms, the degree of regressivity should decrease as market power rises, reflecting the trade-off between efficiency and equality: higher markups increase the Mirrleesian pressure for redistribution at the top, reducing the optimal regressivity.

Key Concepts

Mirrleesian component (of the optimal tax formula): The standard incentive component of the optimal tax, capturing the trade-off between direct redistribution and the efficiency cost of taxation. In the presence of market power, this component is modified because the skill gap for entrepreneurs depends on markups through the profit elasticity: higher markups reduce profit elasticity, widen the skill gap, and amplify the Mirrleesian force toward higher top profit taxes.

Pigouvian component: The correction in the optimal tax formula for the externality from market power. Because oligopolistic pricing causes output to be inefficiently low, the optimal tax subsidizes both worker and entrepreneurial labor supply. In the labor income tax formula, the Pigouvian component is the reciprocal of the employment-weighted average markup; in the profit tax formula, it is the reciprocal of the firm-level markup. As average markups rise, the Pigouvian component reduces the optimal labor income tax rate.

Reallocation Effect (RE): A component of the optimal profit tax formula that captures the efficiency gain from reallocating labor inputs from low-markup firms (where labor’s marginal product is high relative to value) to high-markup firms (where labor demand is inefficiently low). It equals the ratio of the average markup to the firm-level markup minus one. It implies a lower optimal marginal tax rate for firms with markups above the average, producing a regressive structure in the profit tax for large firms. This effect is absent under monopolistic competition (uniform markups) and in competitive markets.

Indirect Redistribution Effect (IRE): A component of the optimal profit tax formula specific to oligopolistic competition, capturing redistribution through competitor prices. Lowering the marginal tax rate of a high-productivity entrepreneur raises their output, which reduces the prices of substitutable goods produced by their competitors, thereby lowering competitors’ incomes and redistributing toward workers who benefit from lower prices. This effect is present only when the cross-inverse demand elasticity is nonzero—i.e., only under oligopolistic (Cournot) competition with multiple firms per market—and vanishes under monopolistic competition and in the limit as the number of firms grows to infinity.

Skill gap (for entrepreneurs): The proportional rate of change in the composite entrepreneur ability measure with respect to entrepreneur type, analogous to the Mirrleesian skill gap for workers. Under market power, the entrepreneur skill gap depends on the markup through the profit elasticity: as firm-level markups rise, profit elasticity falls, the skill gap increases, and the income dispersion across entrepreneurs widens, which amplifies the Mirrleesian incentive to redistribute at the top and raises the optimal top profit tax rate.

Symmetric Cournot Competitive Tax Equilibrium (SCCTE): The equilibrium concept used in the paper. It is a combination of a tax system, symmetric allocation, and symmetric price system such that all agents (final goods producer, entrepreneurs of each type, workers) are optimizing, strategic interaction in the intermediate goods market is a Cournot Nash equilibrium within each granular market, and all commodity and labor markets clear. Strategic interaction is restricted to within each granular market (firms in the same market compete), so decisions across markets are taken as given.

Composite ability: A combined measure of entrepreneur productivity that determines equilibrium allocations and optimal taxation in the nested-CES economy. It aggregates the entrepreneur’s raw ability (affecting output capacity) and the demand parameter (affecting the market-level markup). The markup-relevant component and the quantity-relevant component are not perfect substitutes in the composite, since equilibrium prices depend on their specific composition while equilibrium quantities depend only on their combined value.

Place-Based Redistribution

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

Place-Based Redistribution: Overview

Research Question

Should national governments redistribute income to residents of poor areas through place-based transfers, or should redistribution rely solely on place-blind (income-only) taxes? The longstanding view in urban economics—“help poor people, not poor places”—holds that place-based aid is inefficient because it channels activity to less productive locations. This paper challenges that view by formalizing the conditions under which place-based redistribution improves on purely income-based transfers, using tools from optimal tax theory embedded in a spatial equilibrium model.

Model and Methodology

The paper develops a two-location model (“Distressed” and “Elsewhere”) with a unit mass of heterogeneous households who differ in skill level (θ) and idiosyncratic preference for living in Distressed (φ). Households choose where to live and how much to earn, facing competitive labor and housing markets in each location. Locations may differ in amenity levels, wage schedules (which may embody skill-specific comparative advantage), and housing costs. A utilitarian planner sets location-specific income tax schedules—observed earnings and location are the only signals of unobserved skill—maximizing a weighted average of household utilities and landlord profits subject to a budget constraint.

The paper proceeds in three steps. First, it derives closed-form conditions for the optimality of a lump-sum place-based transfer under a fixed income tax. Second, it characterizes fully general optimal nonlinear, location-specific marginal tax rate (MTR) schedules (Proposition 2). Third, it calibrates the model numerically, anchoring to the U.S. Empowerment Zone (EZ) program.

Three Sorting Mechanisms and Their Policy Implications

The paper identifies three polar mechanisms that generate sorting of lower-skill households into Distressed:

Skill-taste correlation: higher-skill households have stronger tastes for Elsewhere, independent of wages or rents.
Comparative advantage: higher-skill workers are relatively more productive in Elsewhere.
Income-based sorting: because Elsewhere is more expensive, lower-income households are priced into Distressed.

Under skill-taste correlation, place-based transfers to Distressed are unambiguously welfare-improving even when income taxes are already optimal, because high-skill households prefer Elsewhere for reasons that are orthogonal to income. Under comparative advantage, the direction of the optimal transfer depends on migration elasticities: low migration elasticities favor transfers to Distressed, while high migration elasticities can reverse the sign. Under pure income-based sorting (with homogeneous locational preferences), the conditions for superfluous commodity taxation (Atkinson-Stiglitz 1976) are satisfied, and optimal place-based transfers are zero—though idiosyncratic preference heterogeneity restores non-zero optimal transfers even in this case.

Quantitative Findings

Numerical simulations use Census data and ACS moments calibrated to EZ areas. With high migration responsiveness (κ = 0.5, approximating urban EZs) and skill-taste correlation as the sole sorting driver, the optimal average place-based transfer to Distressed is $4,805, with about 40% ($1,943) arising from lower MTRs rather than a higher demogrant. With low migration responsiveness (κ = 4, approximating rural EZs), the optimal transfer more than doubles to $10,918.

When comparative advantage alone drives sorting and migration is low (κ = 4), the optimal transfer to Distressed is $7,091, with a $3,740 larger demogrant. With high migration and comparative advantage, the transfer reverses to −$2,763 (i.e., Elsewhere receives the subsidy). For intermediate migration under comparative advantage (e.g., κ ≈ 1), the optimal policy is nonlinear: the poorest Distressed residents receive a place-based transfer of $1,254, while high-skill Distressed residents face a place-based tax of $12,398 at the 99th percentile.

In the empirically calibrated urban EZ baseline (migration elasticity 0.82, rent ratio 0.86, sorting driven by skill-taste correlation and income effects), the optimal average place-based transfer is $3,143, roughly matching the magnitude of actual EZ wage tax credits (~$3,000 for full-time eligible workers). The demogrant advantage for Distressed is $1,462, with just over half of the transfer arising from lower MTRs.

In the rural EZ baseline (migration elasticity 0.20, rent ratio 0.54, comparative advantage and income effects), the optimal average transfer rises to $4,329, concentrated in lower MTRs rather than a larger demogrant. Halving the migration elasticity from the rural baseline raises the optimal transfer to $6,906, while doubling it reduces the transfer to near zero ($573).

Scope Conditions

All results are derived under the assumption of no market failures; the model deliberately excludes agglomeration spillovers or other Pigouvian motives, attributing the case for place-based redistribution purely to redistributive goals.
The planner observes only earnings and location, not skill type directly.
Household Pareto weights are set equal to one across types in the simulations, so redistribution is driven solely by diminishing marginal utility of consumption.
The model abstracts from interactions with subnational governments, local public services, and endogenous amenities.
Results on the desirability of transfers to Distressed hinge critically on the motive for sorting, not simply on the existence of spatial income inequality.

In depth

Q1. What is the equity-efficiency tradeoff formula for a lump-sum place-based transfer, and what does it reveal?

Lemma 1 shows that the first-order welfare effect of a small per-capita transfer from Elsewhere to Distressed starting from a place-blind tax system is dSWF/dt = (λ̄₁ − λ̄₀) + Eθ{m(0)·[T(z₁*) − T(z₀*)]}. The equity gain (λ̄₁ − λ̄₀) is positive when Distressed households have higher average social marginal welfare weights, which holds when their skill distribution is first-order stochastically dominated by Elsewhere’s. The fiscal cost equals the earnings-tax-revenue loss from movers: households induced to migrate to Distressed who earn less there generate lower tax payments. This formula identifies the earnings response to migration as a sufficient statistic for the efficiency cost of place-based policy.

Q2. What characterizes the optimal lump-sum transfer t* in Proposition 1?

Proposition 1 shows t* = [λ̄₁(t*) − λ̄₀(t*) + Eθ{m(t*)·[T(z₁*) − T(z₀*)]}] / (Eθ[m(t*)] / [L₀(t*)L₁(t*)]). The optimal transfer is larger when (i) the average social marginal welfare weight gap between Distressed and Elsewhere is greater, (ii) migration responses m(t*) are small, and (iii) the earnings difference between locations for marginal movers is small. This formula holds regardless of whether the income tax schedule T(·) is itself set optimally.

Q3. Under skill-taste correlation, why are place-based transfers always welfare-improving even under an optimal income tax?

When sorting is driven by skill-taste correlation (high-skill households have stronger preferences for Elsewhere despite identical wages and rents), the equity gain λ̄₁ − λ̄₀ is positive because low-skill households concentrate in Distressed. A small positive transfer starting from t = 0 also incurs zero fiscal cost because movers between locations face identical wages and do not change their earnings. Thus, welfare unambiguously increases. The key insight is that skill-taste correlation violates the Atkinson-Stiglitz condition: high earners would still prefer Elsewhere even if forced to earn less, so location serves as a proxy for skill not captured by income taxes alone.

Q4. Under comparative advantage, why can the sign of the optimal transfer reverse with migration elasticity?

When higher-skill workers are more productive in Elsewhere, movers to Distressed experience wage and earnings reductions, generating a fiscal externality. When migration elasticities are high (low κ), this fiscal cost is large and can dominate the equity gain, making transfers to Elsewhere optimal (simulated optimal transfer of −$2,763 at κ = 0.5). When migration elasticities are low (high κ), the fiscal cost is small and equity considerations dominate, yielding transfers to Distressed ($7,091 at κ = 4). At intermediate elasticities, the optimal policy is nonlinear, redistributing to poor Distressed residents while taxing rich Distressed residents more.

Q5. Why are place-based transfers superfluous under pure income-based sorting with homogeneous locational preferences?

Example 6 (and its formal proof in Appendix B.3.5) demonstrates that when sorting arises solely from higher rents in Elsewhere and preferences over location are homogeneous (no idiosyncratic φ heterogeneity), the Atkinson-Stiglitz sufficient condition for commodity tax superfluousness is met: hypothetically forcing high earners to earn less would not change their preferred consumption bundle relative to low earners. Hence a place-blind income tax implements optimal redistribution without spatial supplements. As the variance of idiosyncratic location preferences κ shrinks toward zero, Figure 3 confirms that optimal place-based transfers tend toward zero across all three sorting motives.

Q6. What new terms appear in the optimal location-specific MTR formulas (Proposition 2) relative to a standalone-economy optimum?

The optimal MTR schedules in Proposition 2 contain two new terms beyond the standard Mirrlees (1971)/Saez (2001) formula. The term Δτ+(θ) captures the fiscal externality from migration: raising Elsewhere’s MTR at skill level θ and above induces movers to Distressed who change their tax revenue by T₁(z₁*(s)) − T₀(z₀*(s)). The term (λ_L − 1)Δr+(θ) captures the equilibrium rent effect: MTR changes shift households between locations, altering rents in both communities and redistributing between renters and landlords. When λ_L < 1 (landlords are weighted less than average households), the rent term creates additional motives for spatial redistribution depending on the ratio of rents to housing supply elasticities across locations.

Q7. How do housing supply elasticities affect the optimal spatial transfer, and why does the sign differ between urban and rural settings?

The rent redistribution term Δr+(θ) has sign determined by r₁/ϱ₁ − r₀/ϱ₀. For urban EZs, where Distressed has lower rents but also lower housing supply elasticity than Elsewhere (ϱ₁ = 0.24, ϱ₀ = 0.34 in the baseline), this ratio is positive, meaning transfers to Distressed shift households into relatively inelastic markets, raising rents there and generating landlord income. When λ_L < 1, this reduces the desirability of transfers to Distressed. For rural EZs, Distressed has higher housing supply elasticity (ϱ₁ = 0.60), so the ratio is negative: transfers shift households to more elastic markets where rents rise minimally. When λ_L < 1, this actually motivates more transfers to rural Distressed areas. In the 75%-landlord-weight sensitivity, optimal urban transfers fall by ~$1,000 while rural transfers rise by ~$1,000, illustrating this asymmetry.

Q8. What does the urban EZ baseline calibration find about optimal transfers and how does it compare to actual EZ policy?

The urban baseline targets a migration elasticity of 0.82 (from Busso et al. 2013), a Distressed-to-Elsewhere rent ratio of 0.86, and 56% of Distressed residents earning under $50,000. The calibrated κ is 0.44. At the optimum, Distressed residents receive an average place-based transfer of $3,143, with $1,462 as a higher demogrant and the remainder from lower MTRs. By comparison, actual EZs provide a wage tax credit of approximately $3,000 per eligible full-time worker. The paper concludes that the magnitude—but not the capped, flat structure—of EZ transfers approximates the optimal level.

Q9. What does the rural EZ calibration find, and how sensitive are results to migration assumptions?

The rural baseline targets a migration elasticity of 0.20 (from Sprung-Keyser et al. 2022), a rent ratio of 0.54, and 60% of Distressed residents earning under $50,000, with sorting attributed to comparative advantage and income effects. The calibrated κ is 4.06. The optimal average transfer is $4,329, primarily arising from lower MTRs rather than a higher demogrant ($532). Doubling the migration elasticity reduces the optimal transfer to near zero ($573); halving it raises it to $6,906. The direction and magnitude of optimal transfers are therefore highly sensitive to the assumed level of migration responsiveness, highlighting the empirical importance of estimating migration elasticities—particularly heterogeneity in migration by income level and earnings changes for marginal movers.

Q10. Do within-income transfers arising from differences in marital and parental status across communities effectively constitute place-based redistribution?

Online Appendix A investigates this by estimating the implicit place-based transfer induced by marital and parental status differences between EZ communities and the rest of the country. Using ACS tract-level data merged with Piketty-Saez-Zucman distributional national accounts (DINA), the authors find that marital status and parental status have offsetting effects: marital status raises taxes on single households (common in Distressed), while parental status increases transfers to households with children (also common in Distressed). Across all preferred CPS-adjusted estimates, net within-earnings transfers are below $1,000 in magnitude, and the two factors essentially cancel. The authors conclude that marital and parental status differences do not yield substantial de facto place-based redistribution within income levels.

Q11. What does the MTR decomposition (Table 3) reveal about why sorting motives generate different MTR patterns?

The decomposition separates the optimal MTR into a within-community component (standard equity-efficiency tradeoff) and a between-community component (fiscal externality from migration). Under skill-taste correlation with high migration (κ = 0.5), both components contribute positively to the Distressed MTR (0.246 within + 0.234 between = 0.479), yielding lower MTRs in Distressed (0.479) than in Elsewhere (0.510). Under comparative advantage with high migration, the within-community component is negative (−0.111) because high MTRs at the optimum reduce the concentration of high-skill types in Distressed, depressing the standard revenue-raising benefit of MTRs. The large positive between-community component (0.655) reflects the large fiscal externality from movers and overcomes this, yielding higher Distressed MTRs (0.544 vs. 0.509 in Elsewhere). With low migration (κ = 4), between-community components shrink substantially, and MTRs in Distressed fall below Elsewhere in all sorting scenarios.

Q12. What does the crosswalk from urban to rural baseline reveal about which assumptions drive the change in optimal transfers?

Table 5 traces the urban-to-rural transition step by step. Starting from the urban baseline ($3,143 average transfer), replacing the migration elasticity target with the rural value of 0.20 triples the optimal transfer to $9,870. Subsequently replacing skill-taste correlation with comparative advantage as the sorting mechanism reduces the transfer by roughly half ($6,402). Adjusting rent to match the rural ratio (0.54) reduces it further to $2,780, as lower Distressed rent reduces the marginal utility of consumption at the bottom and increases income-based sorting. Targeting the rural income share (60% below $50K) raises it back to $4,140, and incorporating rural housing supply elasticities yields the rural baseline result of $4,329. This decomposition reveals that lower migration responsiveness is the single largest driver of higher optimal transfers in rural settings.

Key Concepts

Place-based redistribution: Transfer schemes in which economic benefits or tax burdens are conditioned on the geographic location of residence, as distinct from place-blind income taxes that condition only on earned income. In this paper, modeled as location-specific tax schedules T_j(z) that may differ across communities j.

Skill-taste correlation: A source of spatial sorting in which households with higher skill levels (θ) have systematically stronger preferences for the “Elsewhere” location, independently of wage or rent differences. Formally, the conditional distribution G_θ(φ) of locational tastes given skill is weakly increasing in θ. This correlation breaks the Atkinson-Stiglitz sufficient condition for commodity tax superfluousness and generates unambiguously positive optimal transfers to Distressed.

Comparative advantage (spatial): A sorting mechanism in which higher-skill workers are disproportionately more productive in Elsewhere than in Distressed, captured by the wage elasticity with respect to skill being higher in Elsewhere (γ₀(θ) > γ₁(θ)). Households with skill above a threshold sort into Elsewhere even with homogeneous locational preferences. The existence of spatial comparative advantage means that migrants to Distressed earn less, creating a fiscal externality for place-based transfers.

Income-based sorting: Sorting of lower-income, lower-skill households into Distressed arising purely from the higher cost of living in Elsewhere, without any systematic skill-taste correlation or comparative advantage. Because high-skill households are less sensitive to rent differences, they sort into Elsewhere when rents there are higher. When this is the sole sorting mechanism and locational preferences are homogeneous, the Atkinson-Stiglitz commodity tax superfluousness conditions are satisfied and optimal place-based transfers are zero.

Fiscal externality (migration): The change in income tax revenue caused by migration responses to place-based policy changes, not by changes in incentives for stayers. When movers from Elsewhere to Distressed earn less in their new location, they generate lower tax payments, imposing a first-order cost on the government budget. This externality is measured by Δτ+(θ) in the optimal MTR formulas and equals the earnings-tax-revenue loss from movers across all skill levels above θ. This term is a “sufficient statistic” for the efficiency cost of place-based transfers in the sense of Chetty (2009).

Demogrant (∆₀): The difference in lump-sum transfers provided to zero-earners across the two locations (−T₀(0) − (−T₁(0)) = T₀(0) − T₁(0)). A positive ∆₀ means Distressed provides a larger transfer to non-earners. It represents the place-based redistribution that occurs at the bottom of the earnings distribution, independently of MTR differences. In the paper’s decomposition, total optimal place-based redistribution (∆_z) exceeds ∆₀ when Distressed also has lower MTRs, meaning redistribution grows with income.

Income-constant average tax difference (∆_z): The paper’s preferred summary measure of the average place-based transfer, defined as an equally weighted average of two tax-difference indices: the tax difference evaluated at Elsewhere earnings levels and the tax difference evaluated at Distressed earnings levels. This measure isolates tax schedule differences from productivity differences across locations, avoiding conflation of tax policy and wage effects on measured income.

Landlord welfare weight (λ_L): The social marginal welfare weight assigned to landlords relative to the multiplier on the government budget constraint. When λ_L < 1, the planner values a marginal dollar of public funds more than a marginal dollar to landlords, creating a motive to use place-based taxes to shift rent incidence. The rent redistribution effect on optimal MTRs operates through the term (λ_L − 1)Δr+(θ), which has opposite signs in urban (positive) and rural (negative) distressed areas because of their different housing supply elasticities.

Politics at Work

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

Layer 1 — Overview

Research Question

Do individual political views shape firm behavior and labor market outcomes in the private sector? Specifically, do business owners sort copartisan workers into their firms, and does employers’ political discrimination drive this sorting?

Data and Setting

The paper studies the complete Brazilian formal labor market over 2002–2019, assembling a novel longitudinal worker-firm-owner-party matched dataset from three administrative sources: (1) RAIS (Relação Anual de Informações Sociais), the universe of formal-sector workers (87 million unique workers, 7.6 million unique firms); (2) the Receita Federal do Brazil (RFB) and Cadastro Nacional de Empresas (CNE), containing business ownership structures for all registered firms; and (3) the Tribunal Superior Eleitoral (TSE) registry of all party members (19.3 million individuals) over 2002–2019. Matching these sources yields political affiliation for 11.4% of all private-sector owners and 7.8% of all private-sector workers in the sample. Party affiliation in Brazil requires an active registration step and is interpreted as a signal of strong and visible political views, distinguishing affiliated from unaffiliated individuals who likely hold milder views. The 35 parties in the sample are highly fragmented; the top 7 account for nearly 70% of all party members.

Main Findings

Political assortative matching. Using a likelihood ratio index (Eika et al., 2019; Chiappori et al., 2020), the paper finds that workers and owners belonging to the same party are on average about twice as likely to match in the labor market relative to random matching. Once within-municipality geographical sorting is accounted for, this figure falls to approximately 55% excess probability of copartisan matching, and increases over time: from 1.41 in 2002–2006 to 1.67 in 2016–2019. A dyadic regression approach — constructing all worker-firm dyads within industry-municipality labor markets and controlling for shared gender, race, age, and education — confirms the result: across all years, a politically affiliated worker is between 41% and 75% more likely to be employed by a copartisan owner than by an owner affiliated with a different party. Political assortative matching is driven both by higher hiring probabilities (range: 32%–59% more likely for copartisans, hiring margin only) and by longer tenure: copartisan workers stay in the firm roughly 5.5% longer than otherwise comparable workers of a different party, even within the same firm and hire-year (column 3 of Table 2). In every year and by every method, the degree of political assortative matching exceeds that of gender (15%–31% excess probability under dyadic approach) and race (approximately 3.4%), which are themselves both positive and significant.

Mechanisms: political discrimination. Three sets of evidence point to employer political discrimination as a relevant driver. First, in the administrative micro-data: assortative matching decreases strongly with firm size — it is more than twice as large in firms with up to 10 employees than in medium firms and more than six times as large as in firms with more than 50 employees — and is stronger for higher occupational layers and for jobs requiring above-median social skills or interpersonal relationships. Political assortative matching is, if anything, larger for parties not in power locally, inconsistent with a patronage mechanism. An event study of 5,262 owners who switched party finds a sharp increase of about 0.2 standard deviations in hires from the new party and a corresponding drop in hires from the old party at the time of the switch, with the share of workers from the new party rising by roughly 5 percentage points persistently. Second, an incentivized resume rating (IRR) field experiment (150 business owners; nondeceptive design) shows that owners rate copartisan resumes 0.213 points higher on a 1–7 Likert scale (a 7.4% increase relative to the mean rating for different-party resumes, statistically significant at p < 0.05), with no significant effect on perceived candidate acceptance probability. Third, a representative survey of 891 owners and 1,003 workers finds that belief-based and taste-based discrimination are ranked as the leading explanations by both groups; 47% of owners and 58% of workers agree with the belief-based discrimination statement. Additionally, 29% of surveyed owners (22% say “Yes” and 7% “In some cases”) explicitly reveal that political views affect their hiring decisions.

Real consequences. Conditional on employment, copartisan workers are promoted faster: they are 0.448 percentage points more likely to be promoted from white-collar to managerial positions (against a base rate of 2.58%) and 0.44 percentage points more likely to be promoted from blue-collar to white-collar positions (base rate 2.98%). Workers from a different party than the owner face a promotion penalty of 0.104–0.180 percentage points for white-collar-to-manager promotions. On wages, copartisan workers earn 3.9% more than unaffiliated coworkers within the same firm and year (firm-year FE specification); the effect is 2.8% when restricting to the same occupation within the firm. Workers from a different party earn 1.6% less. Decomposing by tier: managers (copartisan premium 1.6%), white-collar workers (3.4%), blue-collar workers (1.5%). Despite better outcomes, copartisan workers are 2.1 percentage points (2.3% relative to the mean) less likely to be educationally qualified for their occupation, conditional on firm-year and controlling for a full set of demographics. Finally, a higher share of copartisan workers in the prior year is associated with lower firm employment growth (estimated β = −0.071), corresponding to approximately a 1 percentage point gap in annual growth rate for a one-standard-deviation difference in copartisan share — substantial relative to an average annual growth rate of 10%.

Scope Conditions

All findings pertain to the formal private sector in Brazil over 2002–2019. Political affiliation in the Brazilian system requires an active step and signals strong views; results apply to the approximately 7.8%–11.4% of workers and owners who are party-registered. The field experiment sample is limited to 150 business owners affiliated with major Brazilian parties who were actively seeking to hire. The firm growth result is explicitly characterized as suggestive, without a source of exogenous variation.

In depth

Q1. What is the likelihood ratio index and what does it show for political matching in Brazil?

The likelihood ratio index measures how many times more likely a match between a worker and owner of the same party is, relative to the expected frequency under random matching (conditional on the population shares of each party). Across 2002–2019, the unconditional index ranges from 1.56 to 1.85, implying workers and employers of the same party are on average about twice as likely to match as under random matching. After accounting for geographic sorting within municipalities, the index ranges from approximately 1.41 (2002–2006 average) to 1.67 (2016–2019 average), showing a clear increasing trend. The corresponding gender and race indexes average about 1.2 and 1.35, respectively, in the basic specification, both significantly lower than the party index in every year of the sample.

Q2. How do the dyadic regression estimates control for omitted characteristics, and what do they find?

The dyadic regression constructs all possible worker-firm pairs within each municipality-industry labor market in a given year. The dependent variable is an indicator for whether worker i is employed by firm f. The key coefficient of interest is the differential probability of employment for a copartisan pair relative to a different-party pair, controlling for indicators for shared gender, race, age bracket, and education level, as well as worker occupation fixed effects and experience. This controls for the concern that politically affiliated individuals share non-political traits that correlate with employment choices. After these controls, a politically affiliated worker is 41%–75% more likely (depending on year) to be employed by a copartisan owner than by a different-party owner. The effect stems primarily from copartisan workers being preferentially hired (not just from unaffiliated owners preferring any affiliated worker indiscriminately). The analogous dyadic estimate for shared gender is 15%–31% and for shared race is approximately 3.4%, both lower than the party estimate in all years.

Q3. How is political assortative matching decomposed into hiring versus retention margins?

To isolate the hiring margin, the authors estimate the dyadic regression restricting to newly hired workers (not present in the firm in year t-1). They find that the probability of being hired by a copartisan owner is 32%–59% higher than by a different-party owner across years. The retention (tenure) margin is estimated by regressing the share of subsequent years a worker remains at the firm on partisan alignment at the time of hire. In the most stringent specification (year-of-hire × firm fixed effects), copartisan hires stay 5.5 percentage points longer (as a share of post-hire years) than different-party hires from the same firm and hire-year cohort. Both margins are significant, and both exhibit stronger political sorting than equivalent estimates for gender or race.

Q4. What is the evidence against political patronage as the primary driver of political assortative matching?

If political patronage (parties pressuring owners to hire copartisans) were the main driver, we would expect political assortative matching to be stronger when the owner’s party is in power locally, as those parties have greater leverage over business owners. The authors estimate a modified dyadic regression distinguishing between cases where the owner’s party is in the ruling coalition of the municipal mayor or state governor versus not in power. The results show that political assortative matching is, if anything, larger for parties not in power. This is inconsistent with patronage being the dominant mechanism and consistent with the discrimination channel being driven by owner preferences rather than external political pressure.

Q5. What does the event study of owner party changes show?

The event study tracks 5,262 owners who switch party affiliation during 2002–2019, comparing their firms to control firms in the same market whose owners remain affiliated to the original party. At the time of the switch, there is a sharp increase of approximately 0.2 standard deviations in hires from the owner’s new party and a corresponding sharp decrease in hires from the old party. Hires from other parties and unaffiliated hires also decline modestly. The share of the workforce affiliated with the new party increases by roughly 5 percentage points and remains elevated in subsequent years. Because nonpolitical network ties (shared school, neighborhood, sports team) are unlikely to dissolve abruptly when an owner changes party, this design provides additional evidence that the change in hiring is driven by a direct change in the owner’s political preferences rather than by network overlap.

Q6. What was the design of the incentivized resume rating experiment and why does it identify political discrimination?

The experiment was conducted with 150 Brazilian business owners recruited from the administrative data (who are already known to be affiliated with one of six major parties), targeting owners with active hiring interest through a leading job platform. Owners rated 20 synthetic resumes with fully randomized features (education, experience, training, skills, formatting). Sixteen resumes had no partisan cues; two contained cues signaling copartisanship with the rating owner; two signaled a party from the opposite side of the political spectrum. Incentives were provided by committing to send respondents real job-seeker profiles from the platform chosen by machine learning based on revealed preferences. Because all resume features other than the partisan cue were randomized, the experiment shuts down shared nonpolitical networks and patronage as explanations; the only channel is the employer’s direct preference for the candidate’s partisan affiliation. The response rate was 11% and the survey was conducted March–May 2022.

Q7. What is the quantitative magnitude of the field experiment result?

Owners rate copartisan resumes 0.213 points higher on the 1–7 Likert scale relative to resumes from the opposite side of the political spectrum (statistically significant at p < 0.05), representing a 7.4% increase relative to the mean rating of different-party resumes (2.950). When resume-level controls (gender, high-skill experience flag, years of experience, programming skills, training) are added, the estimate is 0.254. There is no statistically significant effect on owners’ perceived likelihood that a candidate would accept a job offer (coefficient 0.150–0.158, not significant), suggesting that the observed difference in interest ratings reflects a genuine direct preference for copartisans, not an expectation that copartisans are more likely to accept.

Q8. What do the survey findings add about mechanisms and the prevalence of political discrimination?

The survey of 891 owners and 1,003 workers (response rate 26.84%) presents five candidate mechanisms and asks respondents to evaluate each. Both groups rank belief-based discrimination (owners believe copartisans would be more productive) as the most likely explanation: 47% of owners and 58% of workers partially or strongly agree. Taste-based discrimination is second (36% owners, 52% workers agree), followed by networks (39% owners, 49% workers). Patronage and workers’ preferences attract little agreement from either group. Among owners ranked by single strongest agreement, 29.7% most strongly agree with belief-based discrimination and 22.0% with taste-based, while 29% of all surveyed owners explicitly stated that political views do affect their hiring decisions. These patterns are broadly similar regardless of the respondent’s own political affiliation status.

Q9. How large are the political promotion and wage premia, and how do they compare to gender and race effects?

For promotions, copartisan white-collar workers are 0.448 percentage points more likely to be promoted to manager (relative to unaffiliated co-workers hired in the same firm-year), against a base promotion rate of 2.58% — an effect of approximately 17% of the mean. For blue-collar-to-white-collar promotion, the copartisan premium is 0.44 percentage points against a base rate of 2.98%. For wages, copartisans earn 3.9% more than unaffiliated co-workers within the same firm and year; restricting to the same occupation within the firm, the premium is 2.8%. The political wage premium (3.9%) exceeds the gender wage premium (1.5%) and the race wage premium (1.0%) in the same specification. Workers from a different party than the owner earn 1.6% less than unaffiliated co-workers within the same firm-year.

Q10. Are copartisan workers better qualified than those they displace, and what does this imply for firm performance?

Copartisan workers are significantly less qualified in terms of education relative to their occupation: they are 2.1 percentage points less likely to be educationally qualified for their position than their unaffiliated co-workers within the same firm-year (2.3% relative to the mean qualification rate of 93.2%), with the largest effects for managers. Workers of a different party show only a small and economically negligible qualification gap. The fact that copartisans are paid more, promoted faster, and yet are less qualified is consistent with political discrimination substituting for competence in personnel decisions. The qualification shortfall is specifically attributed to copartisanship and not to shared gender, race, age, or education between owner and worker, as those coefficients are economically small.

Q11. What is the evidence on firm growth and what are the limitations of that evidence?

Firms with a higher share of copartisan workers in the prior year grow less. The estimated coefficient β = −0.071, and a one-standard-deviation difference in the copartisan share is associated with approximately a 1 percentage point gap in annual employment growth, relative to a mean growth rate of 10%. The specification compares firms of the same size and with the same number of affiliated workers in the same year. The result is robust to adding municipality and municipality-industry fixed effects. The authors explicitly characterize this evidence as suggestive, noting the absence of an exogenous source of variation in political discrimination. The negative association is more consistent with taste-based discrimination (Becker, 1957) — in which politically homogeneous firms sacrifice productivity for the owners’ amenity of employing copartisans — than with accurate belief-based discrimination.

Q12. How is political assortative matching distributed across parties and does it depend on party ideology?

The likelihood ratio index shows large assortative matching across the entire political spectrum. For most years, relatively more ideologically extreme parties — on the left (PT, PDT) and on the right (PP, DEM) — display higher assortative matching than more centrist parties (PMDB, PSDB). This pattern is consistent with stronger partisan identity at the extremes leading to stronger preferences for copartisan workers, but the paper does not formally model the mechanism behind this heterogeneity.

Q13. What is the role of workers’ preferences as opposed to employers’ discrimination, and how can wages distinguish them?

If workers have a preference for working with copartisan owners (treating this as a job amenity), compensating differentials theory would predict a negative wage premium for copartisan workers — they would accept lower wages in exchange for working with like-minded owners. The data show the opposite: copartisan workers earn significantly more, not less, than their unaffiliated co-workers. This evidence is inconsistent with workers’ preferences being the primary driver of political assortative matching, and is instead consistent with employers’ discrimination. The survey evidence corroborates this: both owners and workers assign low priority to the “workers’ preferences” mechanism.

Key Concepts

Political assortative matching: The phenomenon by which workers and business owners belonging to the same political party are matched in the labor market at rates significantly exceeding what would occur under random matching within the local labor market. Measured via the likelihood ratio index and dyadic regressions that control for shared demographic characteristics. In this paper, political assortative matching is larger in magnitude than assortative matching along gender or racial lines.

Likelihood ratio index (S): A measure of assortative matching defined as the weighted sum of the ratios of observed same-party co-occurrence probabilities to their expected probabilities under random matching. S > 1 indicates positive assortative matching. The paper uses both a basic version and a geography-adjusted version that computes the index within municipalities to control for geographic concentration of party membership.

Dyadic regression: A regression approach that constructs all possible worker-firm pairs within a defined labor market (municipality × 2-digit industry) to estimate the differential probability that a worker is employed by a copartisan firm relative to a different-party firm. The key advantage is the ability to control simultaneously for multiple shared demographic characteristics between worker and owner, accounting for the correlation of assortative criteria.

Incentivized resume rating (IRR) experiment: A nondeceptive field experiment design (following Kessler et al., 2019) in which business owners rate synthetic resumes with fully randomized characteristics. Truthful rating is incentivized because respondents are told that their revealed preferences will be used to select real job-seeker profiles sent to them by a partner platform via machine learning. This design allows direct identification of employer preference for copartisan candidates while ruling out alternative channels such as shared nonpolitical networks or patronage.

Political wage premium: The percentage wage difference earned by copartisan workers relative to unaffiliated co-workers within the same firm-year (and occupation), after controlling for a full set of socio-demographic characteristics. A positive political wage premium is the paper’s primary piece of evidence that workers’ compensating differentials cannot explain political assortative matching, since amenity-based sorting would predict a negative premium.

Political promotion premium: The differential probability that a copartisan worker is promoted to a higher organizational layer (blue-collar to white-collar, or white-collar to manager) relative to an unaffiliated co-worker hired in the same firm and year, net of demographic controls.

Educational mismatch (Qualified): An indicator variable equal to one if a worker’s educational level meets or exceeds the educational level required by their specific occupation in the CBO (Classificação Brasileira de Ocupações) classification. Used to assess whether politically favored (copartisan) workers are less competent along this observable dimension.

Belief-based discrimination vs. taste-based discrimination: Two distinct theoretical channels for employer political discrimination. Belief-based discrimination (Phelps, 1972; Arrow, 1973) occurs when employers perceive copartisans to be more productive — e.g., because shared political views reduce intra-firm conflict. Taste-based discrimination (Becker, 1971) occurs when employers have a direct utility-affecting preference for copartisan workers, independent of productivity beliefs. The paper treats these as observationally distinct from patronage and network overlap, and uses the negative correlation between political homogeneity and firm growth as suggestive evidence favoring the taste-based channel.

Production and Financial Networks in Interplay

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

This paper provides the first integrated empirical analysis of how bank credit supply shocks propagate through both the production network and the financial network simultaneously, using the universe of firm-to-firm VAT transactions and bank-firm credit register data for Spain during the 2008-09 global financial crisis. The theoretical framework, following Bigio and La’O (2016), links credit supply shocks to price distortions in the real economy and derives network-mediated propagation effects. The central empirical finding is that propagation through the production network triples the impact of direct bank credit shocks: a negative bank shock induces a 0.98 percentage point reduction in the directly affected firm’s purchases and sales growth, while first-order network effects add another 0.91 pp and higher-order network effects add 1.07 pp, for a combined indirect effect equal to twice the direct effect. Both upstream and downstream propagation are economically significant and of similar magnitude at the first-order level. Market concentration amplifies all propagation effects, and firms that are simultaneously central in both the production and financial networks generate disproportionately large aggregate contractions.

Summary of a published paper based on the CREI working paper full text, AI-assisted, pending human review. See the linked original for the authoritative claims and full conditions.

Layer 1: Overview

Huremovic, Jimenez, Moral-Benito, Peydro, and Vega-Redondo study how financial shocks originating in the banking sector propagate through interlinked production and financial networks, exploiting Spain’s administrative registers covering essentially the complete production and credit networks of the Spanish economy during the 2008-09 crisis. The Spanish data are unique: approximately 4.3 million VAT firm-to-firm transactions (above a €3,005 threshold) covering 245,000 firms, matched with 1.68 million bank-firm loans from 206 active banks. Bank credit supply shocks are identified using the Khwaja-Mian (2008) / Amiti-Weinstein (2018) approach — isolating bank-level credit supply variation by conditioning on firm-time fixed effects across firms with multiple bank relationships — and cross-validated using banks’ pre-crisis interbank market exposure. The paper’s main contribution is to show that treating production and financial networks separately understates the real effects of financial shocks by a factor of three: the combined direct and indirect (network-mediated) effects are three times the direct bank shock effect alone. First-order and higher-order downstream effects are both quantitatively significant, while upstream propagation is strong at first order but attenuates at higher orders.

In depth

Q1. How does the paper identify bank credit supply shocks, and what makes Spain’s administrative data unusual?

Bank credit supply shocks are identified using within-firm variation across bank relationships — the Khwaja-Mian/Amiti-Weinstein approach — which partials out all firm-level credit demand variation by including firm-time fixed effects, isolating the supply component of each bank’s credit change during the 2008-09 crisis. Spain is particularly suited for this analysis for two reasons. First, it is a bank-dominated economy with minimal shadow banking, so bank credit is the primary external financing channel and the credit register is comprehensive (capturing all loans above €6,000). Second, around 75% of credit comes from firms with at least two banking relationships, enabling the within-firm identification. A complementary shock measure based on banks’ pre-crisis reliance on interbank funding — a market sharply disrupted by the Lehman failure — yields similar results and does not require multi-bank relationships. Crucially, both shock measures show effects that are significant during the 2008-09 crisis but not in the pre-crisis year 2007, consistent with the shocks being crisis-specific supply disruptions rather than pre-existing trends.

Q2. What are the direct effects of bank credit supply shocks on firm-level real outcomes?

At the link (firm-to-firm) level, a direct negative bank credit supply shock to a supplier reduces the purchasing firm’s growth in purchases from that supplier by 3.7 percentage points (29% of the median purchase growth), while a shock to a customer reduces the supplier’s sales growth to that customer by 5.1 percentage points (37% of median sales growth). At the firm level, aggregating across all suppliers and customers, direct bank shocks reduce employment growth by 0.41 percentage points (41% of the median) and investment growth by 0.55 percentage points (9% of the median), consistent with the existing bank lending channel literature. Negative bank shocks also affect total credit availability at the firm level, including trade credit, indicating that the transmission operates through multiple channels and not only through the reduction in direct bank credit.

Q3. How large are the first-order and higher-order network propagation effects, and how do they compare to direct effects?

The first-order indirect effects — propagation from direct customers and suppliers — are of comparable magnitude to the direct bank shock effects: a negative bank shock to all direct suppliers generates a 2.3 pp reduction in firm purchases, while a shock to all direct customers generates a 1.9 pp reduction in sales, both comparable to the 0.98 pp direct effect on purchases and sales combined. Higher-order downstream effects (shocks to suppliers of suppliers) are also quantitatively important at approximately 2.0 pp, similar in magnitude to first-order downstream effects. In contrast, higher-order upstream propagation is weak — only first-order customer shocks matter for upstream transmission. This asymmetry is consistent with the theoretical model’s prediction that upstream propagation is non-linear in shock magnitude, attenuating more rapidly at higher orders than downstream propagation. In aggregate, the combined direct plus first-order plus higher-order effects triple the direct effect: the overall reduction in purchases and sales growth is approximately three times the direct bank shock effect alone.

Q4. What is the symmetric finding on upstream versus downstream propagation, and why does it matter?

Upstream and downstream propagation at the first-order level are of similar magnitude — a negative bank shock induces a 3.7 pp contraction in purchases (downstream, from the shocked supplier to the buying firm) and a 5.1 pp contraction in sales (upstream, from the shocked customer to the selling firm) — challenging the prior literature’s assumption that production network propagation is predominantly downstream. The comparable magnitudes of upstream and downstream propagation imply that financial shocks hitting customers matter for suppliers almost as much as financial shocks hitting suppliers matter for customers. The model provides the analytical basis for this result: downstream propagation is linear in shock magnitude (input supply contraction is passed through proportionally), while upstream propagation is non-linear (demand shortfalls at the customer do not fully translate into supply contraction from the supplier if the customer can be substituted). The near-symmetry at first order, however, means that both channels must be modeled for accurate aggregate impact assessment.

Q5. How does market concentration amplify financial shock propagation?

Firms operating in more concentrated markets — proxied by sectoral market concentration — experience stronger propagation both upstream and downstream; firm-to-firm propagation is also amplified when the two connected firms are mutual trading partners (both buyer and seller of each other), and for downstream propagation specifically when firms are geographically distant and share no common bank. The market concentration amplification is consistent with the theory: concentrated markets have fewer substitution possibilities for inputs and outputs, so firms cannot easily re-route around a shocked partner, forcing the shock to transmit more fully along the existing network link. The amplification from mutual trading ties reflects that the combined demand-and-supply shock through a reciprocal link creates compound effects. The attenuation of downstream propagation when firms share a common bank is consistent with the bank internalizing the financial interdependence of borrowers connected in a supply chain.

Q6. What is the contribution of combining production and financial network analysis jointly, beyond studying either separately?

The joint analysis reveals that the real effects of financial shocks are massively understated when production and financial networks are studied in isolation: the overall impact triples the direct bank shock effect, a result that only emerges when both network structures are mapped and their interaction is quantified. The paper also shows that aggregating to the firm level — rather than analyzing only link-level effects — is essential: firms minimize shocks from individual connections by adjusting across multiple suppliers or customers, so link-level estimates do not translate directly to firm-level outcomes. The joint network analysis further reveals a “dual centrality” amplification: firms that are central both in the production network (high customer-supplier centrality) and in the financial network (large credit relationships with strongly-shocked banks) generate disproportionately large aggregate output contractions. A standard deviation increase in a firm’s customer centrality is associated with a 3 pp decrease in its purchase growth, while the same increase in supplier centrality is associated with a 0.6 pp decrease in sales growth.

Key Concepts

upstream propagation : the transmission of a bank credit supply shock from a directly shocked customer to that customer’s suppliers, operating through the demand channel — a customer facing tighter credit reduces its purchases, contracting the supplier’s sales; the paper shows first-order upstream effects (5.1 pp reduction in sales growth) are of similar magnitude to first-order downstream effects.

downstream propagation : the transmission of a bank credit supply shock from a directly shocked supplier to that supplier’s customers, operating through the supply channel — a supplier facing tighter credit reduces its output, contracting the availability of inputs to customers; both first-order (2.3 pp) and higher-order (2.0 pp) downstream effects are quantitatively large.

dual centrality amplification : the finding that firms simultaneously central in the production network (many supplier-customer relationships) and in the financial network (large credit from banks that receive large supply shocks) generate disproportionately large aggregate output contractions when hit by financial shocks, because the shock propagates through both network channels simultaneously.

Khwaja-Mian identification : the strategy of isolating bank credit supply shocks by exploiting within-firm variation across banks — conditional on firm-time fixed effects, changes in credit from different banks to the same firm reflect supply rather than demand — originally proposed by Khwaja and Mian (2008) and extended by Amiti and Weinstein (2018).

credit network shock : a bank-level credit supply shock derived from the Khwaja-Mian/Amiti-Weinstein methodology, capturing the component of each bank’s credit contraction attributable to bank-level supply factors rather than firm-level demand; the paper uses both this measure and an interbank-market-exposure measure to cross-validate identification.

Professional Motivations in the Public Sector: Evidence from Police Officers

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

This paper studies how public sector workers balance professional motivations against private economic concerns, using arrest decisions by Dallas Police Department (DPD) officers as the empirical laboratory. The central institutional feature exploited is that arrests made near the end of an officer’s shift typically require the officer to stay and work overtime, generating private costs that must be weighed against the professional benefits of making an arrest (e.g., crime reduction or duty fulfillment). The paper further leverages variation from DPD’s “secondary employment” program: approximately 30% of officers held a registered second job at some point during 2019–2021, and on days when a second job is scheduled after the police shift, the opportunity cost of late-shift policing is higher.

The data cover all DPD arrests from January 2015 to December 2021, linked to officer shift assignments, charge types, prosecutorial outcomes (whether the Dallas County Attorney chose to prosecute), and second-job schedules. The sample excludes traffic violations and arrests without shift information. The authors observe wide variation in prosecution rates by charge type: drug and gang offenses exceed 70%, property and violent crimes run 30–50%, and minor charges fall below 20%.

Four main findings emerge. First, arrest rates fall sharply in the last 30–40 minutes of a shift, with the decline most pronounced for drug and gang charges (approximately 50% drop in arrest rate) and smallest for violent charges, consistent with officers having more discretion over the former. Second, arrests that do occur late in the shift are of higher quality: conditional on being made, they are approximately 1.5–2.5 percentage points more likely to result in prosecution than arrests made earlier, with the quality premium larger in more discretionary charge categories (drugs/gang > property > violent). Third, on days when an officer has a second job scheduled, arrest rates are lower by roughly 5–10% relative to baseline across the full shift, with effects concentrated in the second half; and the conditional probability of prosecution on those days is 1–2 percentage points higher than on non-second-job days. The second-job effect appears even earlier in the shift than the overtime effect alone, consistent with the second job magnifying the opportunity cost mechanism.

Fourth, the authors estimate a dynamic structural model of the arrest decision. At each moment of the shift the officer chooses whether to arrest, trading off a professional benefit b_p against a private cost c(t, secondjob) that rises when overtime begins and rises further on second-job days. Structural estimates indicate the overtime cost is large enough to reduce the expected professional value of an arrest in the final 30 minutes of the shift by roughly 20–30%. The additional second-job cost reduces expected professional value by a further 10–20%. Counterfactual simulation implies that eliminating the overtime cost would increase overall arrests by approximately 5–8%, a magnitude the authors describe as economically significant. Welfare analysis shows that the desirability of high overtime costs depends on whether citizens weight quantity of arrests or quality: under quality-weighted preferences the current overtime-cost regime may be socially optimal because officers self-select toward arrests they perceive as likely to result in prosecution; under quantity preferences, reducing overtime costs would increase police activity.

The identification strategy relies on within-officer variation in second-job scheduling, absorbing officer fixed effects (and officer-by-month fixed effects in robustness checks) and time fixed effects. The key identifying assumption is that second-job days are not systematically assigned to low-crime or low-patrol days. Supporting evidence includes balance tests showing second-job status is uncorrelated with local crime call patterns conditional on fixed effects, and the observation that officers who take second jobs do not exhibit a systematically different enforcement style (measured by arrest patterns across the shift) relative to officers who do not.

Scope conditions: results are from a single medium-sized urban police department (approximately 3,000 officers) in Dallas, Texas, a city described as diverse by race, income, and political affiliation. The department is 29% Black, 43% Hispanic, 27% White, and 15% female. Generalizability to other jurisdictions or institutional structures is not established by this study.

Q: What is the main research question? A: The paper asks how public sector workers balance professional motivations (e.g., crime reduction, duty fulfillment) against private economic concerns (e.g., overtime costs, opportunity costs from second jobs). It uses police arrest decisions as the empirical setting because the shift-end timing of arrests generates a clear, observable private cost that varies within officer across days.

Q: What is the key institutional feature that generates identification? A: Arrests made near the end of a shift typically require the arresting officer to stay past the shift and work overtime. This creates a personal cost — more time, delayed transition to off-duty activities — that makes late-shift arrests more costly without changing their professional value. The DPD secondary employment program adds a second source of variation: on days when an officer has a registered second job scheduled after the police shift, the opportunity cost of any arrest (and especially a late-shift arrest) is higher.

Q: How large is the drop in arrest rates near shift end? A: The baseline arrest rate declines by approximately 0.12 percentage points per six-minute time bucket in the last 30 minutes of the shift, or about 5% relative to the mean arrest rate of 2.3 percentage points. The drop is most dramatic for drug and gang charges, where the arrest rate falls by approximately 50%, and smallest for violent charges, where officers appear to arrest regardless of shift timing.

Q: How does arrest quality change near shift end? A: Arrests made in the last 30 minutes of a shift are approximately 1.5–2.5 percentage points more likely to result in prosecution than arrests made earlier in the shift, after controlling for charge type composition and officer fixed effects. The quality premium is larger in more discretionary charge categories (drugs/gang, then property, then violent), consistent with officers becoming more selective to avoid overtime costs on arrests unlikely to result in prosecution.

Q: Does the shift-end drop reflect officer fatigue or overtime cost? A: The paper argues both pieces of evidence point to overtime cost rather than fatigue alone. First, arrest rates increase sharply after the official shift end when the officer is already earning overtime pay — if fatigue were the mechanism, arrests would also decline post-shift. Second, on second-job days arrest rates fall earlier in the shift and by more, consistent with higher opportunity costs rather than accumulated fatigue.

Q: What is the effect of having a second job scheduled on arrest rates? A: Having a second job scheduled reduces arrest rates by roughly 5–10% relative to the baseline across the full shift, with effects concentrated in the second half. The reduction is even larger in the final 30 minutes, consistent with the second job amplifying the overtime cost mechanism.

Q: What is the effect of second-job days on arrest quality? A: Arrests made on second-job days are 1–2 percentage points more likely to result in prosecution compared to arrests on non-second-job days, after controlling for time of day, charge type composition, and officer fixed effects. This parallels the shift-end quality effect and is consistent with officers applying higher selectivity thresholds when opportunity costs are elevated.

Q: How is the second-job variation used for identification? A: The main specification compares the same officer’s behavior on shifts where a second job is scheduled versus shifts where it is not, absorbing officer fixed effects and time fixed effects. The identifying assumption is that second-job scheduling is uncorrelated with unobservable determinants of enforcement intensity conditional on fixed effects. The authors support this with balance tests showing second-job status is not predicted by lagged activity measures or contemporaneous crime call patterns.

Q: What does the dynamic structural model add? A: The structural model formalizes the arrest decision as a dynamic problem where the officer compares the professional benefit b_p of an arrest to the private cost c(t, secondjob), which rises discontinuously when overtime begins and rises further on second-job days. Estimating the model by matching moments (baseline arrest rates, shift-timing patterns, quality changes, second-job effects) yields preference parameters. The model enables counterfactual and welfare analysis that the reduced-form estimates alone cannot provide.

Q: What are the structural estimates of overtime and second-job costs? A: The overtime cost c_ot is estimated to be large enough that arresting someone in the final 30 minutes of the shift reduces the expected professional value of that arrest by roughly 20–30%. The additional second-job cost c_sj reduces expected professional value by a further 10–20%. Both estimates are described as statistically precise.

Q: What does the counterfactual removal of overtime costs imply for arrests? A: Eliminating the overtime cost is estimated to increase overall arrests by approximately 5–8%, which the authors characterize as economically significant. This implies that officers’ private costs have a first-order impact on the quantity of law enforcement activity.

Q: What does the welfare analysis conclude about overtime costs? A: The welfare effect of eliminating overtime costs depends on citizen preferences. Under quality-weighted preferences — where citizens value the probability that an arrest results in prosecution — the current overtime-cost regime may be socially optimal because it induces officers to self-select toward arrests they perceive as likely to stick. Under quantity preferences — where citizens value the total number of arrests per period — reducing overtime costs would increase police activity and benefit citizens.

Q: What are the scope conditions of the study? A: The study is conducted entirely within the Dallas Police Department, a single medium-sized urban department with approximately 3,000 officers. Dallas is described as a diverse city by race, income, and political affiliation, and the department itself is relatively diverse (29% Black, 43% Hispanic, 27% White, 15% female). The findings may not generalize to departments with different overtime rules, labor contracts, or institutional cultures.

professional motivations: The non-pecuniary benefits officers derive from making arrests, such as crime reduction, duty fulfillment, or the legitimacy of their work; modeled as a professional benefit b_p that motivates arrest independent of financial compensation.

private costs of arrest: The personal costs borne by officers when making an arrest, chiefly the overtime cost when an arrest extends the shift past its scheduled end, and the opportunity cost on days when a second job is scheduled. These costs are distinct from professional motivations and respond to economic incentives.

arrest quality: The conditional probability that an arrest results in prosecution by the Dallas County Attorney’s office; used as a revealed-preference measure of the officer’s assessment of arrest strength. Higher arrest quality near shift end reflects greater selectivity under elevated private costs.

secondary employment (second job): A formal DPD program allowing officers to register as certified police officers for private security work after their primary shift. Approximately 30% of DPD officers held a second job at some point during 2019–2021. The scheduled second job raises the opportunity cost of late-shift primary-shift arrests and provides a second source of variation in private costs.

overtime cost: The cost incurred when an arrest requires an officer to remain past the end of the scheduled shift to complete paperwork and processing. Modeled as c_ot per period spent in overtime, this cost is the primary mechanism reducing late-shift arrest rates and increasing arrest selectivity.

dynamic model of arrest decisions: A structural model in which officers decide each moment whether to arrest, balancing professional benefit against private cost as a function of shift timing and second-job status. Estimated by minimum distance on moments from the data; used to recover preference parameters and conduct counterfactual welfare analysis.

Quality Adjustment at Scale: Hedonic versus Exact Demand-Based Price Indices

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

Layer 1: Overview

This paper implements and evaluates methods for constructing quality-adjusted price indices from item-level retail scanner data at scale — across hundreds of product categories, heterogeneously encoded product attributes, and rapid product turnover. Using proprietary NPD Group data covering five general merchandise categories (2014–2018) and NielsenIQ scanner data covering 50+ food product groups (2006–2015), the paper compares hedonic superlative indices (using the Erickson-Pakes EP-TV methodology and a novel machine-learning extension) against exact demand-based indices (the Feenstra 1994 lambda-ratio adjustment and the Redding-Weinstein 2020 CES Unified Price Index, CUPI). The central finding is that quality adjustment is quantitatively large: the hedonic Tornqvist index shows roughly 2.5–2.9 percentage points per year faster price decline than the matched-model Tornqvist in high-tech categories (headphones, memory cards) and 4–5 percentage points of cumulative additional disinflation relative to matched-model indices for food. The Feenstra index agrees closely in magnitude with the hedonic approach, but the CUPI is highly sensitive to the choice of common-goods rule (CGR) and in some specifications shows 20–40 percentage points more cumulative disinflation than the Feenstra, a gap the paper attributes to the CUPI’s extreme sensitivity to low-share goods. The paper establishes that hedonic superlative price indices are feasible to implement at scale, including with machine learning on sparse text descriptions, and recommends them as the practical benchmark for re-engineering official price statistics.

Summary of a published paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What problem in price index construction does the paper address?

The paper addresses the long-standing challenge of simultaneously accounting for consumer substitution and quality change due to product entry and exit in official price statistics, and shows these two corrections are now feasible to implement in real time from item-level retail transactions data. Standard official statistics (CPI, PCE) use an arithmetic Laspeyres index that holds spending weights fixed — the Boskin Commission documented this overstates the true cost of living due to substitution bias. Scanner data permit superlative indices (Tornqvist, Fisher) that correct for substitution at the item level, but further correcting for quality change requires dealing with the millions of products that enter and exit the market each quarter. The paper’s contribution is to show that both corrections can be combined at scale.

Q2. What data infrastructure does the paper use, and what does it reveal about product turnover?

The NPD Group data cover five product groups with quarterly turnover rates of 4.5–13.5 percent per quarter (both entry and exit), and exhibit a characteristic life-cycle pattern: prices peak at entry and decline steadily thereafter while market shares follow a hump shape — rising as products gain distribution and then declining as newer products displace them. Memory cards, for example, show approximately a 50 percent price decline over their life cycle and a 200 percent increase in market share in the first year after entry. These interrelated price-quantity dynamics mean that any matched-model index that ignores entering and exiting goods misses substantial quality improvement. The NielsenIQ data cover over 2.6 million UPCs across 40,000 stores, with nominal food sales closely tracking BEA PCE food expenditures, validating its representativeness.

Q3. What is the EP-TV hedonic method and why does the paper prefer it?

The Erickson-Pakes time-varying unobservables (EP-TV) method estimates hedonic price indices from item-level transactions data using a two-step procedure: first predict log price levels from observable characteristics to recover item-level residuals, then predict log price changes from characteristics plus the lagged residual, which allows the model to track changing valuations of unobservable attributes over time. This approach outperforms the simpler log-level hedonic and the EP-F (fixed unobservables) approach in model fit for price changes: EP-TV achieves R² of 0.13–0.50 versus 0.05–0.24 for log-level models across product groups. The paper extends EP-TV to the NielsenIQ data using deep neural networks to decode sparse abbreviated product descriptions (e.g., “ZR DT LN/LM CF NBP CT” for a diet soft drink), achieving out-of-sample R² of roughly 75% for price-level predictions and above 50% in-sample for price changes.

Q4. What are the main quantitative findings for the hedonic indices?

The EP-TV hedonic Tornqvist index indicates price declines approximately 2.9 percentage points per year faster than the matched-model Tornqvist for memory cards, 2.5 pp/year for headphones, 1.3 pp/year for boys’ jeans, 0.7 pp/year for coffee makers, and 0.4 pp/year for occupational footwear; for NielsenIQ food categories, the hedonic Tornqvist is approximately 4 percentage points lower cumulatively over 2006–2015 than the matched-model Tornqvist. These gaps represent the quality improvement embedded in product turnover — the fact that new memory cards at a given price embody more storage than their predecessors, new headphones better sound quality, etc. The paper also shows that the hedonic Laspeyres, which only adjusts for exiting goods (following the standard Pakes 2003 bounding result), is substantially lower than the matched-model Laspeyres, confirming that the selection bias from ignoring exiting goods in official statistics is quantitatively important.

Q5. How do the demand-based exact price indices compare with the hedonic approach?

The Feenstra (1994) lambda-ratio index, which adjusts the Sato-Vartia index for product entry and exit via the ratio of entering to exiting expenditure shares scaled by (1/(σ−1)), shows cumulative disinflation approximately 2 percentage points beyond the matched-model Sato-Vartia across all five NPD product groups and approximately 5 percentage points for NielsenIQ food, broadly comparable in magnitude to the hedonic adjustment. The estimated substitution elasticities (σ) range from about 5.2 to 7.8 across NPD product groups and have a median of about 6 across food product groups, consistent with the literature. The Feenstra-hedonic agreement is a reassuring finding: two methodologically distinct approaches based on different identifying assumptions yield similar magnitudes of quality correction.

Q6. What is the CUPI and why is it problematic?

The Redding-Weinstein (2020) CES Unified Price Index (CUPI) generalizes the Feenstra index by adding a taste-shock correction (S ratio) and a Jevons index (P ratio), both of which are unweighted geometric means across common goods — making the CUPI extremely sensitive to products with tiny expenditure shares, because any product with a low share is inferred to have low appeal, which the model translates into a large quality-adjustment downward.** Without a common-goods rule (CGR), the CUPI shows 30–40 percent per year price declines for high-tech goods and boys’ jeans, 10–30 percentage points below the Feenstra; with a 25th-percentile market-share CGR, the CUPI is still more than 40 percentage points below the Feenstra for food in 2015 on a cumulative basis. The key concern is that very low expenditure shares for entering or exiting products can reflect search frictions, limited distribution, or clearance-rack effects rather than genuinely low consumer appeal, so the CUPI’s unweighted components may conflate these factors with quality change. The paper concludes that more research on the appropriate CGR is needed before the CUPI can be recommended for official statistics.

Q7. Is the hedonic approach robust to missing or omitted product attributes?

Yes — omitting key observable characteristics (memory size for memory cards, major brand dummies for apparel and footwear) from the EP-TV estimation has only minimal effect on the resulting hedonic price index, in contrast to log-level hedonic models where such omissions produce much larger distortions. For memory cards, the baseline EP-TV Tornqvist index produces an average annual cumulative chained price change of −20.12%; excluding entering products whose size or speed is outside the range of continuing products changes this to −20.09%, even though roughly 50% of entering products (accounting for 25% of entering-product sales) are excluded. This robustness reflects the EP-TV design: the first-stage residual absorbs time-varying unobservable characteristics that would otherwise confound the hedonic mapping.

Q8. What are the implications for official statistics?

The paper argues that adopting hedonic superlative price indices from real-time scanner data would produce official CPI and PCE price measures that simultaneously correct for substitution bias and quality change, resulting in meaningfully lower measured inflation in categories with high product turnover — likely understating quality-adjusted price declines in current official statistics by several percentage points per year in high-tech consumer goods and by roughly half a percentage point per year in food. The practical case for adoption is that the EP-TV approach can be implemented across heterogeneously encoded data (both structured NPD attributes and unstructured NielsenIQ text), is feasible in real time with transaction data, is relatively insensitive to chain drift (full-imputation hedonic indices avoid the transitory price volatility that contaminates matched-model chained indices), and satisfies bounding properties under general conditions established by Pakes (2003). The paper thus operationalizes long-standing recommendations of the Boskin Commission (1998) that called for exactly these corrections.

Key Concepts

EP-TV hedonic index : the Erickson-Pakes time-varying unobservables hedonic price index, which imputes quality-adjusted price changes for entering and exiting products using a two-step regression that includes lagged residuals from a log-level hedonic to control for products whose unobservable attributes change their market valuations over time; the paper’s preferred hedonic approach.

Feenstra (1994) lambda-ratio adjustment : a correction to the Sato-Vartia CES price index that accounts for product entry and exit by multiplying by (λ_{t,t-1}/λ_{t-1,t})^{1/(σ-1)}, where the lambda terms are the expenditure shares of continuing goods relative to all goods in each period; larger entry shares relative to exit shares produce a downward adjustment reflecting quality improvement from new products.

CES Unified Price Index (CUPI) : the Redding-Weinstein (2020) extension of the Feenstra index that additionally incorporates time-varying product appeal shocks via an unweighted Jevons index (P* ratio) and an unweighted expenditure-share ratio (S* ratio); the paper finds this index is highly sensitive to the common-goods rule and may overstate quality adjustment in practice due to sensitivity to low-share goods.

common-goods rule (CGR) : a threshold rule that restricts the set of goods entering the CUPI’s unweighted components to those with sufficiently large or long-duration market shares, introduced by Redding and Weinstein (2020) to limit the influence of fringe products; the paper finds CUPI results are sensitive to the CGR specification in a way that varies across product groups.

full-imputation hedonic index : a hedonic price index that uses the hedonic mapping to impute price changes for all goods (including continuing goods), rather than only entering and exiting goods; reduces chain drift relative to partial-imputation approaches because imputed prices are less volatile than observed prices.

product turnover : the quarterly entry and exit of products from the market, ranging from 4.5% to 13.5% per quarter in NPD data; the primary mechanism through which quality change is embedded in item-level scanner data and the main source of mismeasurement in matched-model price indices.

Racial Disparities in Housing Returns

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

Layer 1 — Overview

Research Question

This paper estimates the racial/ethnic gap in realized housing returns using administrative data on individual housing transactions, and investigates the mechanisms that generate those gaps. The central question is: why do Black and Hispanic homeowners accumulate less housing wealth than White homeowners, even as minority homeownership rates have risen substantially over the last century?

Data and Methodology

The authors merge three primary data sources. First, a nationwide panel of residential property records from ATTOM covering 146.8 million arm’s-length home purchases from 1990 to 2020, which records transaction prices, mortgage characteristics, and property-level identifiers. Second, Home Mortgage Disclosure Act (HMDA) records, which contain self-reported race and ethnicity for mortgage applicants. Third, supplementary administrative sources including McDash mortgage servicing records, Equifax credit bureau data, Fannie Mae/Freddie Mac/ABSNet modification records, and the Survey of Income and Program Participation (SIPP). After applying sample restrictions — including requiring an observed purchase price, a linked HMDA record, an arm’s-length repeat sale, a combined loan-to-value ratio of at most 102.5%, and an ownership spell of at least 12 months — the baseline analysis sample comprises 13.6 million ownership spells for Black, Hispanic, and White homeowners who purchased homes with a mortgage between 1990 and 2016 in 40 states. Ownership spells unsold by March 2020 have their value imputed using the FHFA county-level house price index, a procedure that is conservative in that it understates racial gaps.

The authors construct two complementary return measures. The unlevered return compares the annualized ratio of sale price to purchase price. The levered return (internal rate of return) sets the net present value of all homeowner cash flows — down payment, monthly mortgage payments, implicit rent, maintenance, taxes, insurance, transaction costs, and limited liability in foreclosure — equal to zero.

Main Findings

Among mortgaged home purchases, mean annual unlevered returns are 0.5% for Black homeowners, 0.6% for Hispanic homeowners, and 2.8% for White homeowners, implying Black-White and Hispanic-White gaps of approximately 2.3 percentage points per year. Mean annual levered returns are 1.6%, −3.0%, and 6.6% for Black, Hispanic, and White homeowners respectively, yielding gaps of 5.0 and 9.6 percentage points. After adjusting for the approximately one-fourth of purchases made in cash (for which no racial gap is found), preferred estimates of the unlevered gap are 1.9 (Black-White) and 1.4 (Hispanic-White) percentage points.

Distressed sales — foreclosures and short sales — statistically account for the entire gap in returns. Within non-distressed sales, the Black-White gap in annual unlevered returns falls to less than 40 basis points, and the Hispanic-White gap reverses sign. Two distinct factors drive the role of distressed sales: (1) Black and Hispanic homeowners are approximately twice as likely as White homeowners to experience a distressed sale, and (2) minority homeowners live in neighborhoods where distressed sale price discounts are larger — estimated at 39%–40% for Black and Hispanic homeowners versus 28% for White homeowners. A Blinder-Oaxaca decomposition indicates that equalizing distressed sale rates (holding the distressed sale penalty fixed) would eliminate 84.6% of the Black-White unlevered returns gap and 133.6% of the Hispanic-White gap, confirming that the frequency margin dominates the severity margin.

A counterfactual wealth-accumulation exercise using PSID data shows that equalizing housing returns reduces the Black-White gap in housing wealth at retirement by 37%. Equalizing first-time purchase rates reduces the gap by only 1%, illustrating that promoting homeownership without addressing the returns gap is largely ineffective. Equalizing both returns and purchase rates reduces the gap by 49%.

Mechanisms

Approximately one-third of the gap in unlevered returns can be explained by purchase year and county fixed effects, with much of this timing effect attributable to the Great Recession. Controlling additionally for income, family structure, gender, and leverage reduces the gap by a further ~0.3 percentage points, leaving a substantial residual. About half of the racial gap in mortgage default can be attributed to observable credit risk (family structure, income, leverage, credit score). The remainder is associated with unobservable liquidity shortfalls and income instability: median liquid wealth among Black and Hispanic homeowners is $2,400 and $5,400 respectively, and minority homeowners are 2–4 percentage points more likely to transition to unemployment conditional on pre-unemployment income. Using quasi-experimental variation from adjustable-rate mortgage resets, the paper shows that in response to a 10% increase in monthly payments, White homeowners increase 90-day mortgage default by 3.0 percentage points after 12 months, while Black and Hispanic homeowners show increases of 4.5 and 7.1 percentage points respectively — excess sensitivity that is not captured by credit scores. The early-2000s credit supply expansion through private securitization and portfolio lending channels (as distinct from GSE/FHA) contributed to 61.5% of the 6.2-percentage-point increase in the Black-White distressed-sale gap between the 2002 and 2006 purchase cohorts, and 52.0% of the 12.2-percentage-point increase in the Hispanic-White gap. Evidence from the National Survey of Mortgage Originations suggests that Black homeowners hold overoptimistic expectations about future house price growth and income growth relative to their realized outcomes, which may explain why high-risk minority households do not self-select out of homeownership.

Scope Conditions

Results pertain to mortgaged home purchases (approximately three-fourths of all purchases) by Black, Hispanic, and White homeowners in 40 states (non-disclosure states excluded), with primary coverage from 2000 to 2016. No racial gap in returns is found for cash purchases. The racial gap in non-distressed returns is small and not economically meaningful, so the findings specifically pertain to the realized-return distribution that includes the distressed-sale tail.

In depth

Q1. How large is the racial gap in housing returns, and how does it compare to previously documented racial disparities in housing costs?

A: Among mortgaged purchases, Black and Hispanic homeowners each realize annual unlevered returns approximately 2.3 percentage points lower than White homeowners; levered return gaps are 5.0 percentage points (Black-White) and 9.6 percentage points (Hispanic-White). In dollar terms, this translates to a difference of roughly $5,920 per year for the average Black homeowner and $6,762 per year for the average Hispanic homeowner on a ten-year holding horizon. These gaps are an order of magnitude larger than previously documented racial disparities in housing costs, such as post-origination interest rate disparities of about 40 basis points (~$500 annually for a $200,000 home) or inflated property tax assessments amounting to $300–$390 per year.

Q2. What is the role of distressed sales in explaining racial gaps in returns, and how do frequency versus severity contribute?

A: Distressed sales statistically account for nearly the entire racial gap in realized housing returns. Within non-distressed sales, the Black-White unlevered gap falls to less than 40 basis points and the Hispanic-White gap inverts. Two channels operate: (1) Black and Hispanic homeowners are approximately twice as likely as White homeowners to experience a distressed sale; and (2) within distressed sales, minority homeowners realize lower returns because they tend to live in neighborhoods with larger distressed-sale price discounts (estimated at 39–40% below imputed market value for Black and Hispanic homeowners, vs. 28% for White homeowners). A Blinder-Oaxaca decomposition indicates that equalizing distressed sale frequency (holding severity fixed) would close 84.6% of the Black-White gap and 133.6% of the Hispanic-White gap, so the frequency margin is quantitatively dominant.

Q3. Are racial differences in house price appreciation responsible for the gap in non-distressed returns?

A: No. Among non-distressed sales, realized returns closely track county-level FHFA house price index growth for Black, Hispanic, and White homeowners alike, essentially one-for-one regardless of race. There is no economically meaningful racial gap in house price appreciation conditional on avoiding a distressed sale. This finding implies that the gap in average realized returns is not generated by differential neighborhood-level appreciation but rather by the incidence of distressed sales and the price penalties they entail.

Q4. How much of the racial gap in housing returns can be explained by observable homeowner characteristics such as income, family structure, and leverage?

A: Controlling for county and purchase year fixed effects reduces the raw Black-White and Hispanic-White unlevered returns gaps from 2.3 to 1.5 and 1.6 percentage points, respectively. Additionally controlling for income, family structure (gender and co-applicant status), and leverage reduces the gap by a further ~0.3 percentage points. Even among the ostensibly safest group — high-income couples with low leverage — the Black-White (Hispanic-White) gap in unlevered returns is 0.7 (0.5) percentage points. Among high-leverage, low-income, single-male homeowners the gap is 1.8 (1.7) percentage points. Gaps exist within every demographic subgroup, and neighborhoods (Census tract fixed effects) explain roughly half of the remaining gap for Black homeowners and one-third for Hispanic homeowners, but substantial residual gaps persist even within neighborhood.

Q5. What observable credit risk characteristics explain racial differences in mortgage default?

A: Raw racial gaps in 90-day mortgage delinquency are 2.6 percentage points (Black-White) and 1.8 percentage points (Hispanic-White). Controlling for purchase year and county reduces these to 2.2 and 1.6 percentage points respectively. Controlling for family structure, income, leverage, and credit score reduces the gaps to 0.98 and 0.94 percentage points — implying that observable characteristics explain approximately 55% and 41% of the Black-White and Hispanic-White default gaps respectively. Credit scores contribute the most explanatory power among these controls, while mortgage contract characteristics (a test of differential lender treatment) contribute negligibly.

Q6. What is the evidence that liquidity and income instability — factors not observable to lenders — explain the residual racial gap in default?

A: Survey data from SIPP reveal that median liquid wealth (bank accounts, stocks, bonds) for Black and Hispanic homeowners is only $2,400 and $5,400 respectively, while minority homeowners are 2–4 percentage points more likely to transition to unemployment conditional on pre-unemployment income. In SIPP mortgage delinquency regressions, controlling for liquidity, job loss in the prior year, and income reduces the Black-White coefficient by about 30% and the Hispanic-White coefficient by about 41% (and 29% and 70% respectively when also controlling for income level, current loan-to-value, and family composition). In administrative data using ARM payment resets as liquidity shocks, a 10% increase in monthly payments raises 90-day default by 3.0 percentage points for White homeowners, 4.5 percentage points for Black homeowners, and 7.1 percentage points for Hispanic homeowners after 12 months. This excess sensitivity is not substantially reduced by controlling for credit scores, income, or leverage — indicating that the liquidity risk of minority homeowners is largely unobservable to lenders at origination.

Q7. Is there evidence that strategic default explains higher minority distress rates?

A: No meaningful evidence supports strategic default as a driver of excess minority distress. Using quasi-experimental variation in ex-post leverage from diverging option ARM indices (following Gupta and Hansman 2022), the paper finds large causal impacts of leverage on default but no evidence that these impacts are larger for minority homeowners. Separate survey evidence from the NSMO shows a statistically insignificant Black-White difference of 0.05 percentage points (s.e. 0.65) in agreement that “it is okay to default if it is in the borrower’s financial interest” (relative to a White mean of 6.1%). The absence of larger leverage-driven default responses combined with the presence of larger payment-shock-driven responses points specifically to liquidity — not strategic behavior — as the relevant mechanism.

Q8. What is the evidence for information frictions contributing to excess minority homeownership risk?

A: Black homeowners in the NSMO report future house price expectations that are 0.07 standard deviations more optimistic than White homeowners, conditional on past price experiences, yet realized house price growth in the subsequent two years is actually 1.1 percentage points lower for Black homeowners. Although Black homeowners are 2.8 percentage points more likely to report past personal financial crises, their stated expectations about future financial crises are similar to those of White homeowners — despite 90-day default rates that are 2.5 percentage points higher in the first two years post-origination. Black homeowners also report income growth expectations 0.3 standard deviations higher than White homeowners, while SIPP and CPS data show minorities are more likely to experience income losses. These patterns of overoptimistic expectations relative to realized outcomes are consistent with information frictions causing high-risk minority households to suboptimally select into homeownership.

Q9. How much of the racial gap in distress can be attributed to the early-2000s credit supply expansion?

A: The paper identifies the expansion as concentrated in portfolio loans and privately securitized mortgages, which are distinct from GSE/FHA mortgages that did not exhibit a comparable supply increase. Between the 2002 and 2006 purchase cohorts, the Black-White gap in distressed sales rose by 6.2 percentage points overall but only 2.4 percentage points among GSE/FHA loans. A decomposition using this contrast attributes 61.5% of the overall 6.2-percentage-point increase to the credit supply expansion. Analogously, 52.0% of the 12.2-percentage-point increase in the Hispanic-White gap between 2002 and 2006 is attributed to credit supply. Within-race decompositions find that credit supply accounts for 42%, 30%, and 35% of the increase in distress relative to 2002 for Black, Hispanic, and White homeowners respectively, for mortgages originated 2004–2006.

Q10. What is the implied contribution of the returns gap to the racial wealth gap?

A: Using a simple wealth accumulation model calibrated to PSID data on first-time homebuyer rates and home values (average first home for Black households: $142,587; for White households: $208,621), the paper finds an estimated Black-White gap in housing wealth at retirement of $169,389 versus an observed PSID gap of $182,771. Equalizing housing returns would reduce this gap by 37%. In contrast, equalizing first-time purchase rates alone reduces the gap by only about 1%, because low returns nullify the benefit of purchasing earlier. Equalizing both returns and purchase rates reduces the gap by 49%. Housing wealth in the primary home constitutes 43% of total net wealth for the average retirement-age Black household in PSID, implying the returns gap explains a quantitatively large share of the overall racial wealth gap.

Q11. What do the COVID-19 pandemic forbearance experience and mortgage modification evidence imply for policy?

A: Quasi-experimental estimates using servicer-level variation in modification propensity show that mortgage modifications cause economically large increases in housing returns for Black, Hispanic, and White homeowners alike, suggesting that since minority homeowners are more likely to become distressed, expanded modifications would disproportionately benefit them. The pandemic experience provides macroeconomic confirmation: after the onset of COVID-19 forbearance and foreclosure moratoria in March 2020, the Black-White gap in unlevered returns and distressed sales fell by approximately half, while the Hispanic-White gap (whose pre-pandemic distress convergence was already underway) remained comparatively stable. Administratively, Black homeowners who default are already 3–7 percentage points more likely than observationally similar White homeowners to receive a modification, even controlling for neighborhood and servicer, suggesting servicers partially internalize the larger distressed-sale discounts in minority neighborhoods.

Q12. Are neighborhood-level factors — specifically distressed-sale price discounts from illiquid real estate markets — important for explaining racial heterogeneity in returns conditional on distress?

A: Yes. Using MLS data on median days-on-market as a measure of real estate market thickness, the paper shows that distressed sale discounts are substantially larger in less-liquid markets, with discounts experienced by Black homeowners approximately 13 percentage points lower in the least-thick markets relative to the thickest. Black and Hispanic homeowners are disproportionately likely to realize distressed sales in thin markets. Regular sale returns are not affected by market thickness. This establishes that neighborhood market illiquidity is a second-order channel through which neighborhood-level factors contribute to the racial gap — primarily by amplifying the severity of distressed sale penalties rather than by affecting ordinary house price appreciation.

Key Concepts

Distressed sale: In this paper’s usage, an ownership spell that ends in either a foreclosure (where a lender seizes and sells the property after payment default) or a short sale (where the lender allows the homeowner to sell for less than the outstanding mortgage balance without holding the homeowner liable for the deficiency). Distressed sales are the central mediating factor between race and housing returns.

Unlevered return: The annualized ratio of sale price to purchase price, capturing property-level capital gains without reference to the financing structure. Computed as (P_sale / P_purchase)^(1/T) − 1. Does not capture leverage amplification or limited homeowner liability in foreclosure.

Levered return (internal rate of return): The discount rate that sets the net present value of all homeowner cash flows to zero, including down payment at purchase; monthly payments (principal, interest, taxes, insurance, maintenance); implicit rent; and the net proceeds at sale (property sale price minus outstanding principal balance, subject to a floor of $0.01 capturing limited liability). This measure accounts for both the amplifying effect of leverage on gains and the homeowner’s limited liability in underwater foreclosures.

Distressed sale frequency versus severity: The two distinct components through which distressed sales generate racial gaps. Frequency refers to the higher probability that a minority homeowner’s ownership spell terminates in a distressed sale. Severity refers to the larger price discount at distressed sale that minority homeowners experience, concentrated in neighborhoods with illiquid real estate markets. The paper’s decomposition finds frequency is the dominant margin.

Unobservable liquidity risk: Default risk arising from insufficient liquid wealth (cash, bank deposits, liquid securities) and income instability that is not captured by credit scores or other characteristics observable to lenders at mortgage origination. The paper’s ARM-reset event study shows this risk generates excess minority default responses even conditional on credit score and income.

Information friction (overoptimism): The tendency of minority homeowners, particularly Black homeowners, to hold expectations about future house prices, personal financial crises, and income growth that are more optimistic than their realized outcomes and than observationally similar White homeowners’ expectations. The paper uses this to explain why high-risk minority households do not self-select out of homeownership despite the high cost of distressed sales.

Credit supply channel: The mechanism by which the early-2000s expansion of private securitization and portfolio lending — channels that exhibited substantially greater growth among Black and Hispanic borrowers than among White borrowers — contributed to increased rates of minority distress during the Great Recession. Distinguished from GSE/FHA channels that did not exhibit comparable credit expansion and serve as the counterfactual.

Random Utility with Unobservable Alternatives

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

This paper addresses a foundational gap in the random utility model (RUM) literature: existing axiomatizations by Falmagne (1978) and McFadden and Richter (1990) assume that whenever a menu is observed, the choice frequencies of all alternatives in that menu are observable. In practice, the choice frequencies of some alternatives are routinely missing. The paper derives the full testable implications of the random utility model for such incomplete datasets, delivering a finite, nonredundant system of linear inequalities as a necessary and sufficient condition for RU-rationalizability.

The empirical backdrop motivates the formal contribution directly. In transportation choice (bus, train, walk, drive), revenue data from transit operators can reveal the market shares of bus and train but not walking or driving without survey data. In school choice, governments observe enrollment across public schools but may lack data on private school selections. In market-share analysis, private firms may not disclose sales figures. In each case, researchers typically aggregate all unobservable alternatives into a single “outside option,” treating it as one composite choice. The paper calls this the outside option approach and establishes its formal limitations.

The main theorem (Theorem 3.2) states that an incomplete dataset is RU-rationalizable if and only if two conditions hold jointly. The first is the classical nonnegativity of Block-Marschak (BM) polynomials, which appears in Falmagne’s original characterization and requires that certain inclusion-exclusion quantities over observed choice frequencies are nonneg. The second is a novel balance condition: for any “essential test collection” of choice sets, a specific net signed sum of BM polynomials across observable arcs crossing the boundary of that collection must be nonneg. This second condition captures the informational content that is lost when unobservable alternatives are collapsed. The characterization is nonredundant in the strong sense that removing any single inequality from either condition produces a strictly weaker system — every inequality is independently binding for some dataset.

The limitation of the outside option approach is made precise by Proposition 3.5: the reduced dataset formed by the outside option approach is RU-rationalizable whenever the original incomplete dataset satisfies condition (i) and condition (ii) for singleton essential test collections only. Consequently, if the original data violates condition (ii) for non-singleton essential test collections — meaning it is not genuinely RU-rationalizable — the outside option approach will nonetheless return a verdict of rationalizability. False acceptance of the random utility model is therefore possible under the outside option approach.

The proofs translate the rationalizability problem into a network flow problem on the hypercube lattice over subsets of alternatives, following Fiorini (2004). Each path from the empty set to the full alternative set corresponds to a linear order (ranking). The key methodological innovation is applying a feasibility theorem from network flow theory — specifically a generalization drawing on the max-flow min-cut theorem — to derive the necessary and sufficient conditions in the incomplete-data setting.

The paper also provides an efficient algorithm for computing tight bounds on unobservable choice frequencies, formulated as a minimum-cost transshipment problem. Because the constraint matrix is totally unimodular (it is the incidence matrix of a network), the network simplex algorithm applies directly. Applied to a lottery-choice dataset from McCausland et al. (2020) — 141 participants each choosing from subsets of five lotteries, with choices made six times per choice set — the authors treat two of the five lotteries as unobservable and compare bound widths. Their method yields significantly tighter bounds than the outside option approach and, critically, correctly identifies that lottery 4 is more desirable than lottery 3 among the unobservable alternatives. The outside option approach yields identical trivial bounds for both lotteries and thus cannot distinguish their relative desirability at all.

Q: What is the central research question? A: The paper asks: what are the testable implications of the random utility model when the choice frequencies of some alternatives are unobservable? The goal is a necessary and sufficient condition for RU-rationalizability under incomplete observation, along with a demonstration of what is lost when the standard outside option approach is used instead.

Q: What is the random utility model and why is it the focus? A: The random utility model posits a probability distribution over strict rankings of alternatives; each individual’s preferences correspond to one ranking. It is a cornerstone of discrete choice analysis in economics. Falmagne (1978) and McFadden-Richter (1990) characterized it under full observability of choice frequencies, making the extension to incomplete data a natural and practically important frontier.

Q: What does “incomplete dataset” mean formally in this paper? A: An incomplete dataset is a nonneg vector of choice frequencies satisfying: (i) for menus composed entirely of observable alternatives, frequencies sum to one; (ii) for menus that include at least one unobservable alternative, the sum of observable-alternative frequencies is at most one. The gap between the sum and one corresponds to the unobserved probability mass on unobservable alternatives.

Q: What are Block-Marschak polynomials and why do they appear? A: The Block-Marschak (BM) polynomial K(rho, D, x) is defined by inclusion-exclusion: it sums, with alternating signs, the choice frequency of alternative x over all supersets E of D. In Falmagne’s complete-data characterization, nonnegativity of all BM polynomials is necessary and sufficient for RU-rationalizability. In the incomplete-data setting, nonnegativity of BM polynomials remains necessary but is no longer sufficient.

Q: What is the novel condition in Theorem 3.2 beyond BM nonnegativity? A: Condition (ii) of Theorem 3.2 requires that for any “essential test collection” C of choice sets, the net observable outflow — the sum of BM polynomials on arcs leaving C minus the sum on observable arcs entering C — is nonneg. This balance condition captures the constraint that unobservable flow must be nonneg on every cut of the network corresponding to an essential test collection.

Q: What makes the characterization nonredundant, and why does nonredundancy matter? A: The characterization is nonredundant in the sense that for every individual inequality in conditions (i) and (ii), there exists an incomplete dataset that violates only that inequality and satisfies all others. This is established as part (b) of Theorem 3.2. Nonredundancy is essential for identifying precisely which inequalities the outside option approach discards: without it, some of the novel condition (ii) inequalities might be implied by others, and the argument that the outside option approach loses independent information would not hold.

Q: What does the outside option approach actually discard? A: Proposition 3.5 shows that the outside option approach retains only condition (i) (BM nonnegativity) and condition (ii) for singleton essential test collections. All condition (ii) inequalities corresponding to non-singleton essential test collections are discarded. Because the characterization is nonredundant, each discarded inequality is a genuinely independent constraint, meaning a dataset can violate any one of them while satisfying all others — including all conditions the outside option approach checks.

Q: Can the outside option approach produce a false acceptance of the random utility model? A: Yes. If the true incomplete dataset violates condition (ii) for some non-singleton essential test collection but satisfies all other conditions of Theorem 3.2 — including all conditions the outside option approach checks — then the original dataset is not RU-rationalizable, but the reduced dataset formed by collapsing unobservables into one outside option is RU-rationalizable. Researchers using the outside option approach would therefore erroneously conclude that the data-generating process follows a random utility model.

Q: How is the problem translated into a network flow problem? A: The authors build a directed network on the power set of alternatives, with arcs from D to D union {x} for each alternative x not in D, source at the empty set, and terminal at the full set X. Each source-to-terminal path corresponds to a unique linear order. A probability distribution over rankings corresponds to a flow, with flow conservation at interior nodes and total flow equal to one. The BM polynomial of an observable arc equals the required flow on that arc. Feasibility of this flow — guaranteed by a theorem generalizing max-flow min-cut — is equivalent to RU-rationalizability.

Q: What is the algorithmic contribution for bounding unobservable choice frequencies? A: The bounds problem is formulated as a minimum-cost transshipment problem on the same network. Because the constraint matrix is the incidence matrix of a network (totally unimodular), the network simplex algorithm applies and yields exact solutions efficiently. The algorithm produces tight upper and lower bounds for each unobservable choice frequency by optimizing the flow subject to all feasibility constraints from Theorem 3.2.

Q: How does the paper demonstrate tighter bounds empirically? A: The paper applies its method to a lottery stochastic choice dataset from McCausland et al. (2020), involving 141 participants choosing from subsets of five lotteries, with six repeated choices per choice set. The authors treat two of the five lotteries as unobservable. Their network-flow bounds are significantly tighter than the trivial bounds from the outside option approach. Specifically, their method correctly identifies that lottery 4 is more desirable than lottery 3 among the unobservable alternatives, a distinction the outside option approach cannot draw because it assigns identical trivial bounds to both lotteries.

Q: What is the monotonicity-based lower bound for unobservable choice frequencies? A: Under monotonicity (a weaker condition than full RU-rationalizability), the lower bound L(x*) for the choice frequency of unobservable alternative x* from menu D is the sum over observable alternatives a of the difference rho(D{x*}, a) minus rho(D, a), when D{x*} is in the domain. This lower bound is larger when removing x* from the menu substantially increases observable choice frequencies, indicating that x* was drawing demand away from observables and is therefore relatively desirable.

Q: How does this paper relate to McFadden-Richter (1990)? A: McFadden and Richter (1990) allow for menus to be unobserved but require that when a menu is observed, all its alternative frequencies are observed — a distinct setup from the present paper. Their characterization also involves infinitely many inequalities and is redundant. The present paper’s characterization uses finitely many inequalities and is nonredundant, making it more tractable both theoretically and computationally.

Q: What is the scope of the model regarding which alternatives are unobservable? A: The paper focuses on the case where the set of unobservable alternatives X* is fixed and consistent across all menus: a given alternative is either always observable or always unobservable. The domain of choice sets D is assumed to be an upper set (if a menu is in D, all supersets are too). The paper does not handle cases where observability of an alternative varies by menu.

Incomplete dataset: A nonneg vector of choice frequencies in which, for menus containing unobservable alternatives, the observable frequencies sum to at most one (not exactly one), with the residual mass attributable to unobservable alternatives.

Block-Marschak (BM) polynomial: An inclusion-exclusion quantity K(rho, D, x) defined as the alternating-sign sum of rho(E, x) over all supersets E of D; its nonnegativity is the classical Falmagne condition for RU-rationalizability under complete observation.

Essential test collection: A collection C of choice sets used to define the novel balance condition in Theorem 3.2; for each such C, the net observable outflow of BM polynomial values across the boundary of C must be nonneg for RU-rationalizability.

Outside option approach: The empirical practice of aggregating all unobservable alternatives into a single composite “outside option,” so that all remaining choice frequencies sum to a value below one and the residual is assigned to that composite. This approach retains only a subset of the testable implications of the random utility model.

Nonredundant characterization: A system of inequality conditions in which no single inequality is implied by the conjunction of all others; every inequality is independently binding for some dataset. This property is essential for identifying precisely which implications the outside option approach discards.

Network flow representation: A directed network on the power set of alternatives (source: empty set, terminal: full set X) in which each source-to-terminal path encodes a linear order, flow conservation corresponds to probability conservation, and feasibility of a flow with prescribed values on observable arcs is equivalent to RU-rationalizability.

Minimum-cost transshipment problem: The optimization problem used to compute tight bounds on unobservable choice frequencies; tractable via the network simplex algorithm because the constraint matrix is totally unimodular (the incidence matrix of a network).

Rationing by Race

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

Singh and Venkataramani ask whether resource scarcity causes discriminatory rationing of health care by patient race, with patient death as the starkest possible outcome of biased allocation decisions. They examine 107,221 inpatient admissions from 2015 to 2018 at two large urban academic teaching hospitals (each with over 500 beds) in a Southeastern U.S. city with a sizable Black population. Black patients accounted for 60% of admissions, were on average younger (52 vs. 59 years), more likely to be female (65% vs. 50%), and had similar comorbidity burdens and baseline in-hospital death rates (approximately 2% for both groups), but waited over two hours longer on average for an inpatient bed and were 27% less likely to be admitted to the ICU.

The authors exploit quasi-exogenous hour-to-hour variation in hospital capacity strain — measured as the share of inpatient beds occupied at the hour of a patient’s arrival — which clinical and qualitative literature establishes is difficult to predict even day-to-day. Capacity strain is coded in hospital-specific deciles (beds filled ranged from 69–78% in decile 1 to 91–95% in decile 10). The core regression interacts patient race with strain decile, controlling for hospital-specific hour-of-day, day-of-week, month-of-year, and year fixed effects; physician-of-record fixed effects; and a rich vector of patient characteristics including Elixhauser comorbidity indices, insurance status, and vital signs. Identification rests on the assumption that strain at the hour of arrival is conditionally independent of unobserved patient characteristics correlated with race — an assumption validated through balance tests on demographics, comorbidities, vital signs, machine-learning-derived admission themes, and selective discharge patterns.

The main finding is that in-hospital mortality rises for Black patients but not for White patients as hospitals approach capacity. At the tenth decile of strain, Black patients face a mortality rate 0.7 percentage points higher than White patients — a 47.6% relative increase over the 1.47% White mortality rate at the same decile. A pooled difference-in-differences estimate implies that approximately 15% of Black patient deaths at high strain (decile 10) would not have occurred had Black patients faced the same strain-mortality relationship as White patients (coefficient 0.0052, p = 0.025). This pattern is concentrated among patients with the greatest ex ante medical need as measured by above-median Elixhauser mortality index scores (a score with AUC of 0.92 for predicting in-hospital mortality) and, in qualitatively similar but less precisely estimated form, by abnormal vital signs at arrival.

The authors identify wait time for an inpatient bed as the primary mechanism. At all levels of capacity strain, high-need Black patients wait longer than low-need White patients — a pattern the authors characterize as a striking inversion of any need-based allocation principle. Racial disparities in wait times widen further at the highest decile of strain, exactly mirroring the mortality pattern. As an additional, more suggestive mechanism, the authors analyze free-text clinical documentation (the Reason for Admission field) using descriptive text features (time to completion, character count, average word length), sentiment analysis (subjectivity and polarity scores via TextBlob), and adjective counts. Documentation for Black patients exhibits features consistent with lower provider effort at all strain levels — shorter notes, less time deferred to completion — and subjectivity of notes and adjective counts diverge further by race at the highest strain decile, with White patients receiving increasingly detailed and descriptive notes as strain rises.

The findings are robust across sparse models (age, gender, hospital fixed effects only) through fully saturated specifications (DRG fixed effects, interactions of all controls with race and strain), and to replacing Elixhauser index composites with their 31 individual comorbidity components. The authors explicitly scope their findings to a pre-COVID-19 period (2015–2018), while noting that pandemic-era record capacity strain and racial disparities in health outcomes suggest de facto race-based rationing may have been far more severe during COVID-19.

Q: What is the central research question and why is the health care setting chosen? A: The paper asks whether increasing resource scarcity causes discriminatory rationing on the basis of race in consequential, high-stakes real-world decisions. Health care is chosen because it is high-stakes (patient death is the outcome), has a long documented history of racial discrimination at both provider and system levels, and offers uniquely detailed time-stamped electronic health record data that enables identification from hour-to-hour variation in capacity strain — a finer temporal resolution than most prior work.

Q: How is hospital capacity strain measured and what is the identifying variation? A: Strain is measured as the total number of patients occupying inpatient beds at the specific hour of a patient’s arrival, converted into hospital-specific deciles. The first decile corresponds to 69–78% of beds filled and the tenth decile to 91–95%. The identifying variation is residual hour-to-hour fluctuation in this measure after removing hospital-specific hour-of-day, day-of-week, month-of-year, and year fixed effects, which absorbs all predictable capacity patterns. Clinical and qualitative evidence establishes that even day-to-day strain is difficult to anticipate, making hour-to-hour residual variation plausibly as-if random.

Q: What are the main mortality findings, and how large are the racial disparities at peak strain? A: At the tenth decile of capacity strain, Black patients face a mortality rate 0.7 percentage points higher than White patients, representing a 47.6% relative increase over the 1.47% White mortality rate at that decile. The pooled difference-in-differences estimate (comparing decile 10 to deciles 1–9) implies that approximately 15% of Black patient deaths at high strain would not have occurred if Black patients had the same strain-mortality relationship as White patients (coefficient 0.0052, p = 0.025). White patient mortality does not increase at high strain; if anything, small (imprecisely estimated) decreases appear at deciles 7–9.

Q: Which patients drive the racial mortality disparity? A: The disparity is concentrated among patients with above-median Elixhauser mortality index scores — the ex ante sickest patients. The Elixhauser Mortality Index has a predictive AUC of 0.92 for in-hospital mortality. At decile 10, high-need Black patients experience a sharp increase in mortality not seen for high-need White patients or for low-need Black patients. Qualitatively similar but less precisely estimated results appear when acute need is measured by abnormal vital signs at arrival, with the difference that the triple interaction (race × strain × high-need vitals) is not statistically significant, consistent with vital signs being noisier proxies for severity than the Elixhauser indices.

Q: How do the authors validate the identifying assumption that strain is conditionally independent of patient composition by race? A: They document five types of supporting evidence: (i) the distribution of Black and White patients across hours of arrival and across strain deciles is nearly identical; (ii) regressions of patient demographics, all five Elixhauser comorbidity measures, and five vital signs abnormalities on race × strain interactions show no significant differential selection by race at different strain levels; (iii) machine-learning (Latent Dirichlet Allocation) topic themes from free-text admission notes change similarly by strain for Black and White patients; (iv) there is no evidence of selective discharge to hospice care by race and strain, with point estimates running counter to the hypothesis; and (v) strain is computed at time of arrival to the hospital rather than time of admission to an inpatient bed, preserving exogeneity.

Q: What is the primary identified mechanism for the mortality finding? A: Wait time for an inpatient bed is the primary mechanism. Black patients experience greater increases in wait times as strain rises compared to White patients, with the clearest divergence at decile 10 — exactly mirroring the mortality pattern. More strikingly, at every decile of strain (including decile 1, when beds are most abundant), high-need Black patients wait longer for a bed than low-need White patients, implying that the disparity is not solely a product of logistical constraints but reflects ingrained factors in clinical protocols, likely including implicit or explicit provider bias.

Q: What does the wait time evidence reveal about the role of medical need vs. race in allocation decisions? A: At lower strain levels, low-need patients appropriately wait longer than high-need patients. However, at higher strain levels (deciles 8–10) this need-based gap almost entirely disappears, while the racial gap in wait times persists. The gap between high-need Black and low-need White patients is larger than the gap between high-need and low-need patients of the same race, meaning race is a stronger predictor of wait times than medical need. This pattern is consistent with the paper’s conceptual framework in which increasing strain reduces providers’ ability to accurately assess medical need while increasing the weight assigned to racial identity.

Q: How is provider effort measured and what are the findings? A: Provider effort is inferred from features of free-text Reason for Admission documentation: time to completion, character count, average word length, TextBlob subjectivity and polarity scores, and adjective counts. Across all strain levels, Black patients’ documentation exhibits features consistent with lower effort — shorter completion times (providers less likely to defer documentation for clinical tasks), shorter notes with fewer characters and shorter words. At the highest strain decile, subjectivity scores for Black patients’ notes increase relative to White patients’ (driven by both rising Black and falling White subjectivity), and White patients receive more adjectives as strain rises while Black patients’ adjective counts do not increase. Polarity scores remain stable by race and strain.

Q: What do the documentation patterns suggest about compensatory behavior by providers? A: The authors speculate that providers may anticipate reduced care quality at high strain and compensate by becoming more conscientious with White patients — writing longer, more detailed, more descriptive notes as strain increases, and potentially exerting greater care effort correlated with these documentation improvements. This protective compensatory behavior appears substantially less pronounced or absent for Black patients, which the authors suggest may translate into the small imprecisely estimated decrease in White patient mortality at higher strain deciles. They explicitly characterize this interpretation as speculative and requiring further investigation.

Q: How robust are the main mortality findings to specification choices? A: The mortality findings hold across: (i) sparse models with only age, gender, and hospital/year fixed effects; (ii) linear probability and logistic models; (iii) models with DRG fixed effects to compare within-diagnosis; (iv) models interacting all control variables with patient race and strain; (v) models replacing the Elixhauser composite index with its 31 individual comorbidity components; and (vi) models additionally controlling for five individual abnormal vital sign indicators. Results are substantively unchanged across all these specifications.

Q: What additional care intensity measures are examined and what do they show? A: The authors also examine ICU admission, ICU length of stay, total inpatient length of stay, and inpatient charges. They find no strain-related racial disparities on these margins. However, they note that unconditionally (across all strain levels), Black patients receive fewer resources on average — they are 27% less likely to be admitted to the ICU. The authors treat these care intensity measures as harder to interpret because both over- and under-provision can harm patients, and thus view them as less informative for their research question.

Q: What conceptual framework guides the empirical predictions? A: The framework models providers as assessing perceived medical need Nij(t) = Ni × exp(−γ × S(t)), where the parameter γ captures the diminishing ability to accurately assess true need as strain S(t) rises. Simultaneously, the racial weight Rij(t) = Ri × φ(S(t)) increases with strain through the parameter φ(S(t)). When γ = 0 and φ = 0, allocation is race-neutral and need-based. When both parameters are positive, increasing strain simultaneously degrades need assessment and amplifies reliance on racial identity in allocation decisions — the paper’s core prediction, which is confirmed empirically.

Q: How do the findings relate to the COVID-19 pandemic? A: The data predate COVID-19 (2015–2018). The authors argue that pandemic conditions — record hospital capacity strain (especially in hospitals serving Black patients), extreme provider burnout, and documented racial disparities in health access — suggest race-based rationing may have been considerably more severe during COVID-19. The paper also contextualizes its findings within the pandemic-era debate over whether explicit race-based triage protocols were ethical or legal, arguing that de facto rationing by race appears to occur in ordinary care settings under typical stressors irrespective of that normative debate.

Q: What policy interventions do the authors suggest? A: The authors propose: increasing provider awareness of implicit biases; developing new algorithms to improve triage decisions for high-mortality-risk patients who might otherwise be overlooked; correcting existing care algorithms with documented racial bias; building provider peer networks to reduce biased treatment decisions; supporting patient self-advocacy; improving capacity prediction systems (as spurred by COVID-19); and creating load-shifting protocols and inter-hospital transfer networks to prevent resources from being stretched beyond capacity during high-strain periods.

Capacity strain: The state of a hospital when a high share of inpatient beds are occupied, measured here at the hour of patient arrival as hospital-specific deciles of bed occupancy (ranging from 69–78% full at decile 1 to 91–95% full at decile 10); the paper’s primary measure of resource scarcity.

Rationing by race: The paper’s term for the phenomenon whereby, as resource scarcity deepens, allocation decisions increasingly reflect patient racial identity rather than medical need — a form of discriminatory rationing that the authors distinguish from explicit (de jure) race-based triage and document as de facto practice.

Perceived need (N*): In the paper’s conceptual framework, the provider’s assessment of a patient’s medical need, which deviates from true need Ni by the factor exp(−γ × S(t)) as strain S(t) increases; captures the provider team’s diminishing ability or willingness to accurately assess true medical need under cognitive and resource constraints.

Racial weight (R*): The weight assigned to a patient’s racial identity in allocation decisions, modeled as Ri × φ(S(t)), where the function φ is increasing in capacity strain; represents the potential for discrimination — from implicit bias, algorithmic bias, reduced patient advocacy, or provider-patient social distance — to intensify as strain rises.

Wait time inversion: The condition, documented throughout the paper, where high-need Black patients wait longer for an inpatient bed than low-need White patients at every decile of capacity strain, including decile 1 when resources are most abundant — inverting the normative principle that greater medical need should yield faster access to care.

Elixhauser Mortality Index: A widely validated composite score of patient comorbid conditions used to predict in-hospital mortality (AUC = 0.92); used in this paper as the primary measure of chronic medical need, with patients split at the median into relatively sick (above median) and relatively healthy (below median) groups.

Provider effort (inferred): An unobserved construct inferred in this paper from features of free-text clinical documentation in the Reason for Admission field, including time to note completion, character count, average word length, TextBlob subjectivity and polarity scores, and adjective counts; features argued to reflect how much attention, detail, and care a provider invested in documenting — and by extension, in assessing — a patient’s condition.

Real Credit Cycles

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

This paper incorporates diagnostic expectations — beliefs that overweight the representativeness of recent data, formalized as $E_t^\theta(A_{t+1}) = E_t(A_{t+1}) + \theta[E_t(A_{t+1}) - E_{t-1}(A_{t+1})]$ with θ > 0 — into a workhorse real business cycle model with heterogeneous firms and risky defaultable debt, to assess whether non-rational belief overreaction can account for boom-bust credit cycles without requiring large fundamental shocks. The diagnosticity parameter θ is structurally estimated via simulated method of moments, targeting moments including forecast-error predictability from the IBES manager guidance database, and yields θ ≈ 0.991, consistent with prior estimates from financial analysts and professional forecasters. The estimated DE model generates several untargeted results that the rational-expectations (RE) benchmark cannot: countercyclical credit spreads, predictable firm-level bond returns, and investment fragility in good times — specifically, a one-standard-deviation negative TFP shock causes a much larger investment decline when the previous period had good TFP news than in normal times. The model also shows that the 2008-09 spread increase can be generated by mere disappointment of overoptimistic beliefs, not requiring a large negative TFP shock. These findings establish diagnostic expectations as a parsimonious and empirically disciplined mechanism for producing financial reversals in business cycle models.

Summary of a published paper based on the NBER working paper full text (w28416), AI-assisted, pending human review. See the linked original for the authoritative claims and full conditions.

Layer 1: Overview

Bordalo, Gennaioli, Shleifer, and Terry modify a standard heterogeneous-firm RBC model with risky defaultable debt by a single behavioral parameter — the diagnosticity θ governing belief overreaction to TFP news — to assess whether non-rational beliefs can quantitatively account for boom-bust credit cycles. The model departs from the rational expectations (RE) benchmark only in that firms and lenders form expectations diagnostically: after good TFP news, agents become excessively optimistic about future TFP, causing too much investment and debt issuance; when TFP growth disappoints relative to those optimistic expectations (even without an outright TFP decline), agents sharply revise down their beliefs, causing credit spreads to spike and investment to collapse. The diagnosticity parameter θ ≈ 0.991 is estimated by structural SMM targeting 16 moments — including 3 moments from IBES manager guidance data directly measuring the predictability of forecast errors — and is consistent with independent estimates from analyst forecasts (θ ≈ 0.9, Bordalo et al. 2019), professional macroeconomic forecasters (θ ≈ 0.5, Bordalo et al. 2020), and bond-price-implied beliefs (θ = 1.0, D’Arienzo 2020). The paper shows that the estimated DE model, unlike the RE benchmark, delivers countercyclical spreads, predictable firm-level bond returns, investment nonlinearity (fragility in good times), and an account of the 2008-09 spread episode requiring only a modest TFP disappointment.

In depth

Q1. What are diagnostic expectations, and how does the single parameter θ govern their departure from rational expectations?

Diagnostic expectations (DE) are beliefs that overweight outcomes that are representative of recent news relative to their true base rate, formalized as $E_t^\theta(A_{t+1}) = E_t(A_{t+1}) + \theta[E_t(A_{t+1}) - E_{t-1}(A_{t+1})]$, where $\theta \geq 0$ is the diagnosticity parameter: when $\theta = 0$ beliefs are rational, and when $\theta > 0$ agents exaggerate the persistence of current news shocks. The mechanism is grounded in the psychology of selective recall: good news makes good future outcomes top-of-mind and thus overweighted. In the context of an AR(1) TFP process, DE agents effectively behave as if TFP follows an ARMA(1,1) with an additional moving-average term that boosts the perceived response to current shocks. The parameter θ has a clean measurement interpretation: θ ≈ 1 means that for every unit of incoming news, agents’ beliefs overshoot by approximately one additional unit (forecast errors are roughly equal in magnitude to the news that generated them). DE are forward-looking (unlike adaptive expectations) and hence not mechanically subject to the Lucas critique, since agents’ beliefs respond to news in a structured way.

Q2. How is θ identified and estimated, and what disciplines the model’s departure from rationality?

The diagnosticity parameter θ is identified from three moments that directly exploit the predictability of future forecast errors from current firm-level investment and debt issuance growth — moments that are positive under DE and exactly zero under RE — drawn from the IBES manager guidance database covering 1999-2018. The key identification equation is: $\text{cov}(\Delta \text{Forecast Error}{t+1}, \Delta x_t) = a\pi a_x \rho \theta (1+\theta)$ where $x$ is investment or debt, positive if and only if θ > 0. In the data, a one-standard-deviation increase in the firm’s investment rate predicts approximately 10 percentage points stronger disappointment in next-year earnings, and a one-standard-deviation increase in debt issuance predicts about 5 percentage points stronger disappointment — robust to within-firm estimation that controls for heterogeneity in optimism across firms. The estimated θ ≈ 0.991 (s.e. 0.074) is precisely estimated and falls well within the range [0.5, 1.5] implied by independent estimates from other datasets. The RE model (constrained to θ = 0) cannot generate any comovement between future forecast error growth and current firm fundamentals, offering a falsifiable restriction that the data reject.

Q3. What is the investment fragility finding, and why can the RE model not replicate it?

The DE model generates a strong nonlinearity in investment: the same one-standard-deviation negative TFP shock causes a much larger investment decline when it follows a period of good TFP news (good times) than when it follows average or bad news; the RE model produces essentially no such nonlinearity, with investment responses roughly flat across initial conditions. The mechanism is as follows: after a positive TFP shock, firms and lenders become overoptimistic, driving high investment and low credit spreads. The aggregate investment response to the subsequent negative shock is therefore large — overoptimism has boosted the capital stock and the debt level beyond what fundamentals warrant, so the negative shock both lowers true productivity and triggers a sharp correction in beliefs. Under RE, agents correctly anticipate mean reversion of TFP and do not overbuild, so the same negative shock hits a less-leveraged economy and generates a smaller correction. This fragility-in-good-times mechanism is consistent with empirical evidence from Bachmann et al. (2013), Winberry (2017), and Bloom et al. (2018) that investment is more sensitive to shocks during booms.

Q4. How does the DE model account for countercyclical spreads, and why does the RE model predict the wrong sign?

Under DE, credit spreads are countercyclical because lenders become excessively optimistic about future TFP in good times, driving down perceived default risk and hence spreads below their rational counterpart; when optimism wanes, spreads spike beyond what fundamental deterioration alone would warrant. Under RE with constant required returns (as modeled), the supply of capital tracks fundamentals; in good times with high TFP, default risk is genuinely lower, so spreads fall — a qualitatively correct prediction. But the RE model also generates a positive correlation between spreads and investment in the cross-section of firms, while the data show a strong negative correlation (Column 10 of Table 5: Corr(Investment, Spread) = -0.057 in data, -0.054 in DE model, +0.083 in RE model). The DE mechanism driving this: overoptimistic lenders simultaneously over-supply credit (reducing spreads) and firms over-invest, creating the negative comovement. The paper links this formally to the concept of “financial shocks” in Jermann and Quadrini (2012) and Gilchrist and Zakrajšek (2012): in the DE framework, waning optimism produces inward shifts in the supply of capital that appear as exogenous financial shocks in reduced-form analyses.

Q5. How does the model account for the 2008-09 spread episode, and what shock size is required?

The DE model generates a spread increase consistent in magnitude with the 2008-09 episode from a modest moderation in TFP growth — not an outright TFP decline, but merely disappointment relative to the optimistic expectations formed during the preceding boom — while the RE model requires a large negative TFP shock of implausible size. During 2005-2007, a sequence of positive TFP shocks made firms and lenders excessively optimistic; when TFP growth merely slowed in 2007-08 (below the high level agents had been projecting), their beliefs corrected sharply, spreading up and investment down. In the DE model, the deceleration of TFP growth is sufficient to produce spread increases matching the observed magnitude during 2008-09, along with quantitatively consistent declines in aggregate investment, credit, and earnings forecast revisions. The RE model cannot match this because rational agents, correctly anticipating mean reversion, would not have built up the overoptimistic base to correct from.

Q6. How do the microeconomic boom-bust predictions of the model perform out-of-sample?

The model-simulated data replicate the firm-level boom-bust cycles documented in the paper’s Section 2: current overoptimism (proxied by high investment or debt issuance) predicts next-year spread increases, lower realized bond returns, and subsequent investment declines, with magnitudes that quantitatively match the data regressions; the RE model generates none of these predicted cycles. Specifically, in model-simulated firm-level regressions: higher current investment predicts 1-year-ahead spread increases; current spread increases predict negative future bond returns (the diagnostic model implies bonds are overpriced during booms, consistent with predictable low returns); and current high investment predicts future investment declines (mean reversion amplified by DE correction). All three predictions are also confirmed in the data and at the sectoral level, providing multiple out-of-sample validation tests. The diagnosticity parameter θ = 1 estimated from forecast errors simultaneously fits these untargeted dynamics.

Key Concepts

diagnostic expectations : beliefs that overweight outcomes representative of recent news, with the single deparature parameter θ ≥ 0 governing the degree of overreaction; in the AR(1) TFP context, agents act as if TFP follows an ARMA(1,1) with over-weighted current shocks; estimated at θ ≈ 1 from firm-level forecast error data, consistent with independent estimates from multiple other datasets.

fragility in good times : the paper’s key qualitative finding that the investment response to a given negative TFP shock is much larger when the shock follows a period of positive TFP news; arises because DE agents have built up excessive optimism, inflated capital stocks, and stretched leverage during the boom, making the correction larger; absent in the RE model.

diagnosticity parameter (θ) : the single behavioral parameter governing the degree to which agents overweight representative recent outcomes; θ = 0 is rational expectations; θ ≈ 1 is the structural SMM estimate, implying that forecast errors are roughly as large as the news that generated them; identified from the covariance between future forecast-error growth and current investment/debt changes.

financial shocks as waning optimism : the paper’s interpretation of “financial shocks” — inward shifts in the supply of capital generating spread spikes — as the endogenous waning of previously excessive diagnostic optimism, rather than exogenous disturbances to lender preferences or required returns; provides microfoundations for the Jermann-Quadrini and Gilchrist-Zakrajšek empirical findings.

countercyclical credit spreads : the empirical regularity that credit spreads fall in good times and rise in bad times, a moment the DE model matches (through overoptimistic lenders compressing spreads in booms) but the RE model with constant required returns fails to match in the cross-section (predicting a positive correlation between investment and spreads).

Risk Sharing Tests and Covariate Shocks: Drought, Floods, and Pests in Uganda

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

This paper identifies and corrects a fundamental flaw in the standard methodology for testing efficient risk-sharing when shocks are covariate (affecting common prices rather than only individual incomes). The standard Townsend (1994) approach infers marginal utilities of expenditure (MUEs) from total expenditures, which implicitly assumes homothetic preferences — specifically Constant Relative Risk Aversion (CRRA) — under which all goods have unitary income elasticities and a single scalar price index captures all price effects. Ligon demonstrates that this assumption causes the standard test to fail when applied to covariate shocks such as droughts, floods, and agricultural pests, because these shocks change relative prices in ways that cannot be captured by a single price index. The perverse consequence is that in Ugandan data, every covariate shock — drought, floods, pests, and adverse prices — appears to improve household welfare under the CRRA specification (significant positive coefficients of 0.046, 0.097, 0.095, and 0.103 respectively, all significant at p<0.01), a result the paper argues is mechanically induced by the mis-specification rather than reflecting reality.

The paper makes two core theoretical contributions. First, it characterizes the complete class of preferences that permit MUE inference from expenditure data alone — specifically, requiring that item-level expenditures be “lambda-separable” (additively separable in the MUE and prices). Solving the resulting functional equations yields exactly two families of semiparametric demand systems: Constant Frisch Elasticity (CFE) demands (a generalization of CRRA) and Generalized Stone-Geary demands. Only CFE demands are tractable for panel estimation. Second, the paper shows that under CFE preferences, log expenditures on each good j follow the system: log x^j_it = a_j(p_t) + g_j(z_it) + beta_j * w_it + epsilon^j_it, where beta_j is the good-specific Frisch elasticity and w_it = -log lambda_it is the negative log MUE. This allows price effects to enter flexibly through good-time fixed effects rather than a single index, and MUEs to be recovered via factor analysis on the residual covariance matrix.

The empirical work uses eight waves of the Ugandan National Panel Surveys (2005–2020), an unbalanced panel of 5,601 distinct households yielding 22,791 usable household-year observations across 41 consumption goods (primarily food items). Uganda is divided into four regional markets, producing 32 market-year cells and 1,312 market-year-good dummies. Estimated Frisch elasticities vary substantially across goods — passion fruit is roughly three times as income elastic as cassava — emphatically rejecting the hypothesis of equal elasticities required by CRRA.

Using CFE-estimated MUEs, the risk-sharing test shows that none of the four covariate shocks has a significant effect on welfare (CFE coefficients: drought 0.010, floods 0.035, pests 0.041, adverse prices -0.043, all insignificant). The pattern holds across all time windows from 0–12 months: 42 of 52 covariate shock coefficients are significant and positive in the CRRA specification, versus only 4 of 52 in the CFE specification — barely above the 2.6 false positives expected under the null. These findings indicate that the welfare impacts of covariate shocks in Uganda operate primarily through the common price channel rather than through idiosyncratic income variation, meaning they are broadly shared within market-regions. Idiosyncratic income shocks, by contrast, show the expected pattern: they reduce welfare significantly in both specifications (CFE: 0.050***, CRRA: 0.071***), and health shocks are significant only in CFE (−0.059**).

Q: Why does the standard CRRA risk-sharing test fail for covariate shocks? A: Under CRRA preferences, MUEs depend on total expenditures only through a single scalar price index pi(p). When a covariate shock raises prices of inelastic goods (primarily food), total food expenditures increase even as actual consumption quantities fall. Because risk-sharing tests based on CRRA total expenditures cannot separate this price effect from a welfare improvement, the shock appears to raise welfare. The disturbance term in the CRRA TWFE regression depends on the very prices affected by covariate shocks, violating the exclusion restriction.

Q: What is the lambda-separability condition, and why does it matter? A: Lambda-separability requires that for each good j, some transformation phi_j of expenditures on that good can be written as the sum of a function of prices and a function of the MUE: phi_j(x_j(p,lambda)) = a_j(p) + b_j(lambda). This property is necessary for time fixed effects to absorb price variation and household fixed effects to absorb Pareto weights, which is the identification strategy behind all TWFE risk-sharing tests. Without it, no panel estimator using only expenditure data can consistently recover MUEs.

Q: What are the two demand families that satisfy lambda-separability, and what distinguishes them? A: Theorem 1 establishes that rationalizable lambda-separable demands must belong to either the Constant Frisch Elasticity (CFE) family or the Generalized Stone-Geary family. In CFE demands, log expenditures on each good equal the log of a price function minus beta_j times log lambda, where beta_j is a good-specific constant Frisch elasticity. The Stone-Geary family has a more complex nonlinear form that does not lend itself to linear estimation of log MUEs, making CFE the tractable choice. Both families nest CRRA as the special case where all beta_j are equal.

Q: How are MUEs estimated from the CFE system in practice? A: Estimation proceeds in two steps. First, log expenditures on each good are regressed on good-time-market effects and household demographic controls to obtain residuals. Second, the covariance matrix of these residuals has the factor structure Sigma = Var(w)betabeta’ + Psi, where beta is the vector of Frisch elasticities; the rank-one matrix beta*beta’ is recovered from the sample covariance matrix via factor analysis, and household-level MUEs are then obtained by regression using the estimated beta as generated regressors.

Q: What do the estimated Frisch elasticities reveal about preferences in Uganda? A: The Frisch elasticities beta_j vary substantially across the 41 goods in the Ugandan sample. Starchy staples and salt are least elastic (lowest beta_j), while fresh milk, sweet bananas, coffee, oranges, and passion fruit exhibit high elasticities — passion fruit is roughly three times as income elastic as cassava. The hypothesis that all elasticities are equal (the CRRA restriction) is easily rejected, providing direct evidence against homothetic preferences in this population.

Q: What direct evidence does the paper provide that droughts, floods, and pests are genuinely covariate and harmful? A: About 39% of Ugandan households reported drought in the 2005–06 round. Among drought reporters, 92% said it affected their production, 80% said it affected their income, and 50% said it affected their consumption. Drought, pests, and adverse prices (but not floods) led to statistically significant increases in local farmgate prices. Among markets experiencing covariate shocks, 82%, 74%, 44%, and 53% of t-tests rejected equality of relative food prices for drought, floods, pests, and adverse prices respectively. Dietary diversity and intake of vitamin B-12 (from animal-source foods) declined significantly following covariate shocks.

Q: How do households cope differently with covariate versus idiosyncratic shocks? A: Households experiencing covariate shocks primarily relied on self-insurance: 51% of drought-affected households reduced consumption and 45% drew on savings, with increased labor supply also reported. In contrast, households experiencing idiosyncratic shocks most often relied on help from friends and family (52%). This behavioral difference is consistent with the finding that covariate shocks affect welfare mainly through common price channels that are not individually insurable through social networks, while idiosyncratic shocks are partially absorbed via informal transfers.

Q: What do the CFE results imply about the nature of insurance against covariate shocks in Uganda? A: The CFE regression finds that none of the four covariate shocks (drought, floods, pests, adverse prices) has a statistically significant effect on household MUEs when time-market fixed effects are included. This implies that the welfare impact of covariate shocks is transmitted primarily through common price changes that affect all households in a market-region symmetrically, rather than through idiosyncratic income variation. Effectively, covariate shocks are “shared” within market-regions — but through price deterioration affecting everyone, not through informal transfers.

Q: How robust are the results across different shock time windows? A: Figure 3 shows that for the CRRA specification, any prior covariate shock 3–12 months earlier has a significant positive effect on log consumption in every month, while for the CFE specification no shock window produces a significant effect on w. In the full tabulation across all shock types and windows (Tables 4 and 5), 42 of 52 covariate shock coefficients are significant and positive in CRRA versus only 4 of 52 in CFE — the latter barely exceeding the 2.6 false positives expected under the null hypothesis of full insurance.

Q: What are the policy implications of these findings for relief program design? A: Because covariate shocks affect welfare mainly through common prices within market-regions, relief programs should target communities rather than individual households, since the burden is broadly shared and not concentrated. Policies that integrate markets across regions of Uganda or connect Ugandan markets to broader African or world markets would reduce the price impact of local covariate shocks. Targeted household transfers would be less effective than interventions that stabilize regional prices or supply.

Q: What broader applicability do CFE MUEs have beyond risk-sharing tests? A: Since MUE construction is independent of the risk-sharing hypothesis, CFE-estimated MUEs can be used to estimate and test any dynamic life-cycle model that puts structure on the evolution of MUEs over time, including consumption Euler equations, intertemporal marginal rates of substitution calculations, and household bargaining models. The CFE approach requires only the same expenditure data used in the standard CRRA approach and therefore serves as a more general drop-in replacement across all settings where CRRA MUEs are currently employed.

Marginal Utility of Expenditure (MUE): The Lagrange multiplier lambda on the household budget constraint in the consumer’s optimization problem; the object whose proportionality across households (log lambda_it = log mu_t - log theta_i) characterizes efficient risk-sharing. It is a function of budget, prices, and household characteristics — not reducible to a scalar function of total expenditure except under special preference restrictions.

Lambda-separability: A property of Frischian expenditures on good j such that some transformation phi_j(x_j) can be written as the sum of a function of prices and a function of the MUE alone — phi_j(x_j(p,lambda)) = a_j(p) + b_j(lambda). This is the necessary and sufficient condition for using time fixed effects to control for prices and household fixed effects to control for Pareto weights in a TWFE risk-sharing regression based solely on expenditure data.

Constant Frisch Elasticity (CFE) expenditure system: The tractable member of the two demand families satisfying lambda-separability, characterized by log x^j_it = a_j(p_t) + g_j(z_it) + beta_j * w_it + epsilon^j_it, where beta_j is a good-specific constant elasticity of expenditures with respect to MUE. Nests CRRA as the special case of equal beta_j across all goods, but admits nonhomothetic preferences and fully flexible relative-price responses.

Frischian demands: Demands expressed as functions of prices and the MUE lambda rather than prices and budget — f(p, lambda). Homogeneous of degree zero in (p, 1/lambda), equivalently written f(p*lambda). This representation is central to the lambda-separability characterization because it separates the role of the budget (via lambda) from the role of prices directly.

Covariate shock: In this paper’s usage, a shock that affects prices common to all households in a market-region — not merely a shock affecting many households simultaneously. The key analytical distinction is that idiosyncratic shocks change individual budgets without changing prices, while covariate shocks change prices, which is what causes the standard CRRA test to fail.

Nonhomothetic preferences: Preferences for which expenditure shares vary with income (budget), so no single scalar price index can fully represent the welfare impact of price changes. The paper confirms nonhomotheticity in the Ugandan data through widely varying Frisch elasticities, and argues this is the root cause of the CRRA test’s failure for covariate shocks — a problem that does not arise when shocks are idiosyncratic and leave prices unchanged.

Screening and Segmenting: A Consumer Surplus Perspective

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

Bergemann, Heumann, and Wang study consumer surplus when a monopolist simultaneously engages in second-degree price discrimination (screening consumers within each market segment through quality-differentiated menus) and third-degree price discrimination (offering different menus across segments). The central question is which market segmentation maximizes aggregate consumer surplus, and under what conditions any segmentation benefits consumers at all.

The model features a monopolist selling vertically differentiated goods of quality q at strictly convex cost c(q) to a continuum of buyers with privately known values v drawn from an aggregate market m*. A segmentation is any decomposition of m* into submarkets, each receiving a profit-maximizing screening menu. The seller observes segment identity but not individual values. The problem of finding the consumer-optimal segmentation is, on its face, an optimization over distributions of distributions — an infinite-dimensional object.

The paper’s central methodological contribution is a dramatic dimensional reduction. Theorem 1 establishes that the maximum consumer surplus achievable by any segmentation equals the maximum of the expected local information rent, u(v,h) = h·Q(v−h), over all inverse hazard rate functions h satisfying a majorization constraint h ≺ h* (where h* is the aggregate market’s inverse hazard rate). The local information rent captures both the extensive margin (h measures the mass of higher-value buyers per unit of value-v buyers who earn rent from v’s allocation) and the intensive margin (Q(v−h) is the quality allocated to value v, decreasing in h as distortion increases). The two margins trade off: raising h widens the base of rent-earning buyers but worsens allocative distortion, making u(v,h) hump-shaped in h with an interior maximizer h̄(v).

The consumer-optimal segmentation has a striking structural property: every buyer of a given value v receives the same quality in every segment in which they appear, even though the monopolist could in principle offer different qualities across segments. Prices, however, differ across segments for identical buyers. This holds because the optimal segmentation is always a uniform segmentation — one in which the inverse hazard rate hm(v) is equalized across all segments containing value v.

Under log-concavity of both aggregate demand (equivalently, a non-increasing aggregate inverse hazard rate h*(v), satisfied by uniform, normal, logistic, and exponential distributions) and the supply function Q(v) (equivalent to c’’’(q)q/c’’(q) ≥ −1, satisfied by all power cost functions), the optimal segmentation takes a transparent two-regime form (Proposition 3): for values below a threshold v̂ where h*(v̂) = h̄(v̂), the inverse hazard rate is reduced to h̄(v) by concentrating low-value buyers; for values above v̂, the aggregate market is left unchanged. The resulting segments are nested convex intervals [vm, v̄], all sharing the same upper bound v̄, with pricing differing across segments only by a quality-independent base price Tm that increases with vm (Theorem 2).

Corollary 3 delivers the sharpest policy-relevant finding: under log-concave demand and supply, zero segmentation is optimal — any segmentation harms consumers — if and only if h*(v̲) ≤ h̄(v̲) at the lowest value v̲. For iso-elastic costs c(q) = q^γ/γ (γ > 1), this becomes η*(v̲) ≤ γ/(1−γ), where η*(v̲) is the aggregate demand elasticity at the bottom of the distribution. When demand is sufficiently elastic relative to supply, the monopolist’s screening already provides near-optimal consumer rents and no redistribution of buyers across segments can improve them. More elastic supply (lower γ) shrinks the set of markets where zero segmentation is optimal (Proposition 4, Zγ’ ⊂ Zγ for γ’ < γ); more inelastic supply (higher γ) expands it, and in the limit γ → ∞ zero segmentation is suboptimal only when the aggregate allocation itself is efficient.

For iso-elastic costs, the optimal segmentation assigns each segment a Pareto distribution below v̂ with shape parameter α = γ/(γ−1), and the aggregate market above v̂ (Corollary 1). Each segment’s demand elasticity equals the constant γ/(1−γ) below v̂ and the aggregate elasticity above (Corollary 2): the supply elasticity 1/(γ−1) determines how elastic demand must be made within segments to counteract monopoly distortions. The paper also extends the framework to adverse selection (where seller cost rises with buyer type), with the full reduction to inverse hazard rate optimization preserved when the rate of increase in adverse selection satisfies τ’’(v)v/τ’(v) ∈ [0,1] (Proposition 5).

Q: What is the local information rent and why is it central? A: The local information rent is u(v,h) = h·Q(v−h), where h is the inverse hazard rate at value v and Q is the inverse marginal cost (supply) function (equation 9). The factor h captures the extensive margin — the mass of higher-value buyers per unit of value-v buyers who earn rent from v’s quality allocation — while Q(v−h) captures the intensive margin — the quality allocated to v via the virtual value v−h, which falls as h rises. Because u is hump-shaped in h, there is an interior rent-maximizing inverse hazard rate h̄(v) for each value. Lemma 2 establishes that in every regular market, total consumer surplus equals the integral of u(v,hm(v))dFm(v), so the entire segmentation problem reduces to choosing h.

Q: What is the majorization constraint and what does it exactly characterize? A: The majorization constraint h ≺ h* requires that for all v ∈ V, the integral from v̲ to v of [h*(t) − h(t)]dF*(t) ≥ 0 (equation 18). Proposition 1 shows that for any segmentation σ, the average inverse hazard rate hσ must satisfy hσ ≺ h*. A partial converse holds: given h ≺ h* under regularity conditions, a uniform segmentation implementing h exists. The constraint is strictly weaker than the pointwise bound h ≤ h* available in the binary case because it permits h to exceed h* at some values (dilution) provided it falls sufficiently below h* at higher values (concentration) to maintain the cumulative inequality.

Q: What are concentration and dilution, and how do they interact? A: Concentration gathers buyers of a given value into fewer segments, lowering their inverse hazard rate below h*(v). Dilution raises the inverse hazard rate of value v by placing v in segments where immediately higher values are missing — creating gaps in the support — thereby increasing the support increment Δm(v) and hence hm(v) (equation 12). Dilution at v requires that values just above v have already been concentrated elsewhere to create the gaps; concentration thus enables dilution, linking the two tools. With only binary values, only concentration is available; with a continuum, dilution can strictly expand achievable consumer surplus by permitting h to exceed h* at low values.

Q: What does Theorem 1 establish and why is it a major simplification? A: Theorem 1 states that the maximum consumer surplus over all segmentations of m* equals the maximum of ∫u(v,h(v))dF*(v) over all h satisfying the majorization constraint h ≺ h* (equation 25). The original problem maximizes over distributions on the infinite-dimensional space of probability measures on V; the reduced problem is a standard optimal control problem over a single real-valued function h: V → R+, amenable to Karush-Kuhn-Tucker methods and often yielding closed-form solutions. Furthermore, every optimal segmentation is a uniform segmentation implementing some h solving the reduced problem, so the reduction is exact. The optimal h always satisfies regularity (h’(v) ≤ 1), meaning v − h(v) is non-decreasing, which ensures segments in the optimal uniform segmentation are themselves regular.

Q: What is the structural property of consumer-optimal segmentations regarding quality across segments? A: In any consumer-optimal segmentation, every buyer of value v receives the same quality in every segment in which they appear (the uniform quality property following from Theorem 1). This holds because the optimal inverse hazard rate h(v) is equalized across segments (uniform segmentation), and quality in a regular market is qm(v) = Q(v − hm(v)), which depends on the market only through hm(v). Prices, however, differ across segments for identical buyers: the monopolist does not redesign its product line across segments but adjusts only quality-independent base prices. This is counterintuitive because nothing in the monopolist’s problem requires quality uniformity — it emerges purely from the consumer surplus maximization.

Q: What conditions guarantee the simple two-regime convex segmentation structure? A: Log-concavity of aggregate demand — equivalently, h*(v) non-increasing in v, satisfied by uniform, normal, logistic, and exponential families — and log-concavity of the supply function Q(v), equivalent to c’’’(q)q/c’’(q) ≥ −1, together guarantee the structure of Proposition 3 and Theorem 2. Under these conditions, h̄(v) is strictly increasing in v (log-concave supply) while h*(v) is decreasing (log-concave demand), so they cross exactly once at v̂. The optimal h equals h̄(v) below v̂ and h*(v) above. Only concentration (not dilution) is ever used because log-concave supply makes u concave in h and log-concave demand ensures monotone ordering of marginal local information rents across values, so the binding majorization constraint becomes the pointwise constraint at the bottom.

Q: What is the structure of convex segmentations and their menus (Theorem 2)? A: Under log-concave demand and supply, the consumer-optimal segmentation consists of segments m with absolutely continuous supports [vm, v̄] for varying lower bounds vm ≤ v̂, all sharing the same upper bound v̄ (Part 1 of Theorem 2). Pricing across these segments differs only by a quality-independent base price Tm that is increasing in vm — more concentrated segments (lower vm) face a lower base price and carry higher information rents — while the quality menu p(q) is uniform across segments (Part 2). Equivalently, the monopolist offers nested menus all sharing the same efficient upper bound quality Q(v̄), differing in how far down the menu is extended and in the price of the lowest offered quality.

Q: What do Corollaries 1 and 2 say for iso-elastic cost functions? A: With iso-elastic cost c(q) = q^γ/γ (γ > 1) and log-concave demand, the consumer-optimal segmentation assigns each segment a Pareto distribution with shape parameter α = γ/(γ−1) below the threshold v̂, and the aggregate distribution above v̂ (Corollary 1). This delivers a constant demand elasticity of γ/(1−γ) within each segment below v̂, matching the aggregate market’s elasticity above v̂ (Corollary 2). The Pareto shape — and thus the degree of demand manipulation — is determined entirely by the supply elasticity 1/(γ−1): more elastic supply (lower γ) mandates a higher shape parameter α and more elastic within-segment demand to counteract larger monopoly distortions.

Q: When is zero segmentation optimal, and what is the precise elasticity condition? A: Under log-concave demand and supply, zero segmentation is optimal if and only if h*(v̲) ≤ h̄(v̲) — the aggregate inverse hazard rate at the lowest value already lies at or below its rent-maximizing level (Corollary 3). Since h* is decreasing under log-concavity, this condition at v̲ implies it holds everywhere, so the designer cannot improve rents at any value. For iso-elastic cost, the condition becomes η*(v̲) ≤ γ/(1−γ): aggregate demand elasticity at the bottom must be at least as large in magnitude as one plus the supply elasticity. For a Pareto aggregate distribution with shape parameter α, zero segmentation is optimal when α ≥ γ/(γ−1).

Q: How does supply elasticity govern the scope for beneficial segmentation (Proposition 4)? A: Proposition 4 establishes that for iso-elastic cost, the set of markets Zγ where zero segmentation is optimal is strictly nested increasing in γ: for any γ’ < γ, Zγ’ ⊂ Zγ. More elastic supply (lower γ) amplifies monopoly distortions and enlarges the set of markets where segmentation benefits consumers; more inelastic supply (higher γ) makes quality provision rigid, reducing segmentation’s scope. In the limit γ → ∞ (approaching unit demand), zero segmentation is suboptimal only if the aggregate allocation is already efficient — but this limit also means very inelastic supply, so the potential benefits from segmentation have shrunk toward zero simultaneously.

Q: How does this paper compare to and depart from Haghpanah and Siegel (2023)? A: Haghpanah and Siegel (2023) showed that in generic markets with a finite number of goods, some segmentation always improves consumer surplus relative to the aggregate market. This paper shows that with a continuum of qualities, this universal improvement result fails: Corollary 3 identifies a large, non-degenerate class of markets satisfying Haghpanah and Siegel’s genericity conditions where zero segmentation is optimal for consumers. The discrepancy arises because the log-concave supply condition (equation 27) is violated in finite-good environments — Haghpanah and Siegel explicitly provide a counterexample showing their result fails with a continuum of goods. This paper characterizes exactly when the finite-good gains vanish as the quality space becomes continuous, providing the precise elasticity conditions.

Q: What changes and what is preserved when extending to adverse selection? A: In the adverse selection specification, buyer net value v is private and the seller’s cost per unit is τ(v) − v, increasing in v when τ’(v) > 1. The local information rent becomes w(v,h) = u(v, τ’(v)·h), where adverse selection enters by amplifying the effective inverse hazard rate by τ’(v) (equation 40). Proposition 5 confirms that the full reduction to majorization-constrained optimization over h goes through, and the optimal segmentation features more elastic within-segment demand when adverse selection is more severe. The reduction requires τ’’(v)v/τ’(v) ∈ [0,1] (equation 39), bounding the rate of increase of adverse selection severity; if this fails, the key inequality (35) driving the optimality of uniform segmentations may break down.

Q: What are the policy implications for regulation of price discrimination? A: The results imply that blanket restrictions on market segmentation may harm consumers by preventing welfare-enhancing price discrimination in markets where demand is sufficiently inelastic relative to supply (the region outside the zero-segmentation condition). In markets satisfying η*(v̲) ≤ γ/(1−γ), allowing segmentation yields no consumer benefit, so restrictions are harmless to consumers. The key policy-relevant primitives are demand and supply elasticities, which are in principle measurable. The findings also imply that the welfare effects of data-driven personalized pricing depend critically on the interaction between consumer heterogeneity (demand shape) and cost structure (supply elasticity), rather than on the degree of segmentation per se.

Local information rent: u(v,h) = h·Q(v−h), the total consumer surplus generated per unit mass of buyers at value v as a function of the inverse hazard rate h. The factor h is the extensive margin (mass of higher-value buyers per unit of value-v buyers who earn rent) and Q(v−h) is the intensive margin (quality allocated to v via the virtual value v−h). It is hump-shaped in h with interior maximizer h̄(v), and the segmentation problem reduces entirely to maximizing its expectation.

Inverse hazard rate hm(v): in a continuous market, (1−Fm(v))/fm(v); generalized to accommodate atoms and support gaps (equation 12). It simultaneously determines the virtual value ϕm(v) = v − hm(v) (governing allocative distortion) and the scaled mass of higher-value buyers per unit of value-v buyers (governing the extensive margin of rents). The dual role requires both a continuum of qualities and endogenous segmentation.

Majorization constraint h ≺ h*: for all v, the cumulative integral of [h*(t)−h(t)]dF*(t) from v̲ to v is non-negative (equation 18). It is the exact characterization of inverse hazard rate functions achievable by some segmentation of m*, strictly weaker than the pointwise bound h ≤ h* of the binary case because it permits h to exceed h* at some values (dilution) provided it falls sufficiently below h* at higher values (concentration).

Uniform segmentation: a segmentation in which every buyer of value v faces the same inverse hazard rate hm(v) = hσ(v) in every segment containing v (equation 22). Theorem 1 establishes that every consumer-optimal segmentation is uniform; this class converts the double integral over segments and values into a single integral against F*, enabling the dimensional reduction of Theorem 1.

Concentration and dilution: the two tools by which segmentation modifies inverse hazard rates. Concentration gathers buyers of a given value into fewer segments, lowering hm(v) below h*(v). Dilution raises hm(v) above h*(v) by placing value v in segments where immediately higher values are absent, creating support gaps. Dilution requires prior concentration of adjacent higher values, so the two tools are linked; under log-concave demand and supply, only concentration is used in the optimal segmentation.

Convex segmentation: a segmentation whose constituent segments have nested convex interval supports [vm, v̄] all sharing the same upper bound v̄, with varying lower bounds vm. This is the consumer-optimal structure under log-concave demand and supply (Theorem 2). For iso-elastic cost, each segment below the threshold v̂ corresponds to a Pareto distribution with shape parameter α = γ/(γ−1) determined by cost convexity γ.

Zero-segmentation condition: the condition under which no segmentation can improve consumer surplus over the aggregate market. Under log-concave demand and supply with iso-elastic cost c(q) = q^γ/γ, it is η*(v̲) ≤ γ/(1−γ): aggregate demand elasticity at the lowest value must be at least as large in magnitude as one plus the supply elasticity (Corollary 3). When this holds, any redistribution of buyers across segments strictly reduces consumer surplus.

Supply, Demand, Institutions, and Firms: A Theory of Labor Market Sorting and the Wage Distribution

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

Layer 1 — Overview

Research question. How do workforce composition (labor supply), labor demand, and minimum wage policy jointly determine the wage distribution in imperfectly competitive labor markets, and what were the quantitative contributions of each force to the dramatic decline in Brazilian wage inequality between 1998 and 2012?

Motivation. Brazil’s formal-sector wage inequality fell sharply over this period. Three candidate shocks are well-documented: (1) a large increase in educational attainment — the share of adults completing at least secondary school rose by 20 percentage points (a 68 percent increase) between 1998 and 2012; (2) labor demand shocks, primarily the commodities boom of the 2000s; and (3) a 93.7 percent (66.1 log point) real increase in the federal minimum wage. Existing frameworks analyze these shocks separately — competitive supply/demand models on one side and imperfectly competitive minimum wage models on the other — and therefore cannot detect interactions or jointly explain all observed patterns, including the novel finding that assortative matching between high-wage workers and high-wage establishments rose in 104 out of 151 microregions, a fact inconsistent with the predictions of leading minimum wage models.

Data. The paper uses the RAIS (Relação Anual de Informações Sociais), a confidential linked employer-employee dataset covering the Brazilian formal sector, together with Brazilian Census data for 1991, 2000, and 2010. Statistics are computed for 151 microregions (analogous to US commuting zones) with at least 15,000 workers in RAIS in both base years and at least 1,000 formal workers per educational group. The final sample covers 73 percent of the adult population. Firm wage premiums and assortative matching are measured via AKM two-way fixed effects regressions using the bias-corrected KSS (Kline, Saggio, Sølvsten 2018) estimator, run separately for each microregion and period on three-year panels.

Theoretical framework. The paper develops a unified general-equilibrium model featuring: (i) a task-based production function with distance-dependent complementarity between worker types; (ii) monopsony power arising from idiosyncratic worker preferences for firms, generating constant firm-level labor supply elasticity β (calibrated at 4, implying markdowns of 20 percent); (iii) heterogeneous firms differentiated by their production “blueprints” (the complexity of tasks they require), with blueprint shape parameterized as a Gamma distribution; and (iv) free firm entry, endogenous participation, and goods market general equilibrium with CES consumer preferences (elasticity σ). A key result is that firms with different blueprints exhibit different within-firm substitution patterns: worker types that are substitutes at low-skill, low-wage firms may be complements at high-skill, high-wage firms.

Estimation. A parsimonious parameterization is estimated by simultaneous-equation nonlinear least squares, targeting 26 endogenous outcomes per region (13 per period) including between- and within-group wage inequality, variance of establishment effects, covariance of worker and establishment effects, formal employment rates by education, and minimum wage bindingness. The model requires solving for equilibrium more than 15,000 times per optimization step (151 regions × 2 periods × 53 Jacobian columns). The elasticity of substitution between goods is estimated at σ = 8.36 (significantly above 1), and the aggregate labor supply parameter λ implies formal-sector elasticities of approximately 0.6–0.7 for college workers and around 1.1 for less-than-secondary workers. The model fits the data well, with R² above 0.5 for most targeted moments and perfect fit for the six moments used in the inversion procedure.

Main findings.

Demand shocks and the minimum wage are the primary drivers of falling inequality. In counterfactual simulations, the minimum wage alone (a 66.1 log point increase) reduces the variance of log wages by 0.13. Demand shocks reduce it by a further 0.18. Supply shocks (rising education) increase the variance by 0.04, leaving their net inequality-reducing contribution negligible.
Supply shocks increase assortative matching despite compressing within-firm skill premiums. Within-firm task reassignment would reduce the variance of log wages by 0.221 and the correlation between worker and establishment effects by 0.165, holding production levels and firm entry fixed. However, scale, entry, and price adjustments — driven by the large estimated σ = 8.36 > β + 1 = 5 — reallocate skilled labor toward high-wage, skill-intensive firms, counteracting within-firm compression and raising assortative matching by 0.189. These two channels largely offset each other.
Concurrent supply and demand changes attenuate minimum wage impacts by roughly half. When the minimum wage is the only shock, it would have reduced the variance of log wages by 0.13; in the presence of supply and demand changes, its incremental contribution is approximately 0.07. Minimum wage effects on sorting (which would reduce assortative matching when acting alone) disappear when accompanied by supply and demand transformations.
Minimum wage effects are concentrated in the bottom two productivity deciles. Wage effects for workers in productivity deciles three through ten from the minimum wage are approximately 1 percent or less once all channels are considered. Strong wage gains are concentrated at the bottom, primarily through the monopsony channel. The wage-posting channel (within-firm returns to skill) reduces wages for low- and middle-skill workers and raises them at the top two deciles due to the reallocation of low-skilled workers toward high-wage firms, which reduces those workers’ marginal products there.
Cross-firm differences in substitution patterns generate non-standard minimum wage spillovers. Conditional on the task demands of the firm employing them, a pair of worker types may be substitutes in low-skill firms and complements in high-skill firms. This firm-heterogeneity channel causes minimum wage impacts to be non-monotone across the productivity distribution, contrasting with the smooth inequality-reducing effects predicted by both competitive task-based models and frictional minimum wage models.

In depth

Q1. What is the novel empirical fact that motivates the unified framework?

A: Using KSS bias-corrected AKM decompositions performed separately for each of 151 microregions, the paper documents that assortative matching — measured as the correlation between worker and establishment fixed effects — rises in 104 out of 151 regions between 1998 and 2012. The covariance term accounts for less than 7 percent of the average decline in the variance of log wages. This finding is inconsistent with the leading imperfectly competitive minimum wage model (Engbom and Moser 2022), in which minimum wages reduce assortative matching. It is also inconsistent with purely competitive supply/demand models, which have no role for firm wage premiums or sorting. The divergence from prior national-level studies (which do not find rising sorting) is explained by the fact that national-level sorting conflates geographical sorting with supply-demand dynamics.

Q2. What is the key mechanism through which the task-based production function generates cross-firm differences in substitution patterns?

A: In the task-based production function, each firm assigns workers to tasks assortatively — lower types handle lower-complexity tasks, higher types handle higher-complexity tasks, with cutoff thresholds determined by the firm’s blueprint. When a firm has a blueprint concentrated in complex tasks (a high-skill, high-wage firm), adjacent worker types are more differentiated in the tasks they perform, making them complements. When a firm has a blueprint concentrated in simple tasks (a low-skill, low-wage firm), adjacent worker types are assigned to a narrow, similar range of tasks and are therefore closer substitutes. The elasticity of complementarity between any pair of worker types is thus endogenous, depending on which tasks the firm uses and, in the monopsony case, on the firm’s skill intensity — a prediction validated empirically using nonroutine cognitive task content data for Brazilian occupations.

Q3. Under what conditions can a positive supply shock (rising educational attainment) widen the aggregate skill wage premium rather than compress it?

A: The paper’s Proposition 4 and Corollary 2 show that a supply shock that increases the relative supply of skilled workers can widen the aggregate skill wage premium when the elasticity of substitution between goods (σ) exceeds the firm-level elasticity of labor supply plus one (β + 1). Intuitively, when σ is large, the reduction in prices for skill-intensive goods generated by the supply shock shifts consumption toward those goods, causing net entry of skill-intensive firms. If the gains in firm wage premiums earned by skilled workers reallocated to those firms outweigh the compression in within-firm productivity differentials, the aggregate skill premium can rise. This mechanism does not require non-convexities from endogenous innovation; it operates through imperfect competition and firm entry alone. In the estimated Brazilian model, σ = 8.36 substantially exceeds β + 1 = 5, so this condition holds, explaining why rising education increases rather than compresses assortative matching in the data.

Q4. How does the model generate positive employment effects from minimum wages, and how do these interact with reallocation?

A: In the monopsonistic baseline without a minimum wage, firms post wages below workers’ marginal revenue products, causing some workers to choose non-employment. A minimum wage increase raises posted wages at constrained firms, shifting some workers from non-employment (or home production) to formal employment, generating positive employment effects at the margin where the minimum wage binds. Simultaneously, minimum wages price out the least productive workers at low-wage firms (disemployment), while workers in the intermediate productivity range reallocate from low- to high-wage firms, because high-wage firms have higher revenue productivity and can profitably hire workers that low-wage firms can no longer afford. The net employment elasticity for the lowest productivity decile with respect to the log minimum wage is −0.61 (Table 7), while the mean wage for that decile rises substantially through the monopsony channel.

Q5. What are the three channels through which the minimum wage affects wages and employment in the model, and what does each channel contribute?

A: The paper decomposes minimum wage effects into three channels. Channel 1 (monopsony): mechanical wage increases, positive employment effects at firms where the minimum wage binds, disemployment of very low-productivity workers, and reallocation from low- to high-wage firms, holding posted wage schedules, prices, and entry fixed. This channel accounts for nearly all of the strong wage effects at the bottom two productivity deciles. Channel 2 (wage posting): firms reoptimize earnings schedules following changes in worker composition and marginal products induced by Channel 1, holding prices and entry fixed. This channel reduces wages for low- and middle-skill workers (productivity deciles 1–7) by approximately 0.01–0.02 log points and increases wages for top deciles (decile 9: +0.04, decile 10: +0.11), because reallocation of low-skill labor to high-wage firms lowers those workers’ marginal products there. Channel 3 (general equilibrium): firm entry and price responses. The fall in low-wage-firm profits causes entry of high-wage, skill-intensive firms, while the price of low-skill goods falls. General equilibrium effects generate modest positive wage effects for most workers but negative effects for very low-productivity workers due to reduced aggregate demand for low-skill labor.

Q6. Why do the minimum wage’s inequality-reducing effects diminish when accompanied by concurrent supply and demand changes?

A: The paper documents that, under concurrent supply and demand transformations, the minimum wage’s reduction of the variance of log wages is approximately 0.07, roughly half the 0.13 reduction it would achieve acting alone. The attenuation occurs through interactions: supply and demand shocks raise the average productivity level of the labor market and shift workers toward high-wage, skill-intensive firms. In this altered equilibrium, the minimum wage binds less tightly (or hits a different part of the distribution), and the reallocation effects of the minimum wage that would normally reduce assortative matching are offset by the sorting-increasing effects of supply and demand changes. The estimated model shows that interactions between the minimum wage and supply/demand changes (columns 6, 7, 8 of Table 5) are economically meaningful, something undetectable without a unified framework.

Q7. How does the model’s prediction regarding minimum wage spillovers differ from Engbom and Moser (2022), and what explains the difference?

A: Engbom and Moser (2022) find that the Brazilian minimum wage hike had significant wage effects extending far up the worker productivity distribution, while this paper’s model finds negligible effects (approximately 1 percent) beyond the bottom two productivity deciles. Two structural differences explain this divergence. First, Engbom and Moser (2022) assume perfect substitutability between worker types within firms, so a minimum wage increase at low-wage firms mechanically raises posted wages at all other firms to maintain relative competitiveness. In this paper’s framework, wage-posting responses at high-wage firms can be negative for low-skill workers because the inflow of reallocated low-skill workers reduces their marginal products — a channel absent under perfect substitution. Second, Engbom and Moser (2022) use a national model, allowing displaced low-skill workers to reallocate to top-productivity firms anywhere in the country, dampening disemployment; this paper’s local labor markets approach restricts reallocation to within-region boundaries, consistent with low rates of interregional migration documented for Brazil by Dix-Carneiro and Kovak (2017).

Q8. How are firm wage premiums generated in the model, and why do differences in physical productivity between firms not generate wage differentials?

A: Proposition 3 establishes that wage dispersion for similar workers across firms requires either (i) differences in blueprint shapes (firm heterogeneity in skill intensity) or (ii) differences in entry costs. Differences in physical productivity (z_g) or consumer taste parameters alone are insufficient, because with equal entry costs, differences in productivity lead to additional firm entry until the marginal revenue product of labor is equalized across firm types. Wage premiums proportional to entry costs arise because optimal firm creation requires larger-scale operation for higher-entry-cost firms, and hiring more workers forces those firms to post higher wages. Additionally, skill-intensive firms (firms with blueprints tilted toward complex tasks) pay relative wage premiums for the worker types they use most intensively, and if skill intensity and entry costs co-vary, all workers at high-skill firms may receive a wage premium.

Q9. How does the estimation procedure handle unobserved regional heterogeneity in labor demand?

A: Demand shocks are not directly observed; they are inferred as a residual from changes in targeted outcomes after accounting for observed supply (education shares from Census) and minimum wage changes. Five region-time-specific demand parameters — TFP (z), blueprint complexities (θ₁, θ₂), relative entry costs (F₂/F₁), and relative consumer preferences (γ₂/γ₁) — are modeled as linear functions of 1998 regional covariates (educational shares, agricultural share, manufacturing share, and initial minimum wage bindingness) with time-specific coefficients. This formulation allows unobserved demand shifters to correlate with initial educational levels, preventing incorrect attribution of demand-supply correlations to causal supply effects. Region-specific parameters (TFP in each period, education-group-specific formal employment shifters) are inverted exactly from six targeted moments within each region, eliminating incidental parameter bias.

Q10. What micro-level empirical validations does the paper conduct for the task-based model’s mechanisms?

A: The paper tests four micro-level predictions using nonroutine cognitive task content data for Brazilian occupations. First, skill-intensive firms have greater demand for complex tasks (consistent with Figure 1 of the model). Second, within firms, more skilled workers are assigned to more complex tasks (Lemma 1). Third, workers who move to more skill-intensive firms are assigned more complex tasks (Lemma 2, consistent with the monopsony model’s mismatch prediction). Fourth, wage gaps between high- and low-skill firms are larger for skilled workers (Proposition 3). The paper reports finding strong support for all four predictions in the data, lending credibility to the theoretical structure and quantitative results.

Key Concepts

Task-based production function (paper’s definition): A production function in which a firm produces output by assigning workers of different types to tasks indexed by complexity. The assignment is assortatively optimal: lower-type workers handle lower-complexity tasks, with unique threshold complexities separating adjacent worker types. The critical property is distance-dependent complementarity — any pair of worker types that are “close” in skill rank are substitutes, while pairs distant in skill rank are complements. This differs from CES production functions where the elasticity of complementarity is the same for all pairs; in the task-based version, substitutability depends on endogenous assignment and thus on the firm’s blueprint.

Blueprint (paper’s definition): A function b_g(x) that specifies the density of tasks of each complexity level x required to produce one unit of good g. It is the fundamental source of firm heterogeneity in the model: firms producing goods with blueprints tilted toward complex tasks are more skill-intensive, hire workers of higher average type, and pay higher wages. The paper parameterizes blueprints as Gamma distributions with shape parameter θ_g indexing average task complexity; firms with higher θ_g are more skill-intensive.

Firm wage premium (paper’s definition): The component of wages at a given establishment that accrues equally to all workers at that firm regardless of their type, measured as the establishment fixed effect ψ_j in AKM two-way fixed effects regressions. In this model, firm wage premiums arise from heterogeneity in blueprints (skill intensity) and entry costs, not from differences in TFP or consumer tastes. Under monopsony, firms with higher entry costs must operate at larger scale and post higher wages; blueprint heterogeneity generates differential wage premiums by skill type.

Sorting / assortative matching (paper’s definition): The correlation between the worker fixed effect (ν_i,r capturing worker skill) and the establishment fixed effect (ψ_j capturing firm wage premium) in the AKM decomposition, measured as Cov(ν_i,r, ψ_{J(i,r,τ)} | r). In this paper’s framework, sorting arises because firms with blueprints demanding complex tasks (high-wage firms) have a comparative advantage in employing high-skill workers; labor market sorting can therefore change over time due to supply, demand, or minimum wage shocks, even without changes in search frictions.

Monopsony power / markdown (paper’s definition): Arising from idiosyncratic worker preferences for firms (modeled as a nested logit), firms face upward-sloping labor supply curves with constant firm-level elasticity β. Optimal posted wages equal a constant markdown β/(β+1) of the marginal revenue product of labor, set to β = 4 (implying a 20 percent markdown). The macro elasticity of formal sector labor supply is governed by a separate parameter λ, estimated from the data, yielding aggregate formal-sector supply elasticities of approximately 0.6–0.7 for college workers and around 1.1 for less-educated workers.

Wage posting responses (paper’s definition): The second channel of minimum wage effects, in which firms reoptimize their entire earnings schedule following the wage-composition changes induced by the minimum wage’s mechanical and reallocation effects (Channel 1), while keeping goods prices and firm entry fixed. Because task-based production functions are concave, changes in factor proportions (due to reallocation of low-skill workers to high-wage firms) alter marginal products of all worker types within those firms, causing firms to adjust all posted wages — not just those directly constrained by the minimum wage.

Distance-dependent complementarity (paper’s definition): The property, proven as a Corollary to Proposition 1, that for a fixed worker type h, the partial elasticity of complementarity between h and any other type h’ is strictly increasing in h’ for h’ ≥ h (more distant high types are stronger complements) and strictly decreasing in h’ for h’ ≤ h (more distant low types are weaker substitutes / stronger complements). This pattern results from the division of labor: adding a very different worker type allows specialization gains that do not arise when adding similar-type workers competing for the same tasks.

Take the Goods and Run: Contracting Frictions and Market Power in Supply Chains

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

Overview

This paper studies the efficiency of self-enforced relational agreements in manufacturing supply chains when sellers have market power and contracts cannot be externally enforced. The setting is Ecuador, an upper-middle-income country with slow commercial courts (debt enforcement takes around two years even after a 2016 reform) and highly concentrated manufacturing markets (average Herfindahl-Hirschman Index of 0.6 for 6-digit economic codes, well above the 0.25 threshold used by the US Department of Justice to identify highly concentrated markets).

Research question. How efficiently do long-term trade relationships operate, period by period, when the seller can price discriminate and the buyer can opportunistically default on trade-credit debt? Does seller market power worsen or mitigate enforcement-driven inefficiencies?

Data. The paper uses three Ecuadorian government administrative databases: (1) an electronic invoicing (EI) system covering all sales of 49 large manufacturing firms in textiles, pharmaceuticals, and cement products for 2016–2017, providing product-level unit prices, quantities, and payment method for each buyer-seller pair (median seller has 600 buyers); (2) the universe of firm-to-firm VAT transactions from 2008–2015, used to measure relationship age (censored at 9 years); and (3) annual financial statements providing variable costs to proxy marginal cost.

Model. The author develops a dynamic contracting model that embeds non-linear pricing with heterogeneous buyers (following Jullien 2000 and Attanasio-Pastorino 2020) into an infinitely repeated game with limited enforcement (following Martimort et al. 2017). The seller holds all bargaining power, commits to a long-term menu of prices and quantities, and finances every transaction through trade-credit. The buyer has a privately observed, fully persistent type (willingness to pay) and can opportunistically default after delivery — “take the goods and run” — at the cost of losing the future relationship. The seller uses the value of the ongoing relationship as the enforcement instrument. The paper solves the seller’s profit-maximization problem using a recursive Lagrangian approach, yielding a modified virtual-surplus condition that governs optimal quantity allocations as a function of current and past limited-enforcement Lagrange multipliers (LE multipliers).

Six motivating empirical facts documented in the data: (1) New buyers are ~35% of pairs but account for only ~10% of total trade; relationships lasting nine or more years are less than 10% of pairs but generate over 30% of trade. (2) Trade-credit is used in approximately 65% of transactions in the first year and 70–75% in older relationships. (3) Quantities increase as relationships age. (4) A 10% increase in quantity purchased is associated on average with a 2% decrease in unit price (quantity discounts). (5) Conditional on quantity, older buyers pay up to 3% less; these price discounts appear only in trade-credit transactions, not in pay-in-advance transactions. (6) Approximately 40% of new relationships survive one additional year, 60% of relationships aged 1–3 years survive, and more than 75% of relationships aged four or more years survive.

Key structural finding. Almost all new relationships have binding enforcement constraints. The estimated LE multiplier equals 1 (unconstrained) only for the top 1% of pairs at tenure 0. As relationships age, the constraint relaxes and quantities are backloaded — consistent with the seller making promises of higher future trade to incentivize current debt repayment.

Efficiency results. New relationships operate at approximately 30% of the frictionless (first-best) surplus level. Efficiency rises to 60% at tenure 2, 75% at tenure 4, and over 80% at tenure 5. Aggregating across buyers weighted by efficient quantities: only 5% of sellers trade efficiently with new buyers, rising to 70% by tenure 2 and 84% in the long term. By sector, 68% of textiles, 88% of pharmaceutical, and 95% of cement-product sellers reach efficient aggregate output by tenure 5. Sellers capture approximately 80% of generated surplus; the median buyer captures around 25%, and the smallest buyers may capture less than 10%.

Counterfactuals reveal a second-best interaction. Fixing enforcement alone (Counterfactual a: non-linear pricing with perfect enforcement) raises surplus for 75% of buyers in the early tenures but reduces surplus for essentially all buyers in later tenures, because the threat of buyer default was the force compelling the seller to promise growing quantities over time. Fixing market power alone (Counterfactual b: uniform pricing with limited enforcement) collapses surplus to 0–40% of the baseline because the seller can no longer tailor dynamic incentives to each buyer’s enforcement constraint, causing a large share of buyers to be excluded from trade. Addressing both frictions simultaneously (Counterfactual c: uniform pricing with perfect enforcement) raises surplus for most buyers in early tenures but remains welfare-reducing for high types in later tenures; the aggregate effect depends critically on weighting: positive (~40% gain) when weighted by number of buyers, negative (surplus falls to ~58% of baseline) when weighted by quantities.

In depth

Q1. What is the central theoretical mechanism by which limited enforcement leads to backloading of quantities in the model?

The buyer can default after delivery because payment is post-delivery (trade-credit). To prevent this, the seller must ensure the buyer’s discounted future net returns exceed the current payment obligation. This creates a forward-looking enforcement constraint: the seller must credibly promise sufficiently large future quantities at lower prices. As a result, current quantities are distorted downward (the seller delays granting full trade volumes), but quantities increase over time as past promises become binding promise-keeping constraints. The optimal contract is therefore non-stationary: total surplus generated and the buyer’s net return both increase over time even without efficiency gains in production.

Q2. How does seller market power interact with enforcement frictions — does it worsen or improve efficiency relative to a perfect-enforcement benchmark?

The paper’s key finding is that market power and enforcement constraints act as partially offsetting frictions. Seller market power creates downward quantity distortions (the seller restricts supply to extract rents). Limited enforcement, however, compels the seller to promise growing quantities to prevent buyer default, which counteracts the market-power distortion. Thus, in older relationships, the enforcement constraint effectively disciplines the seller’s rent-extraction incentives, producing trade levels that approach the frictionless first-best. This is an instance of the theory of second-best: each friction partially offsets the other, so removing only one friction can reduce total welfare.

Q3. What are the six motivating empirical facts and why do they rule out standard alternative explanations?

The six facts are: (1) heavy concentration of trade in long-established relationships; (2) widespread trade-credit even in new relationships; (3) quantities increase with relationship age; (4) quantity discounts within any age cohort; (5) older buyers pay lower prices conditional on quantity; (6) survival rates increase with quantity and relationship age. Alternative models — efficiency gains, learning, demand assurance, and supply-side enforcement issues — cannot jointly account for all six patterns under realistic assumptions. Critically, Fact 5 holds only in trade-credit transactions and not in pay-in-advance transactions, which supports limited enforcement (not learning or demand assurance) as the underlying mechanism.

Q4. How is the model identified from cross-sectional data on prices and quantities for a single seller?

Identification exploits two sources of variation. First, because the seller offers non-linear price menus that induce type revelation, cross-sectional variation in prices and quantities across buyers reveals their underlying private types. Second, for the highest-type buyer at tenure 0, the cumulative LE multiplier equals 1 by construction, so the gap between the observed marginal price and marginal cost directly reveals the current enforcement multiplier for that type; cross-sectional variation across high-type buyers then identifies the elasticity parameter β. Once β is pinned down, the multipliers for all types and tenures are recovered as unique solutions to ordinary differential equations, and buyer types are recovered semi-parametrically. The approach requires only cross-sectional data from one seller per year — no panel of individual buyers is needed.

The paper finds a wedge between the buyer’s marginal product of capital (MPK) and the transaction price of 40% for the median new relationship and 34% for the median tenure-5 relationship. These wedges are smaller than the 80% gaps estimated for Indian firms by Banerjee and Duflo (2014), and larger than the average 6% gap calculated by Blouin and Macchiavello (2019) in the international coffee market. They are also much smaller than the 300–500% gaps estimated for Mexican micro-enterprises by McKenzie and Woodruff (2008), which is consistent with the buyers in this sample being substantially larger (median yearly sales of USD 200,000).

Q6. What does Counterfactual (a) — perfect enforcement with non-linear pricing — reveal about the intertemporal trade-off?

Counterfactual (a) shows massive short-run gains for low and middle types: surplus at tenure 0 increases to 1,508% and 628% of baseline for the bottom 10th and median buyer percentile groups respectively. However, for higher types (top 25%), perfect enforcement is immediately welfare-reducing because these buyers are already trading near efficiently and the seller loses the incentive to grow quantities over time once default is not a threat. By tenure 3 and beyond, perfect enforcement reduces surplus for essentially all buyers. The aggregate effect is negative because high-type buyers, who trade larger volumes, bear larger losses in later tenures when those tenures are weighted by quantity.

Q7. Why does uniform pricing with limited enforcement (Counterfactual b) perform so poorly?

Under uniform pricing, the seller cannot tailor the dynamic contract to each buyer’s individual enforcement constraint. Without individualized price-quantity menus, many buyers cannot credibly commit to repaying their debts — because the seller cannot offer a sufficiently personalized future stream of benefits — and are thus excluded from trade entirely. For instance, at tenure 0, 95.8% of the bottom-decile buyers and 64% of median buyers are excluded. The aggregate surplus under this regime reaches only 3–68% of baseline across different tenures and percentile groups. This implies that the seller’s price discrimination ability, while generating informational rents, also serves a second purpose: it allows each buyer’s specific enforcement constraint to be satisfied, enabling trade that would otherwise be infeasible.

Q8. What do the sector-level results suggest about the generalizability of the main findings?

All six motivating empirical facts are consistent across the three industries studied (textiles, pharmaceuticals, and cement products). The efficiency patterns also appear in all three sectors, though with heterogeneous speeds of convergence. Pharmaceutical and cement-product sellers converge faster (88% and 95% efficient at tenure 5) than textiles sellers (68% efficient at tenure 5). The finding that relationships approach efficiency in the medium and long term holds in every industry analyzed, suggesting that the underlying mechanisms — limited enforcement and seller market power — are broadly operative rather than sector-specific.

Q9. How does the paper establish that the standard non-linear pricing model without enforcement constraints does not explain the data?

The paper tests whether the LE multiplier at tenure 0 (G0) is statistically distinguishable from the null hypothesis of a standard non-linear pricing model (which would imply G0 = 1 for all buyers). Based on t-statistics from the estimated distribution of G0 across seller-year markets, the null of a standard model is rejected for 86% of the markets (seller-years) in the sample. Additionally, the dynamic price discounts conditional on quantity — which are the key signature of backloading — appear only in trade-credit transactions and not in pay-in-advance ones, ruling out alternative explanations such as learning about buyer quality or demand assurance.

Q10. What are the model’s main limitations and how do they affect the counterfactual conclusions?

The author flags three principal limitations. First, buyer types are assumed fully persistent due to data constraints (only two years of invoice-level data); a Markov type structure would require longer buyer-level panels. Second, the identification strategy relies on the seller’s first-order optimality conditions and cannot recover counterfactual dynamic quantities — the counterfactuals are therefore static comparisons of per-period surplus rather than full dynamic simulations. Third, if buyers have unobserved outside options, the counterfactual efficiency results may be biased, though the direction of the bias is uncertain and depends on the distribution of types and the curvature of the return function.

Key Concepts

Limited enforcement constraint (LE-B). The paper’s central friction: because payment is post-delivery, the buyer can default and keep the goods. In the model, the contract is “default-free” only if the buyer’s post-delivery payment is weakly less than the discounted value of all future truthful net returns. The constraint is binding when this condition is tight — the buyer is on the margin of defaulting. When binding, it forces the seller to reduce current tariffs and quantities (to lower the attractiveness of default) while promising higher future quantities (to raise the continuation value).

Limited enforcement Lagrange multiplier (LE multiplier), Gt(α). The shadow price on the buyer’s enforcement constraint at tenure t for a buyer at quantile α. It takes values in [0,1], equals 1 only when the enforcement constraint is slack (unconstrained buyer), and equals zero for the lowest type at all tenures. In the paper’s framework, the entire trajectory of Gt(α) across tenures encodes the history of past enforcement promises and is the key object identified and estimated to recover the dynamic distortions.

Backloading. The equilibrium property whereby the total surplus generated by the relationship and the buyer’s net return both increase over time. The seller achieves this by initially restricting quantities and promising growing future allocations as an enforcement device. Formally, quantities increase over time if and only if enforcement constraints are relaxed (gt+1(q) ≤ gt(q)).

Modified virtual surplus. The object that replaces ordinary virtual surplus (which appears in standard non-linear pricing models) in the seller’s first-order condition. It augments standard virtual surplus by adding shadow costs for current binding enforcement constraints and subtracting corrections for past enforcement promises. Optimal quantity allocations are determined by an inverse-markup rule applied to this modified virtual surplus.

Relational agreement / self-enforced relational contract. An informal long-term agreement sustained purely through the repeated interaction between the parties, without access to third-party (court) enforcement. In this paper’s setting, the seller disciplines the buyer’s opportunism exclusively through the threat of relationship termination; no legal recourse is available or used in equilibrium.

Quantity discounts (non-linear pricing / wholesale quantity discounts). Price schedules under which the unit price decreases with the quantity purchased, offered by a seller with market power. In the paper’s empirical setting, a 10% increase in quantity is associated with a 2% decrease in unit price, and these discounts appear at every relationship age. The model generates them as the incentive-compatibility requirement that ensures higher-type buyers truthfully reveal their demand.

Trade-credit. Seller financing of the transaction, in which goods are delivered before payment is received. In the Ecuadorian data, approximately 65% of first-year purchases and 70–75% of purchases in mature relationships are conducted via trade-credit. Because the seller bears the full cost of buyer default, trade-credit is the financial arrangement that gives rise to the limited enforcement constraint studied in the paper.

Second-best interaction of frictions. The paper’s counterfactual finding that removing a single friction (either enforcement or market power) can reduce total welfare when both frictions are present simultaneously. This occurs because the two frictions partially offset each other: enforcement constraints discipline the seller’s monopoly distortions, and market power allows the seller to price-discriminate in ways that enable enforcement in the first place. Addressing both frictions simultaneously can improve welfare, consistent with the Lipsey-Lancaster theory of second-best.

Talent Hoarding in Organizations

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

This paper provides the first empirical evidence of talent hoarding in organizations — the practice whereby managers deliberately suppress workers’ internal mobility to retain productive team members, thereby serving their own performance-based compensation interests at the expense of firm-wide talent allocation. The research question is whether managers with misaligned incentives hoard talent, how this can be measured, and what consequences it have for worker career outcomes and organizational efficiency.

The study uses personnel records from a large German manufacturing firm with over 200,000 employees worldwide, focused on more than 30,000 white-collar and management employees in Germany, covering over 300,000 employee-by-quarter observations from 2015 to 2018. This is supplemented by a manager survey (62% response rate, over 3,000 responses) and an employee survey (50% response rate, over 15,000 responses), plus the universe of internal job application and hiring data covering over 16,000 job openings and over 200,000 applicants.

The conceptual framework formalizes talent hoarding as a moral hazard problem: managers observe worker productivity and are compensated based on team performance, but are tasked with identifying and developing talent for promotion. When a high-productivity worker leaves, team productivity falls. The framework predicts that hoarding intensity increases with worker productivity, team vulnerability to departures (smaller teams), and manager-level hoarding incentives (performance-related pay, low talent visibility).

The key administrative measure of hoarding is the systematic gap between managers’ private performance ratings (not shared outside the team) and public potential ratings (widely circulated within the firm). Managers who suppress potential ratings relative to what would be predicted given worker performance are interpreted as strategically reducing worker visibility. Managers with a 1 percentage point higher share of performance-related pay are 0.19 percentage points more likely to hoard talent; a one-person increase in team size reduces hoarding probability by 1.3 percentage points; and managers in low-visibility functional areas are 4.0 percentage points more likely to hoard. Survey-based hoarding measures yield directionally identical patterns.

To identify causal effects on workers, the paper exploits quasi-random manager rotations. When a manager learns they will move to a different team — typically two to three quarters before the actual transition — their hoarding incentive ceases. This creates a temporary window of reduced hoarding. During this window, worker application rates increase by 2.3 percentage points, representing a 78% increase over the baseline application rate of 2.9%. An event study confirms flat pre-trends prior to the announcement period, supporting the identifying assumption.

Using manager rotations as an instrument for worker applications, marginal applicants — those induced to apply only by the manager rotation — face a 49.1% likelihood of receiving a new position, compared to an average hiring likelihood of 27.6%. This positive selection implies that many deterred applicants would have been successful and that talent hoarding meaningfully degrades the quality of the internal applicant pool. Gender analysis reveals that women are 22% more likely to rely on manager career guidance and 26% more likely to prioritize preserving a good manager relationship. Marginal female applicants are more positively selected on education, past performance, and hiring probability for higher-level positions. The counterfactual reduction in the gender pay gap from eliminating talent hoarding is estimated at 86%.

Scope conditions: the firm is a large European manufacturer with long average tenures (13 years), an application-based internal labor market, and centralized online job portal. Results apply most directly to white-collar and management employees in Germany. External validity is supported by comparisons to German workforce surveys and by the fact that 83% of top publicly listed German companies and half of 665 global organizations in industry surveys report talent hoarding as a significant organizational friction.

Q: How is talent hoarding formally defined in this paper? A: Talent hoarding is defined as actions taken by managers that lower the likelihood that a worker applies for and receives a promotion or any internal transfer outside the team. In the formal framework, a manager chooses hoarding intensity β ≥ 0, where β > 0 reduces the equilibrium probability that a worker gets promoted. The definition encompasses all forms of managerial action that reduce worker departure probability, including suppressing visibility, restricting access to trainings, explicit discouragement, and threats.

Q: Why do managers have an incentive to hoard talent? A: Managers are compensated based on team performance, so losing a high-productivity worker (whose replacement is a random draw from an outside distribution with expected productivity ᾱ) reduces team performance and thus manager compensation. The framework shows that when a worker’s productivity αi exceeds the expected productivity of an outside hire ᾱ, the manager optimally sets β* > 0. The cost of hoarding (parameterized as φm) is convex and varies across managers, capturing altruism, reputation risk, or detection probability.

Q: What share of managers in the survey self-report talent hoarding? A: 75% of managers reported that they sometimes find themselves in situations where they need to dissuade a team member from exploring opportunities in another department due to immediate team needs or performance goals. Additionally, 45% cite the risk of losing talent as a reason not to invest in employee career development, and 66% cite the need to prioritize short-term performance targets over long-term employee development.

Q: How are misaligned incentives documented in the manager survey? A: 55% of managers agree or strongly agree that talent development entails a conflict of interest because more developed workers are more likely to leave the team. While 96% believe their direct intervention has a large impact on workers’ career development, only 36% perceive that impact to be valued by the firm as much as team performance impact. Similarly, 87% say talent development is a high-impact area for the firm, but only 40% believe a track record in talent development matters for their own compensation and promotion.

Q: How is the administrative measure of talent hoarding constructed? A: The measure is the residual from an OLS regression of a worker’s potential rating (a public signal of promotion readiness, widely circulated within the firm) on their performance rating (a private signal of current task performance, not shared outside the team) and worker characteristics including age, education, gender, and tenure. The manager-level measure is the average of these residuals across all workers and quarters under that manager. Managers in the top tercile (mean deviation above 0.1036) are classified as hoarding-prone.

Q: Does the hoarding measure respond to the incentive proxies as predicted by the framework? A: Yes. A 1 percentage point higher share of performance-related compensation is associated with a 0.19 percentage point increase in the probability of being classified as hoarding-prone (p = 0.000), corresponding to a 13 percentage point difference between the 90th and 10th percentiles of the financial incentive distribution. A one-person increase in team size reduces hoarding probability by 1.3 percentage points (p = 0.000), again a 13 percentage point difference across percentiles. Managers in low-visibility functional areas are 4.0 percentage points more likely to hoard (p = 0.002) relative to high-visibility areas.

Q: Is the training-based hoarding measure consistent with the potential-rating measure? A: Yes. A complementary measure based on managers restricting worker access to high-visibility in-person trainings yields nearly identical patterns: a 1 percentage point increase in performance-related pay increases hoarding probability by 0.20 percentage points (p = 0.000); a one-person increase in team size reduces it by 1.4 percentage points (p = 0.000); low-visibility areas increase hoarding by 2.98 percentage points (p = 0.021). The direction and economic magnitudes are highly similar across both administrative measures and the survey-based measures.

Q: How are manager rotations used to identify causal effects on workers? A: When a manager learns they will move to a different position — typically two to three quarters before the rotation — their incentive to hoard workers on their current team ceases. This creates a quasi-random window of reduced talent hoarding for workers on that team. An event study with worker and quarter fixed effects shows flat pre-trends in application rates beyond three quarters before the rotation, consistent with the identifying assumption that managers do not yet know about their rotation in that earlier window. Balance tests confirm workers exposed to rotations are observationally similar on demographics and past performance to non-exposed workers.

Q: How large is the effect of manager rotations on worker applications? A: Manager rotations increase worker application rates by 2.3 percentage points in the quarter of rotation, representing a 78% increase over the baseline application rate of 2.9%. The effect is transitory: application rates return to baseline within one quarter after the new manager settles in. The effect is not driven by managers taking subordinates with them (97% of applications are to positions outside both the current team and the manager’s new team).

Q: Does the rotation effect vary with predicted hoarding intensity as the framework requires? A: Yes. The rotation effect is larger for workers with higher productivity, those whose replacement would be costlier (consistent with the prediction that workers harder to replace face more hoarding), and those working under managers with lower utility costs of hoarding. The paper tests these cross-sectional predictions using continuous interactions between the rotation indicator and standardized proxies for hoarding intensity, and all patterns are consistent with the talent hoarding mechanism rather than alternative explanations.

Q: How successful would the deterred applicants have been? A: Marginal applicants — those induced to apply by the manager rotation who would not otherwise have applied, identified via IV assumptions — face a hiring probability of 49.1%, compared to the average hiring likelihood of 27.6% across all applicants. This large positive selection implies that a substantial share of deterred applicants would have been successful, and that talent hoarding meaningfully degrades the quality and quantity of the firm’s internal applicant pool and the firm’s ability to promote high-productivity workers.

Q: Does talent hoarding have differential effects by gender? A: Yes. Women are 22% more likely to place high value on preserving a good relationship with their manager and 26% more likely to rely on manager career guidance when making career decisions. Consistent with this, marginal female applicants are more positively selected on educational qualifications, past performance, and hiring probability for higher-level positions than marginal male applicants. When comparing potential earnings outcomes, both men and women would earn more in the absence of talent hoarding, but the larger earnings gains for women imply a counterfactual reduction in the gender pay gap of 86%.

Q: What evidence supports external validity of the findings? A: The firm’s employee demographics closely match those of large manufacturing firms in the German BiBB workforce survey across gender, age, citizenship, and marital status. The firm’s internal labor market design is standard for large German firms, where 83% of top publicly listed companies cite talent hoarding as a key organizational friction. Industry surveys also report that half of 665 global organizations report managers hoarding talent by discouraging worker mobility, and talent hoarding occurs through many of the same behaviors documented in this study.

Q: How does the paper rule out confounding mechanisms for the rotation effect? A: The paper tests and rules out several alternatives: worker-manager specific match effects (the effect does not depend on characteristics of the incoming or outgoing manager); finite project timelines driving a rush to apply; and workers being recruited by managers to their new teams (97% of applications are outside the current team and not to the manager’s new team). Balance tests show workers exposed to rotations are observationally similar to non-exposed workers, and event studies confirm absence of pre-trends in team-level outcomes including absenteeism.

Q: What are the policy implications of the findings? A: The findings suggest firms forgo productivity gains when hoarded workers are not allocated to positions where they would be most productive. Potential organizational responses include monitoring or rewarding managers for promoting talent, reducing performance-related pay tied to team composition, or structuring career development activities in ways that cannot easily be suppressed by individual managers. The paper notes that firms generally do not compensate managers for promoting workers, partly due to practical difficulties of such contracts, and that the misalignment between what managers believe benefits the firm and what is recognized in their own compensation is particularly pronounced for talent development relative to all other managerial responsibilities.

Talent hoarding: Actions taken by managers that lower the likelihood that a worker applies for and receives a promotion or internal transfer outside the team, driven by managers’ incentive to retain productive workers to protect team performance and manager compensation. Distinct from mere neglect — it is strategic and deliberate.

Potential rating: A public signal of a worker’s future potential for higher-level positions, assigned by the direct supervisor and widely circulated within the firm (e.g., via HR lists of high-potential workers); distinguished from performance ratings by its visibility outside the worker’s current team, making it a lever for strategic manipulation by hoarding managers.

Performance rating: A private, task-specific signal of a worker’s past performance in their current position, not shared with other units in the firm; used as the baseline against which potential ratings are compared in the paper’s administrative hoarding measure.

Visibility suppression (hoarding measure): The manager-level average residual from a regression of workers’ potential ratings on their performance ratings and worker characteristics; a positive average residual indicates the manager systematically assigns lower potential ratings than predicted, suppressing worker visibility outside the team in a manner consistent with strategic talent hoarding.

Manager rotation: An event in which a manager leaves their current team for a different internal position within the firm, temporarily eliminating their hoarding incentive for current team workers and creating the paper’s quasi-experimental source of variation in hoarding exposure.

Marginal applicant: In the IV framework, a worker who applies for an internal position only because their manager is rotating and would not have applied otherwise; estimated via complier analysis (Abadie 2003) and used to characterize the counterfactual quality and hiring probability of workers deterred by talent hoarding.

Utility cost of hoarding (φm): A manager-level parameter capturing the convex private cost to a manager of engaging in talent hoarding; may reflect altruism, detection risk, or reputational consequences; managers with lower φm hoard more intensively, and variation in φm is proxied empirically by performance-related pay, team size, and functional-area talent visibility.

Temporary Layoffs, Loss-of-Recall, and Cyclical Unemployment Dynamics

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

This paper measures and models the role of temporary layoffs (TL) in cyclical unemployment dynamics, motivating the analysis by the extraordinary surge in temporary layoffs at the onset of the pandemic recession — roughly 15% of employed workers moved to temporary-layoff status from March to April 2020. The paper documents two opposing effects of temporary layoffs on total unemployment: a stabilizing direct effect (workers on TL return to employment rapidly via recall) and a destabilizing indirect effect through “loss-of-recall” — workers initially on temporary layoff who fail to be recalled and instead transition to jobless unemployment (JL), inheriting that state’s far lower reemployment probability. A new recursive accumulation method is used to construct a time series of the stock of workers in jobless unemployment whose most recent exit from employment was to temporary-layoff status (JL-from-TL); this stock has a standard deviation 16 times that of GDP and 2 times that of total unemployment, and is a high-correlation indicator of labor market slack. A search-and-matching model with staggered Nash wage bargaining, endogenous layoff thresholds, and separate recall and new-hire channels replicates the pre-pandemic cyclical behavior of TL and JL flows. Applying the model to the pandemic recession, the paper finds that the Paycheck Protection Program (PPP) reduced employment shortfalls by roughly 2 percentage points at peak, primarily by dampening loss-of-recall — the program’s forgivable loan structure reduced firms’ incentive to permanently separate workers who had been placed on temporary layoff.

Summary of a published paper based on the NBER working paper full text (w30134), AI-assisted, pending human review. See the linked original for the authoritative claims and full conditions.

Layer 1: Overview

Gertler, Huckfeldt, and Trigari study two distinct features of temporary layoffs in aggregate unemployment dynamics: the well-documented stabilizing role of recall hiring, and a less-studied destabilizing mechanism they term “loss-of-recall” — the countercyclical flow of workers from temporary-layoff unemployment into jobless unemployment. Using monthly CPS data from 1979 through the pandemic period, they construct a four-state Markov transition matrix (employment, TL unemployment, JL unemployment, inactivity) and develop a novel recursive method to track the accumulated stock of jobless unemployed workers whose most recent employment exit was via temporary layoff (JL-from-TL). This stock is small on average (roughly 40% of the average TL stock) but highly volatile — its standard deviation is 16 times GDP and twice total unemployment — and strongly co-moves with total unemployment (correlation 0.93) and the vacancy-unemployment ratio (0.83). Across historical recessions: TL unemployment contributed 36.1% of the increase in total unemployment during the 1980s recessions (25.1% direct, 11.0% indirect via loss-of-recall); 17.2% during the Great Recession (8.7% direct, 8.5% indirect — nearly equal); and 98% during the pandemic recession (almost entirely direct, because PPP dampened loss-of-recall). The structural model — DMP with staggered multiperiod Nash wage bargaining, firm-specific overhead cost shocks that generate endogenous exit and temporary layoffs, and separate hiring and recall margins — captures pre-pandemic dynamics and shows that loss-of-recall amplifies unemployment persistence following recessionary TFP shocks. In the pandemic recession application, the PPP counterfactual finds that without PPP: peak unemployment would have been roughly 2 percentage points higher; jobless unemployment would have peaked at 7.0% versus 5.9% in the PPP scenario; and cumulative TL-to-JL flows would have been roughly double, amounting to 47.4% of what they would otherwise have been.

In depth

Q1. What distinguishes temporary-layoff unemployment from jobless unemployment in the data, and why does the distinction matter for cyclical dynamics?

Temporary-layoff unemployment (TL) is the state in which a CPS respondent indicates an expectation of recall — either a specific return date or a stated expectation of recall within six months — while jobless unemployment (JL) is unemployment without such an expectation; the two states have starkly different reemployment probabilities, with TL workers returning to employment at substantially higher rates than JL workers, making the composition of total unemployment — not just its level — a key determinant of unemployment persistence. In the Markov transition matrix estimated from CPS data 1979-2019 (Table 2), TL is a transient state: workers on TL transition to employment at a far higher rate than workers in JL, reflecting the attached recall relationship. The stock of TL unemployment is consequently small — averaging roughly one-eighth of total unemployment — even though TL separations account for roughly one-third of all separations from employment to unemployment. The distinction matters for aggregate dynamics because a recessionary increase in TL generates both a direct, relatively transient component (elevated TL stock) and an indirect, more persistent component (heightened loss-of-recall feeding into JL stock). Standard two-state unemployment models that lump TL and JL together miss the indirect channel entirely, understating both the volatility and persistence of total unemployment in the presence of countercyclical loss-of-recall.

Q2. What is the recursive accumulation method for estimating JL-from-TL, and what does it reveal about the indirect contribution of temporary layoffs?

The paper proposes a novel method to estimate the time series stock of jobless unemployed workers whose most recent employment exit was through temporary-layoff unemployment — the JL-from-TL stock — by propagating forward through the Markov transition matrix each cohort of workers who enter TL from employment, tracking the fraction that survive in any unemployment state without returning to employment, and summing across all past cohorts. Formally, if $x_{t-m,t}$ denotes the distribution of workers at time $t$ whose last exit from employment was to TL at time $t-m$, then $x_{t-m,t} = \tilde{P}t x{t-m,t-1}$ where $\tilde{P}t$ is a modified transition matrix, and the JL-from-TL stock is $u^{JL,TL}t = \sum{j=0}^{T} e’{JL} x_{t-j-1,t}$. The method requires only the Markov transition matrix — no individual-level panel data — and extends the Shimer (2012) / Elsby-Hobijn-Sahin (2015) variance decomposition approach to level decompositions. Applied to CPS data, the JL-from-TL stock has a standard deviation 16 times that of GDP (versus 2 times for TL itself) and a correlation of 0.93 with total unemployment — substantially higher than the 0.83 correlation of the vacancy-unemployment ratio with total unemployment. The large relative volatility reflects that the JL-from-TL stock compounds both the volatility of TL separations and the cyclical variation in the TL-to-JL transition probability (loss-of-recall); both components are countercyclical, so they co-amplify in recessions.

Q3. How does the paper’s structural model generate endogenous temporary versus permanent layoffs and a procyclical recall probability?

Temporary layoffs and permanent exits arise endogenously from two cost shocks in the model: an employee-specific cost shock (ϑ) and a firm-specific overhead shock (γ), with thresholds ϑ and γ determined by firm optimization; workers whose idiosyncratic cost exceeds ϑ* are placed on temporary layoff (retaining recall rights), while firms whose overhead shock exceeds γ* exit, converting their TL workers to jobless unemployment.** The framework is a modified DMP model with staggered Nash wage bargaining (following Gertler-Trigari 2009), where firms can expand their workforce either by recalling workers from TL unemployment or by hiring new workers from JL unemployment, with separate quadratic adjustment costs for each margin ($\kappa$ for new hires, $\kappa_r$ for recalls). The recall elasticity exceeds the new-hire elasticity, consistent with the lower cost of re-integrating previously attached workers. Recall hiring (xr) and new hiring (x) are both driven by the discounted value of a worker to the firm, J(w,s), but respond with different sensitivities governed by their respective adjustment cost parameters. The TL-to-JL (loss-of-recall) flow is endogenous and driven by firm exit: when the overhead shock γ exceeds γ*(w,s), the firm exits and its TL workers lose their recall option, converting to JL unemployment. Because γ* rises in bad times (higher firm insolvency), loss-of-recall is countercyclical, matching the data pattern. An exogenous loss-of-recall probability $(1-\rho_r)$ is also included to capture TL-to-JL flows that occur even when the firm survives (e.g., firm restructuring or expiration of recall expectations), and this parameter is calibrated to long-run flow moments.

Q4. What does the calibrated model reveal about the amplification role of loss-of-recall, and how is this quantified?

A counterfactual exercise that sets the TL-to-JL transition probability to zero (shutting off loss-of-recall) shows that total unemployment peaks earlier and at a lower level following a recessionary TFP shock, and that unemployment displays markedly less persistence — revealing loss-of-recall as an important amplification mechanism by which a recessionary increase in temporary layoffs can generate persistently higher total unemployment. The model is calibrated to monthly frequency with 16 parameters: 9 assigned externally (β=0.991^{1/3}, δ=0.025^{3}, α=1/3, standard AR(1) TFP parameters, matching function elasticity σ=0.5, bargaining power η=0.5, λ=8/9 targeting quarterly wage adjustment frequency), and 7 calibrated to long-run flow moments and business cycle volatility moments (Table 8-9). The calibrated model captures the cyclical volatility of aggregate labor market stocks and flows, and the impulse response to a negative 1% TFP shock shows a hump-shaped increase in total unemployment with TL unemployment recovering within roughly two years (due to lower recall costs) while JL unemployment recovers more slowly (due to lower job-finding rates). The countercyclical overshooting of employment-to-JL transition probabilities during the subsequent expansion reflects the procyclicality of the reservation wage — workers are less willing to accept pay cuts in good times, triggering exits from employment at the margin. The overall result is that loss-of-recall accounts for a quantitatively significant share of unemployment persistence in recessions, particularly in the later part of the sample.

Q5. How is the model adapted for the pandemic recession, and what are the specific mechanisms through which PPP reduced jobless unemployment?

The pandemic application introduces two temporary shock processes: (i) a “virus shock” that exogenously raises the TL rate above the threshold determined by ϑ (capturing mandatory closures and social distancing-induced reductions in effective labor demand), and (ii) a productivity shock from social-distancing requirements; PPP is modeled as a policy that subsidizes firms’ wage bills conditionally on maintaining worker-firm attachments, reducing firms’ incentive to exit and thereby directly dampening the endogenous TL-to-JL (loss-of-recall) flow.* With these modifications the model captures the key features of pandemic labor market dynamics: the extraordinary March-April 2020 TL spike, the rapid initial recall, and the subsequent slow recovery of employment. In the PPP counterfactual (no PPP), cumulative TL-to-JL flows over the pandemic period would have been approximately double their actual levels — the model generates a 47.4% ratio of actual-to-counterfactual cumulative TL-to-JL flows, indicating PPP prevented roughly 53% of the loss-of-recall that would have otherwise occurred. At peak (six months after the shock), employment under the no-PPP counterfactual is 8.8% below pre-pandemic levels versus 6.8% with PPP — a 2 percentage point gap. Jobless unemployment peaks at 7.0% without PPP versus 5.9% with PPP. Consistent with estimates from Hubbard and Strain (2020), the estimated average monthly PPP employment gain is approximately 2.0% over the first six months, with gains of 1.57% through February 2021 before convergence toward zero.

Q6. What does the evidence on reemployment probabilities of workers who transition from TL to JL establish, and why is it important for identifying loss-of-recall?

Workers in jobless unemployment who were in temporary-layoff unemployment in the previous period have reemployment probabilities virtually indistinguishable from those of the full population of jobless unemployed (Table 3), which — because JL workers have far lower reemployment probabilities than TL workers — establishes that the TL-to-JL transition is a true loss-of-recall event: the worker has genuinely lost the recall relationship and now faces the same search frictions as other permanently separated workers. This finding is important for the paper’s empirical strategy because it validates the interpretation of CPS-recorded TL-to-JL transitions as genuine loss-of-recall rather than mismeasurement or recategorization without substantive change in the worker’s employment prospects. The result also implies that TL-to-JL transitions create true duration dependence in reemployment probabilities among workers initially on TL: workers who spend longer in TL unemployment are more likely to lose recall, so the average reemployment probability of the TL cohort declines with duration. This duration dependence is consistent with the model’s mechanism — exit probability rises over time as firms facing prolonged overhead cost shocks eventually breach the exit threshold — and provides a micro-level validation of the endogenous loss-of-recall channel.

Key Concepts

temporary-layoff (TL) unemployment : the labor market state in which an unemployed worker retains an expectation of recall to the prior employer (either a specific return date or an indication of recall within six months, per CPS classification); characterized by substantially higher reemployment probabilities than jobless unemployment, accounting for roughly one-third of separations from employment but only one-eighth of the total unemployment stock due to the transient nature of TL spells.

loss-of-recall : the conversion of a temporary layoff into a permanent separation — the event by which a worker initially on TL status transitions to jobless unemployment because the prior employer exits or cannot recall; the paper’s central amplification mechanism, shown to be countercyclical (higher in recessions), to account for 8.5–11.0% of unemployment increases in pre-pandemic recessions, and to be substantially dampened by PPP during the pandemic.

JL-from-TL stock : the accumulated stock of workers currently in jobless unemployment whose most recent exit from employment was through temporary layoff — constructed via the paper’s novel recursive accumulation method; has a standard deviation 16 times GDP and 2 times total unemployment, correlates 0.93 with total unemployment, and constitutes a leading slack indicator that captures the indirect destabilizing contribution of temporary layoffs to unemployment dynamics.

recall hiring versus new-hire margin : the model’s two channels through which firms can expand their workforce — recalling workers from their own TL pool (lower adjustment cost, higher recall elasticity) versus hiring new workers from the pool of jobless unemployed (higher cost); both margins respond positively to the discounted firm value J(w,s) but with different sensitivities calibrated to match the differential volatility of TL-to-E and JL-to-E transition probabilities in the CPS.

staggered Nash wage bargaining : the model’s wage rigidity mechanism (following Gertler-Trigari 2009), in which firms and workers negotiate base wages with probability (1-λ) each period; the calibrated λ=8/9 targets a wage adjustment frequency of roughly one per quarter, consistent with Taylor (1999) and Gottschalk (2005) evidence; wage rigidity — combined with the allowance for temporary pay cuts to prevent exit — is quantitatively important for replicating the observed volatility of labor market flows and stocks.

The Effect of High-Tech Clusters on the Productivity of Top Inventors: Comment

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

This paper is a comment on Moretti (2021b), which studied agglomeration effects for innovation by testing whether the size of technology clusters causes patenting. The original paper (M21) used US patent data from 1971 to 2007 (Zucker and Darby, 2014) and reported a baseline elasticity of patenting with respect to cluster size of 0.0676, along with event study and instrumental variables (IV) evidence supporting a causal interpretation.

Wiebe identifies two major methodological problems that undermine M21’s causal claims.

Problem 1 — Misspecified event study. M21’s event study (Figure 6) was designed to test for selection bias from “rising star” inventors sorting into large clusters. The event is inventors moving across cities exactly once. However, M21’s specification interacts pre-move average cluster size with pre-move event-time indicators and post-move average cluster size with post-move event-time indicators separately — it does not exploit the change in cluster size generated by the move itself. Following the standard “mover” design literature (Finkelstein et al., 2016; Molitor, 2018; Cantoni and Pons, 2022), the correct specification uses the change in average cluster size as the treatment variable, interacted with event-time indicators. Wiebe implements this corrected event study and finds no statistically significant pre-trend and no statistically significant treatment effect post-move. Notably, the baseline elasticity estimated on the mover sample using all observed variation is large and significant at 0.3145 (SE 0.0953), but no effect is detected when variation is restricted to that generated by moving. The null result could also partly reflect attenuation bias from misclassified moves, since the dataset does not distinguish inventors who share the same name.

Problem 2 — Coding error in IV. M21’s Table 5 instruments cluster size using variation in the number of inventors in other cities employed by firms also active in the focal inventor’s city, with the instrument calculated via first-differencing. Due to a coding error, M21 sorts data by firm, field, and year but not by city before first-differencing, so the differencing is taken across cities rather than within cities. Because firm-field-year is not a unique sorting key, Stata’s sort command pseudo-randomly orders observations with tied values, making the results unreproducible across runs. When Wiebe corrects the code to sort by city and compute first-differences within city, the 2SLS estimates become unstable and nonsignificant, with the first-stage F-statistic falling to approximately 7. This means M21 provides no valid IV evidence against confounding from city-field-year shocks such as local subsidies.

Beyond these two major problems, the Appendix documents seven additional issues. The positive effect of cluster size on patent quality (M21 Table 6) disappears and reverses when the log transformation is corrected from log(y + 0.00001) to log(y + 1) or Poisson regression — the corrected estimate is negative and significant, implying that cluster size reduces citations per patent along the intensive margin and the overall quality effect is negative. Heterogeneous elasticity estimates (M21 Table 8) contain a coding error; corrected estimates show substantial heterogeneity. The distributed lag model (M21 Figure 5) uses an incorrectly defined lag structure in an unbalanced panel; corrected estimates yield nonsignificant contemporaneous effects. Cluster quality estimates (M21 Table A.8) use a cluster size definition differing from the text, and corrected elasticities are approximately half as large. M21’s claimed extensive margin effect in Table A.7 is logically unsupported since no zeros are observed. The team size robustness check is conceptually flawed because it controls twice for per-coauthor adjustment. A gap-interpolation coding error in Table A.6 biases estimates downward. Broader computational reproducibility failures arise from many-to-many merges with non-unique sort orders. Wiebe explicitly notes that the null IV and event study results are not evidence against agglomeration effects per se.

Q: What is the baseline finding in M21 that Wiebe contests? A: M21 reports a baseline elasticity of patenting with respect to cluster size of 0.0676, estimated from linear regressions with extensive fixed effects including inventor fixed effects. M21 presents an event study and IV strategy as additional evidence supporting a causal interpretation of this elasticity.

Q: What is wrong with M21’s event study specification? A: M21’s event study interacts pre-move average cluster size with pre-move event-time indicators and post-move average cluster size with post-move event-time indicators, but never uses the change in cluster size associated with moving. The standard mover design (Finkelstein et al., 2016; Molitor, 2018) uses the change in average environment as a constant treatment variable interacted with all event-time indicators. Because M21’s specification does not exploit moving-induced variation, it would be identified even if moving induced no change in cluster size.

Q: What does Wiebe’s corrected event study find? A: Wiebe’s corrected mover event study shows no statistically significant pre-trend (consistent with no systematic sorting of rising-star inventors into large clusters) and no statistically significant post-move treatment effect. In contrast, the baseline fixed-effects elasticity on the mover sample using all observed variation is 0.3145 (SE 0.0953) — large and significant — indicating the null result is specific to the moving-generated variation.

Q: What alternative explanation does Wiebe offer for the null event study result? A: The null result could be partly explained by attenuation bias from misclassified moves. M21’s code creates inventor identifiers based on names, but the COMETS dataset does not distinguish inventors who share the same name, so an apparent cross-city move may simply be two different inventors with the same name living in different cities.

Q: What is the coding error in M21’s IV strategy? A: M21 constructs the instrument by first-differencing a variable measuring inventors in other cities working for firms also active in the focal city. The code sorts by firm, field, and year before differencing, but omits city from the sort key, so first-differencing is computed across cities rather than within cities, generating an instrument that does not match the definition in the text.

Q: Why does the coding error also cause non-reproducibility? A: Firm-field-year is not a unique sorting key because multiple cities can share the same firm-field-year values. Stata’s sort command pseudo-randomly orders observations with tied values, so each run produces a different city ordering within tied groups and therefore a different instrument and different estimates.

Q: What do the corrected IV results show? A: After correcting the sort order to include city and computing first-differences within city, the 2SLS estimates are unstable and nonsignificant. The first-stage F-statistic falls to approximately 7, indicating a weak instrument. This does not constitute evidence against agglomeration effects, but means M21’s IV strategy provides no valid evidence against confounding from city-field-level shocks such as local subsidies.

Q: What happens to the patent quality results when the log transformation is corrected? A: M21 uses log(citations + 0.00001), which assigns very large weight to the extensive margin. When Wiebe uses log(citations + 1) or Poisson regression instead, the estimated effect of cluster size on patent quality is negative and statistically significant, reversing M21’s finding. The corrected result implies that while cluster size may raise the probability of producing any cited patent, it reduces citations per patent for inventors who do produce cited patents, and the overall effect is negative.

Q: What are the corrected aggregate agglomeration loss estimates? A: Using the corrected constant elasticity, the estimated output reduction from equalizing cluster sizes is -9.15% (slightly smaller than M21). Using corrected heterogeneous elasticities based on within-field-year size quartiles, the output loss is -23.75% (about twice as large). Using elasticities based on global size quartiles, the loss is -35.11%.

Q: What is wrong with M21’s distributed lag model (Figure 5)? A: M21’s code defines lags and leads using sequential observations in the panel rather than calendar years. Because the inventor-year panel is unbalanced, a coded “one-year lag” can refer to any number of years prior. When Wiebe restricts to inventors with 11 consecutive years and correctly defines year-based lags, confidence intervals widen substantially and the contemporaneous effect estimate becomes nonsignificant.

Q: What is the conceptual flaw in M21’s team-size robustness check? A: M21’s Table A.8 controls for the number of coauthors on a patent, but the dependent variable is already measured as patents per coauthor. Controlling for team size after already dividing by team size effectively controls for the same variable twice.

Q: What are the broader computational reproducibility problems in M21? A: The cleaning code uses many-to-many merges with non-unique sort orders, generating slightly different datasets on each run. For example, when merging inventors with patent assignees, patent identifiers are not unique because multiple firms can be assigned to a single patent. Removing name suffixes also causes distinct inventors (e.g., Paul H. Hamisch Jr. and Sr.) to be assigned the same identifier. Additionally, using reghdfe with the keepsingletons option retains singleton groups explicitly warned against by the package due to biased standard errors.

Agglomeration elasticity: The elasticity of an inventor’s patent output with respect to the size of the technology cluster (city-field-year cell) in which they work; reported as 0.0676 in M21’s baseline and 0.3145 on the mover sample with all observed variation.

Mover event study design: An event study specification in which the treatment variable is the change in an individual’s average environment (here, cluster size) before and after a geographic move, interacted with event-time indicators — the standard design used in Finkelstein et al. (2016) and Molitor (2018), which M21’s specification does not follow.

Cluster size: The number of inventors (or cluster density) active in the same city-field-year cell as the focal inventor, used as the key independent variable in M21’s regressions.

First-stage F-statistic: A measure of instrument strength in 2SLS IV estimation; the corrected instrument yields F ≈ 7 (indicating weakness), whereas M21’s incorrectly constructed instrument produced a stronger first stage by exploiting spurious cross-city variation.

Extensive vs. intensive margin (patent quality): The extensive margin captures whether an inventor produces any cited patent; the intensive margin captures citations per patent conditional on having any. M21’s log(y + 0.00001) transformation overweights the extensive margin, and the corrected intensive-margin effect of cluster size on quality is negative and significant.

Computational reproducibility: The property that running code on the same data produces identical results across runs. M21’s code fails this standard due to non-unique sort orders in merges and first-differencing steps, causing the IV instrument to differ across runs.

Rising star sorting: The hypothesized selection mechanism whereby inventors with increasing patent trajectories are preferentially hired into large clusters, which would bias OLS agglomeration elasticity estimates upward; M21’s event study was designed to test for this but is incorrectly specified and does not use moving-induced variation.

The Effect of Omitted Variables on the Sign of Regression Coefficients

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

Masten and Poirier demonstrate a previously unrecognized asymmetry in the coefficient stability literature: depending on how omitted variable bias is measured, it can be substantially easier for omitted variables to flip a regression coefficient’s sign than to drive it to zero. The paper focuses specifically on Oster (2019b), a widely used robustness framework with approximately 5,500 Google Scholar citations as of December 2025, and shows that Oster’s sensitivity parameter δ — commonly interpreted as the ratio of selection on unobservables to selection on observables — exhibits a structural problem when used to assess sign robustness.

The core theoretical result (Theorem 2) is that, in Oster’s sensitivity analysis, the sign change breakdown point is bounded above by 1 for any value of R²_long. Since researchers typically treat |δ| = 1 as the cutoff for a robust result, this implies that no empirical result is robust to sign changes under Oster’s framework, even when the explain away breakdown point is far larger than 1. The mechanism is a vertical asymptote in the identified set for βlong that occurs precisely at δ = 1, arising from near multicollinearity between the treatment X and the covariates. At this asymptote, the bias-adjusted estimand becomes discontinuous: βlong can jump from a positive to a negative value as δ crosses 1, even when δ is changed by a negligible amount.

The paper illustrates this with the bias-adjusted estimand formula. Under Oster’s Proposition 1 (which requires δ = 1 plus an auxiliary proportionality assumption), the point estimate for the social capital application is 0.532. But if δ = 1 without the auxiliary assumption, the identified set becomes {−0.0855, 1.8947}. For δ = 0.99, the identified set includes {−18.66, −0.0868, 1.736}. The baseline OLS estimate is 0.17, and the explain away breakdown point (correct) is −32.0, while the sign change breakdown point is only 0.586 — well below the conventional robustness threshold of 1.

The authors propose a modified robustness measure that adds Assumption A5: an explicit bound M on the magnitude of omitted variable bias (|βlong − βmed| ≤ M). Under this restriction, the sign change breakdown point can exceed 1, making robust sign conclusions possible. The choice of M requires substantive justification by the researcher.

Two meta-analyses covering 58 empirical papers document the practical extent of the problem. For papers published in top-five journals from 2019–2021 that cite Oster (2019), the median explain away breakdown point is 2.65, while the median sign change breakdown point (with M = 10|β̂med|) is 1.15 and without the M restriction is 0.96. At the 90th percentile, the explain away point is 13.22, while the sign change point (M = 10|β̂med|) is only 1.66. Across both meta-analytic samples, more than 50% of regressions require that the sign of βlong must be assumed a priori in order to interpret the explain away breakdown point as evidence of sign robustness.

Scope conditions: The results apply specifically to Oster’s linear regression coefficient stability framework under the assumption of exogenous controls (cov(W1, W2) = 0, Assumption A4). The authors note this exogeneity assumption is strong in many applications. The paper does not claim the results extend to other sensitivity analysis frameworks (e.g., Cinelli and Hazlett 2020). The methods are implemented in the companion Stata module regsensitivity.

Q: What is the central finding of the paper?

A: The sign change breakdown point for Oster’s δ is bounded above by 1 (Theorem 2), regardless of how large the explain away breakdown point is. Since |δ| = 1 is the conventional robustness threshold, this implies that, under Oster’s framework, no result is ever robust to a sign change. The explain away breakdown point can simultaneously be very large — e.g., −32.0 in the social capital application — while the sign change breakdown point is only 0.586.

Q: What are the two kinds of breakdown points the paper distinguishes?

A: The explain away breakdown point answers: what is the smallest |δ| required for the data to be consistent with a zero causal effect? The sign change breakdown point answers: what is the smallest |δ| required for the data to be consistent with a causal effect of opposite sign? These two quantities are often equal but are not generally equivalent, and the sign change breakdown point can be strictly smaller than the explain away breakdown point.

Q: What is the mechanism behind the sign change breakdown point being bounded above by 1?

A: The identified set for βlong has a vertical asymptote precisely at δ = 1, arising because the sensitivity analysis allows treatment X and the covariates (W1, W2) to approach near multicollinearity. Near this asymptote, omitted variable bias can be arbitrarily large while δ remains close to 1. This discontinuity allows the bias-adjusted estimand to jump across zero — changing sign — even as δ is changed by an infinitesimal amount near 1.

Q: How sensitive is Oster’s bias-adjusted point estimator near δ = 1?

A: Extremely sensitive. In the social capital application, Oster’s Proposition 1 formula (which assumes δ = 1 with the auxiliary proportionality condition) yields an estimate of 0.532. But without the auxiliary assumption, at δ = 1 the identified set is {−0.0855, 1.8947}; at δ = 0.99 it includes {−18.66, −0.0868, 1.736}; at δ = 1.01 it includes {−0.0843, 2.133, 15.64}. These are not minor perturbations — the estimand is discontinuous in δ at the value that Oster’s formula evaluates it.

Q: What modification do the authors propose to recover sign robustness?

A: They propose adding Assumption A5, which bounds the magnitude of omitted variable bias: |βlong − βmed| ≤ M for a researcher-specified M ≥ 0. Under this restriction, the identified set BI(δ, R²_long, M) is intersected with [βmed − M, βmed + M], and it becomes possible for the sign change breakdown point to exceed 1. The practical difficulty is that M must be chosen with substantive justification, and the authors show via meta-analysis that the conventional choice M = |βmed| (equivalent to assuming the sign of βlong is already known) applies to more than 50% of regressions in their sample.

Q: What do the meta-analyses show about the gap between explain away and sign change breakdown points in practice?

A: For 34 primary regressions from top-five journal papers (2019–2021) with R²_long = 1, the median explain away breakdown point is 2.65 while the median sign change breakdown point (M = 10|β̂med|) is 1.15 and without the M restriction is 0.96. At the 90th percentile, the explain away point is 13.22 versus a sign change point (M = 10|β̂med|) of only 1.66. The second meta-analysis (141 regressions from 55 papers, 2008–2013) produces qualitatively similar results.

Q: Why does the paper flag the implicit sign assumption embedded in many applications of Oster’s method?

A: Using the explain away breakdown point as evidence of sign robustness implicitly requires that M = |βmed|, which is equivalent to constraining βlong ∈ [0, 2βmed] — that is, assuming the sign of βlong is the same as the sign of βmed. The paper shows (Table 4) that across both meta-analytic samples, more than 50% of regressions make this implicit sign assumption in order to interpret the explain away breakdown point as informative about sign robustness.

Q: What is δ, and what are its interpretive limitations?

A: δ is the ratio of (cov(X, γ′2,long W2)/var(γ′2,long W2)) to (cov(X, γ′1,long W1)/var(γ′1,long W1)), measuring the relative magnitude of selection on unobservables versus observables. As Cinelli and Hazlett (2020) show, it is a double ratio: the ratio of the treatment-unobservable association to the treatment-observable association, divided by the ratio of their outcome effects. This double-ratio structure leads to counter-intuitive behavior: a single omitted variable that is only modestly related to treatment can produce δ values far from 1 if the observable control is also only weakly related to treatment, even if the omitted variable is not strongly confounding in an absolute sense.

Q: What assumption is required for the entire sensitivity analysis framework, and how restrictive is it?

A: Assumption A4 requires that all observed covariates W1 are uncorrelated with all unobserved covariates W2 (exogenous controls). The authors note this is a strong assumption in many empirical settings. A companion paper (Diegert, Masten, and Poirier 2025a) addresses the case where controls are endogenous.

Q: What do the authors recommend as best practice?

A: They recommend two practices: (1) plotting the full estimated identified set for the coefficient of interest across a range of assumptions about omitted variables, rather than relying on a single bias-adjusted point estimate; and (2) reporting sign change breakdown points as robustness summary statistics in addition to (or instead of) explain away breakdown points. Both are implemented in the companion Stata module regsensitivity.

Explain Away Breakdown Point: The smallest value of the sensitivity parameter |δ| required for the data to be consistent with a zero causal effect (βlong = 0). This is the quantity computed by Oster’s Proposition 2 and commonly reported as “Oster’s delta.”

Sign Change Breakdown Point: The smallest value of |δ| required for the data to be consistent with a causal effect of opposite sign from the baseline estimate. The paper proves this is bounded above by 1 in Oster’s framework, regardless of the magnitude of the explain away breakdown point.

Oster’s δ: The ratio of the regression of treatment X on the omitted variable index (γ′2,long W2) to the regression of X on the observed covariate index (γ′1,long W1), measuring relative selection on unobservables versus observables. Interpreted as a double ratio: (treatment-unobservable association / treatment-observable association) ÷ (outcome effect of unobservable index / outcome effect of observable index).

Identified Set BI(δ, R²_long): The set of values of βlong consistent with the observed data and a given value of δ and R²_long. Characterized as roots of a cubic polynomial. Has a vertical asymptote at δ = 1, meaning the set can include arbitrarily large or small values of βlong as δ approaches 1.

Bias Magnitude Restriction (Assumption A5): A bound M ≥ 0 on the magnitude of omitted variable bias: |βlong − βmed| ≤ M. Adding this assumption intersects the identified set with [βmed − M, βmed + M], allowing the sign change breakdown point to potentially exceed 1 and making sign robustness conclusions possible.

Coefficient Stability Analysis: A class of empirical methods that assess omitted variable bias by comparing regression coefficients across specifications that include different sets of covariates. The intuition is that if adding observed controls substantially raises R² but barely moves the coefficient, further omitted variable bias is likely small. Formalized by Altonji, Elder, and Taber (2005) and extended by Oster (2019b).

Near Multicollinearity (in this context): The situation in which treatment X and the combined covariate vector (W1, W2) are nearly collinear. In Oster’s framework, this arises precisely at δ = 1 and produces the vertical asymptote in the identified set, making the bias-adjusted estimand discontinuous and potentially unbounded near this value.

The Environmental Bias of Corporate Income Taxation

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

This paper documents and quantifies an “environmental bias” embedded in the U.S. corporate income tax code: CO2-intensive (“dirty”) firms systematically face lower effective tax rates than clean firms, constituting an implicit subsidy on pollution. The authors — Iovino, Martin, and Sauvagnat — establish this cross-sectional fact, trace it to a specific mechanism, provide causal evidence using the 2017 Tax Cuts and Jobs Act (TCJA), and quantify aggregate emissions implications using a calibrated multi-sector general-equilibrium model.

Data and sample. The empirical analysis combines firm-level CO2 emissions from Trucost (scope 1 greenhouse gases) with financial data from Compustat North America for U.S. publicly listed firms, 2003–2021, yielding 11,223 firm-year observations with positive pretax and gross capital income. Effective tax rates are measured as income taxes paid divided by gross capital income (sales minus COGS minus SGA expenses, adding back R&D).

Cross-sectional finding. A one-standard-deviation increase in CO2 intensity is associated with a decrease in the effective tax rate equal to approximately 9% of its standard deviation (coefficient −0.021 to −0.022, significant at 1%). The negative relationship is entirely explained by the lower taxable fraction of gross capital income for dirty firms — that is, by larger interest expense deductions — rather than by differences in the statutory tax rate applied to pretax income.

Mechanism. The chain of causation runs: CO2-intensive production requires tangible capital (primarily machinery and equipment) → tangible capital serves as collateral → higher collateral supports higher debt → higher debt generates larger interest deductions (the “tax shield of debt”) → lower effective tax rates. Once PPE-to-capital-income is controlled for, the coefficient on CO2 intensity in leverage, pretax income, and tax regressions becomes small and statistically insignificant. The relationship holds both across and within industries, including within the energy sector, though the dominant variation is cross-industry.

Causal evidence: TCJA 2017. The paper exploits the federal corporate tax rate cut from 35% to 21% (effective January 2018) in a difference-in-differences design, comparing firms in the top quartile of 2017 CO2 intensity (“dirty”) to cleaner firms. Dirty firms experienced a relative increase in their federal effective tax rate of 2.4 percentage points post-reform. Correspondingly, dirty firms’ total assets grew approximately 11% less than clean firms post-reform. This translates to a semi-elasticity of firm total assets to a one-percentage-point increase in the effective tax rate of approximately −4.8. Parallel pre-trends are confirmed visually and via Rambachan-Roth (2023) sensitivity analysis; a placebo using non-federal taxes shows no differential effect. Results survive controls for other TCJA provisions (interest deductibility limits, international tax changes, net operating loss restrictions), exposure to import tariffs and carbon taxes, leave-one-industry-out specifications, and a triple-difference using foreign firms.

General-equilibrium model and counterfactuals. A 375-sector model with input-output networks (both intermediate and investment networks), financial frictions linking equipment to debt capacity, and endogenous CO2 emissions through fossil fuel usage is calibrated to 2017 BEA and Compustat data. In the Cobb-Douglas benchmark, the 2017 tax cut raises output by 5.9% and emissions by only 4.5% — a less-than-proportional emissions response because clean sectors expand relatively more. A counterfactual eliminating the tax shield of debt while simultaneously cutting the tax rate from 35% to 30% (to hold GDP constant) reduces aggregate emissions by 1.3% with output declining only 0.1%. When equipment and fuel are treated as complements (elasticity of substitution below 1), the emissions reduction under the same policy rises to over 3.7%, implying an absolute reduction of 80–240 million metric tons of CO2 from 2017’s total of 6,457 million metric tons. Monetized at the social cost of carbon, this ranges from USD 8–24 billion (conservative, ~USD 100/ton) to USD 112–336 billion (USD 1,400/ton per Bilal and Kanzig 2024).

Q: What is the central empirical finding of the paper? A: CO2-intensive firms in the U.S. face systematically lower effective corporate income tax rates than clean firms. A one-standard-deviation increase in CO2 intensity is associated with a roughly 9% of a standard deviation decrease in the ratio of taxes paid to gross capital income. This negative relationship is robust to alternative emissions measures (EPA data, scope 2 and 3 emissions), alternative tax scalings (taxes over sales or assets), log CO2 emissions, and leave-one-industry-out specifications.

Q: What is the mechanism linking CO2 intensity to lower effective tax rates? A: Dirty firms rely on tangible capital — specifically machinery and equipment — to produce. Tangible capital is pledgeable as collateral, enabling higher debt. Higher debt generates larger interest expense deductions under the tax code (the “debt tax shield”), which reduces taxable income relative to gross capital income. Once PPE-to-capital-income is included as a control, the coefficient on CO2 intensity in regressions of leverage, pretax income, and taxes paid all become small and statistically insignificant, confirming that PPE fully mediates the relationship.

Q: Which component of tangible capital drives the result? A: Machinery and equipment, not buildings, leases, land, natural resources, or construction in progress, explains virtually the entire positive relationship between PPE and CO2 intensity. This finding is based on the Compustat breakdown of PPE components available for roughly 70% of sample firms.

Q: Does the mechanism operate within industries or only across them? A: Both. Decomposing firm CO2 intensity into an implied industry component (sales-weighted from pure-play firms) and a firm residual, both components are significantly associated with higher tangible capital, leverage, lower taxable fraction of capital income, and lower taxes paid at the 1% level. However, the largest share of the total effect stems from cross-industry variation. Within the energy sector specifically, firms with greater fossil fuel production capacity (from EPA/EIA data) also have more tangible capital, higher debt, and lower effective tax rates.

Q: How does the 2017 TCJA cut affect clean versus dirty firms differently? A: Because dirty firms already shield a large fraction of their capital income from taxation via interest deductions, a uniform cut in the statutory rate benefits them less in proportional terms. The difference-in-differences estimates show that dirty firms (top quartile of 2017 CO2 intensity) experienced a relative increase in their federal effective tax rate of 2.4 percentage points post-reform compared to clean firms, and their total assets grew approximately 11% less than clean firms post-reform. The semi-elasticity of firm assets to a one-percentage-point increase in effective tax rate is approximately −4.8.

Q: How is the parallel trends assumption supported? A: Event-study graphs show no pre-2018 divergence in federal effective tax rates or asset growth between dirty and clean firms. A placebo test using non-federal income taxes (which should be unaffected by the federal statutory rate change) shows no differential post-reform effect. The Rambachan-Roth (2023) sensitivity analysis confirms that the null of no differential effect can be rejected at the 1% level allowing for pre-trend deviations up to M = 0.5, and at the 10% level up to M = 1.

Q: What robustness checks address other provisions of the TCJA and concurrent shocks? A: The authors exclude or control for firms affected by the TCJA’s interest deductibility limitation, multinational firms (more than 20% foreign sales), firms with large loss carryforwards, and manufacturing firms — results are unchanged. They also control for firm-level exposure to import tariff changes and carbon taxes (using the World Carbon Pricing Database), with coefficients of interest remaining virtually unchanged. Leave-one-industry-out specifications and a triple-difference using foreign firms (comparing U.S. dirty vs. clean firms pre/post-2018, against foreign equivalents in countries with stable tax rates) yield a semi-elasticity of −5.8, if anything larger than the baseline.

Q: What does the general-equilibrium model add that the difference-in-differences cannot? A: The DiD design identifies relative effects of the tax cut on dirty versus clean firms but cannot recover the absolute effect on aggregate output and emissions. The GE model, calibrated to 2017 data and validated against the untargeted DiD estimates, quantifies aggregate impacts: the 2017 tax cut raises steady-state output by 5.9% while emissions rise by only 4.5% — a less-than-proportional increase due to compositional reallocation toward clean sectors.

Q: What does the counterfactual removing the debt tax shield find? A: Eliminating the tax shield of debt while simultaneously lowering the corporate tax rate from 35% to 30% (to keep GDP constant) reduces aggregate emissions by 1.3% (Cobb-Douglas benchmark) while total output falls only 0.1% and GDP remains constant by design. The emissions reduction arises because clean sectors, which rely more on less-pledgeable capital, are made relatively cheaper once the tax advantage of debt is removed, redirecting demand away from CO2-intensive sectors.

Q: How does the complementarity assumption between equipment and fuel affect the results? A: When equipment and fuel are modeled as complements (elasticity of substitution below 1) rather than Cobb-Douglas substitutes, both policy counterfactuals yield larger emissions effects. For the tax shield removal policy, the predicted emissions reduction rises from 1.3% to over 3.7% as complementarity strengthens. This is because policies that raise the cost of equipment also induce firms to cut fuel consumption, amplifying the direct compositional effect.

Q: What is the quantified absolute emissions impact of removing the tax shield? A: Given 2017 U.S. total emissions of 6,457 million metric tons, the model predicts an absolute reduction of 80–240 million metric tons of CO2, depending on the assumed complementarity between equipment and fuel. Monetized at conservative estimates (~USD 100/ton), the policy saves USD 8–24 billion; at USD 1,400/ton (Bilal and Kanzig 2024), the value rises to USD 112–336 billion. The authors note that the physical quantity measure is more reliable than the monetized figure given uncertainty in the social cost of carbon.

Q: How does this paper relate to the ECB bond purchasing literature? A: Piazzesi et al. (2022) document that the ECB’s market-neutral bond purchases implicitly favor dirty firms because those firms issue more bonds due to higher tangible capital holdings. This paper identifies the same underlying mechanism — tangible capital → debt capacity — but on the tax side, showing that the corporate income tax code independently provides an implicit subsidy to dirty firms through the debt tax shield.

Q: What is the policy implication for the debt tax shield specifically? A: The debt tax shield — the deductibility of interest payments but not dividends — has no clear economic rationale (both are returns to capital) and, per several policy proposals (CBO 1997, IMF 2016), is a candidate for elimination. This paper adds a new dimension: the tax shield indirectly subsidizes CO2 emissions by differentially benefiting capital-intensive, CO2-intensive sectors. A revenue-neutral reform eliminating the shield can reduce emissions without sacrificing GDP.

Effective tax rate (paper’s definition): The ratio of corporate income taxes paid to gross capital income, where gross capital income equals sales minus cost of goods sold minus SGA expenses plus R&D spending. This differs from the tax-to-pretax-income ratio because it captures how much of total capital earnings — before any deductions — is remitted as tax.

Debt tax shield (tax advantage of debt): The reduction in corporate tax liability arising from the deductibility of interest payments on corporate debt. Because dividends are not deductible, debt-financed capital faces a lower after-tax cost than equity-financed capital. The shield’s value is estimated at approximately 10% of firm value in prior literature.

CO2 intensity: Metric tons of CO2 equivalent per USD 1,000 of output (tCO2/k$). The sample average is 0.1 tCO2/k$, with a heavily right-skewed distribution (median 0.02, 99th percentile 1.5).

Environmental bias of corporate taxation: The paper’s central concept — the systematic difference in effective tax rates between dirty and clean firms that arises not from explicit environmental policy but from the interaction of the debt tax shield with the capital structure of CO2-intensive industries. This constitutes an implicit subsidy on pollution embedded in the corporate income tax.

Asset pledgeability (psi): The fraction of a firm’s assets recoverable by creditors in the event of default. In the model, equipment has higher pledgeability than other capital (estimated b_psi = 0.23 additional pledgeability for equipment, a_psi = 0.35 base). Higher pledgeability allows firms to sustain more debt and thus benefit more from the tax shield.

User cost of capital: The total cost to a firm of using one unit of capital, combining depreciation, tax allowances from accelerated depreciation, and the financing cost advantage of debt over equity. The model formalizes how both the equity-financed component and the debt advantage component respond to tax rate changes, with the debt advantage term being larger for firms with more pledgeable (tangible) capital.

Investment network: An input-output structure capturing which sectors’ outputs are used to produce each type of capital good. The paper extends vom Lehn and Winberry (2021) by constructing separate equipment and non-equipment investment networks across 375 non-fuel BEA sectors, enabling emissions accounting that includes capital production alongside direct production inputs.

The Gender Pay Gap: Micro Sources and Macro Consequences

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

Layer 1: Overview

This paper uses linked employer-employee data from Brazil (RAIS, 2007–2014, covering 267 million worker-years, 56 million unique workers, and 607,000 employers) to document that the gender pay gap of 13.3 log points is overwhelmingly driven by women sorting into lower-paying employers — 78.7% of the gender gap in employer pay fixed effects is attributable to between-employer sorting, not within-employer discrimination. To interpret this sorting, the authors develop an equilibrium on-the-job search model (extending Burdett and Mortensen 1998) with endogenous firm pay, amenities, and hiring, and provide a constructive proof that all model parameters are point-identified from linked employer-employee data. The estimated model finds that amenities explain approximately half of total compensation for both genders (mean amenity share 48.8% for men, 52.2% for women), that compensating differentials account for roughly half of the gender pay gap (reducing it from 13.3 to 4.6 log points in total-compensation terms), and that higher-ranked employers offer women higher amenities rather than higher pay — resolving the puzzle that women disproportionately work at large employers despite a flat employer-size-pay gradient for women. Eliminating gender differences in employer preferences (gender wedges) would raise output by 12.9% but pull women into low-amenity firms, reducing their welfare, while equal-pay and equal-hiring policies close part of the pay gap but lower worker welfare through adverse incentive effects on firms’ compensation and hiring decisions.

Summary of a published paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What empirical patterns motivate the paper’s framework?

Three facts from Brazilian linked employer-employee data require a richer model than standard pay-only frameworks: (i) 78.7% of the 11.3 log-point gender gap in employer pay fixed effects is a between-employer sorting gap (women work at lower-paying firms); (ii) pay is increasing in employer size for men (R² = 3.3%) but essentially flat for women (R² = 0.1%); and (iii) women are disproportionately concentrated at the largest employers, which is inconsistent with models in which large firms pay more if pay is all that matters. These three facts together reveal that women value employer attributes other than pay, particularly at larger firms. Direct amenity proxies confirm this: women at larger employers are substantially less likely to be exposed to workplace hazards (coefficient −0.013, p < 0.01), less likely to be fired unjustly (coefficient −0.005, p < 0.01), much more likely to receive generous parental leave (coefficient 1.054, p < 0.01), and more likely to work part time. The AKM two-way fixed effects decomposition further shows that employer fixed effects account for 12.5% of the variance of log earnings for men and 11.1% for women, with the variance of earnings explained at 92.3% (men) and 93.1% (women).

Q2. What is the equilibrium model and how does it generate compensating differentials?

The model extends Burdett-Mortensen on-the-job search to allow firms to simultaneously choose wages, amenities, and vacancies, with firms differing in three dimensions: productivity p, gender wedges τ (an implicit tax on employing women capturing taste-based discrimination or comparative advantage), and gender-specific amenity cost shifters ca,0 — making firm pay, amenities, and hiring jointly determined in equilibrium. Workers maximize flow utility x = w + a (wage plus amenity value), and each gender climbs a separate firm utility ladder. Firms with higher composite productivity p̃ = (1−τ)p + a* − c(a*) offer higher utility to attract more workers given convex vacancy posting costs. Because amenity costs are convex and increasing in amenity value, firms optimally set amenities so that the marginal cost equals one (the unit wage), creating endogenous compensating differentials: high-amenity firms can pay lower wages while still attracting workers. The model is isomorphic to a standard wage-only Burdett-Mortensen model with wages replaced by flow utility and productivity replaced by composite productivity.

Q3. How are all model parameters identified constructively?

The authors provide a five-step constructive identification proof that recovers all parameters — including the unobservable amenity values, gender wedges, and productivity distribution — without distributional assumptions: (1) gender-specific employer pay components from AKM; (2) employer utility ranks from the employer size distribution (higher-utility firms are larger in equilibrium); (3) labor market flow hazards (λU, λE, λG, δ) from worker flow data conditional on ranks; (4) firm-level parameters (p, τ, ca,0) by inverting equilibrium profit functions; (5) economy-wide parameters (cv,0, ηv, ηa) from aggregate labor share, firm pay-profit gradient, and aggregate amenity cost share. The key insight for step (4) is that unobserved firm profits per matched worker can be inferred from equilibrium firm sizes (more profitable firms post more vacancies and hire more workers), and comparing utility levels inferred from sizes with observed wages identifies amenity values. For step (3), the involuntary job offer hazard λG is separately identified because job-to-job transitions involving a decline on the utility rank ladder — which cannot be voluntary (workers strictly prefer higher utility) — must be involuntary, allowing the hazard to be estimated by counting down-rank transitions.

Q4. What are the estimated structural results on amenities and the pay-amenity tradeoff?

Amenities are pervasive and quantitatively large: the mean amenity share of total compensation is 48.8% for men and 52.2% for women, yet compensating differentials explain the lion’s share of firm pay dispersion, with utility dispersion accounting for only 4.4% of pay dispersion for men and 3.6% for women — far less than pay dispersion alone might suggest. Higher-ranked firms for men mostly offer higher pay, but higher-ranked firms for women mostly offer higher amenities. The estimated gender productivity gap is 8.3 log points (employment-weighted mean log productivity 0.864 for men, 0.781 for women), and the employment-weighted mean gender wedge is 0.059 for women but 0.235 for men (wedge represents an implicit disutility from hiring women, so higher means women face higher wedge on average in firms where they are less likely to work). Estimated labor market parameters show women receive fewer job offers from nonemployment (λU_F = 9.1% monthly vs. 10.4% for men) and have lower job destruction rates (δ_F = 2.8% vs. 3.6% for men), contributing to slower job-ladder climbing.

Q5. How does the paper decompose the gender pay gap into micro sources?

Shutting down firm heterogeneity in amenities — replacing gender-specific amenity values with their mean — closes 45% of the gender pay gap, largely because women relocate toward formerly male-dominated, higher-paying, lower-amenity firms; shutting down differences in employer preferences (gender wedges) eliminates the pay gap entirely; differences in labor market flow rates have little effect. The total-compensation gender gap, which accounts for amenity differences, is only 4.6 log points — 40.7% of the raw pay gap of 11.3 log points — confirming that compensating differentials explain approximately half of the measured pay disadvantage. This decomposition is a novel contribution over Card et al. (2016), who rationalized the gap through exogenous gender-specific bargaining parameters without modeling amenities or their equilibrium provision.

Q6. What are the macro consequences of the gender pay gap for output and welfare?

Removing all gender differences from the economy (wedges, amenity costs, and flow rates) raises output by 6.1% and welfare by 2.1%, substantially below what pay differences alone might suggest; however, eliminating employer preferences over gender (gender wedges only) raises output by 12.9% at the cost of a welfare reduction for women, because women are pulled into high-paying, low-amenity firms. The quantitative wedge between output gains (12.9%) and welfare gains when wedges are removed reveals that women’s sorting into amenity-rich firms is partly welfare-enhancing from their perspective, even if it involves accepting lower wages. This is a key insight for policy: policies targeting pay gaps without accounting for amenity losses can be welfare-reducing.

Q7. What do equal-pay and equal-hiring policies achieve in equilibrium?

Both equal-pay mandates (forcing firms to pay men and women identical wages) and equal-hiring mandates (requiring gender-neutral hiring) close part of the gender pay gap but lower worker welfare for both genders, because the policies generate adverse incentive effects: equal-pay mandates induce firms to reduce amenities for women (since the wage-amenity tradeoff is disrupted), and equal-hiring mandates distort firms’ recruiting decisions in ways that raise vacancy costs. These general-equilibrium effects would be missed in partial-equilibrium analyses. The paper thus provides a rigorous case that equal-treatment policies — while closing observable pay gaps — fail to achieve the underlying welfare gains from eliminating gender differences, and may generate unintended welfare losses.

Q8. How does the model resolve the employer-size puzzle and what discriminatory mechanisms does it admit?

The flat employer-size-pay gradient for women (versus steeply increasing for men) is rationalized in the model because large employers offer women high amenities that substitute for pay; women optimally accept lower wages at large employers in exchange for amenity bundles that are unavailable at smaller firms. The model accommodates three discrimination channels simultaneously: taste-based discrimination (Becker 1971, via the gender wedge τ), compensating differentials reflecting gender-specific job characteristics (Rosen 1986, via amenity cost shifters), and monopsony power (Robinson 1933, via search frictions). Even nondiscriminatory firms treat women differently than men as a best response to the equilibrium distribution of discriminatory firms — an equilibrium spillover of discrimination that purely partial-equilibrium analyses miss.

Key Concepts

gender wedge (τ) : a firm-level parameter capturing the implicit disutility cost per unit of female employment, encompassing taste-based discrimination (Becker 1971) and comparative-advantage differences (Goldin 1992); estimated to explain substantial variation in women’s employment shares across firms, with female managers, routine manual tasks, and smaller size associated with lower wedges (R² = 54.6%).

compensating differentials : the wage reduction a worker accepts in exchange for favorable non-wage job attributes (amenities); in this paper, estimated to explain approximately half of the gender pay gap — the total-compensation gap is 4.6 log points vs. a pay gap of 11.3 log points — implying that women’s lower wages partly reflect their preference for amenity-rich employers.

amenity share : the fraction of total compensation (wages plus amenities) attributable to non-wage job attributes; estimated at 48.8% for men and 52.2% for women, indicating that amenities are quantitatively as important as wages in total compensation for both genders.

employer rank : a revealed-preference ordering of employers by gender-specific utility offered to workers, identified by the employer size distribution (larger firms are higher-utility in equilibrium); the paper’s key object for separating the between-employer sorting component of the pay gap from the within-employer component.

composite productivity (p̃) : the model’s reduced-form measure of a firm’s profitability per worker, combining raw productivity p, the gender wedge τ, and the optimized amenity net of amenity costs; allows the equilibrium to be analyzed as a standard Burdett-Mortensen model with composite productivity replacing raw productivity and flow utility replacing wages.

involuntary job offer hazard (λG) : the arrival rate of unsolicited job offers that workers must accept regardless of utility ranking, capturing spousal relocations and other idiosyncratic transitions; identified from the frequency of utility-rank-decreasing job transitions, since voluntary transitions can only increase utility.

The Productivity of Professions: Evidence from the Emergency Department

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

This paper studies the productivity of nurse practitioners (NPs) versus physicians performing overlapping tasks in Veterans Health Administration (VHA) emergency departments (EDs), exploiting a quasi-experiment created by the VHA’s December 2016 grant of full practice authority to NPs. The identification strategy instruments patient assignment to NPs versus physicians using quasi-random variation in the number of NPs on duty on a given ED-day, conditional on ED-by-time-category fixed effects. The sample covers 1.1 million ED visits across 44 VHA EDs from January 2017 to January 2020, seen by 1,348 physicians and 156 NPs. The instrument is validated by demonstrating balance in patient observable characteristics across values of the instrument, stability of IV estimates across 256 combinations of patient covariate controls, and absence of spillover effects from NP presence onto physician performance.

On average in the ED setting, NPs increase patient length of stay by 11 percent (approximately 18 additional minutes) and raise the cost of the ED visit by 7 percent (approximately $66 per visit). NPs raise the 30-day preventable hospitalization rate by 0.25 percentage points, a 20 percent increase relative to the mean. No statistically significant effect on 30-day mortality is detected (95 percent confidence interval: -0.34 to 0.11 percentage points). OLS estimates carry the opposite sign because NPs are assigned healthier patients in observational data; the IV design corrects for this selection.

The average NP-physician performance gap varies systematically by case complexity and severity. For the highest-complexity quartile of cases (by Elixhauser comorbidities), NPs increase ED costs by 12 percent and length of stay by 28 percent. For cases at or above the 95th percentile of severity (based on 30-day mortality by diagnosis), NPs increase ED costs by 25 percent, length of stay by 99 percent, and admissions by 26 percentage points (42 percent relative to the mean), while reducing 30-day preventable hospitalization by 3 percentage points — suggesting that NPs’ higher care intensity partially offsets worse intrinsic skill for the most severe cases. For lower-complexity cases, the cost and length-of-stay gaps are smaller, but NPs still significantly raise preventable hospitalizations.

NPs exhibit clinical decision-making patterns consistent with lower diagnostic skill: they are more likely to order consults (2.6 percentage points, or 11 percent of the mean), CT scans (1.2 percentage points, or 8.3 percent), and X-rays (2.0 percentage points, or 6.9 percent). NPs lower opioid prescriptions by 1.8 percentage points (20 percent of the mean) and raise antibiotic prescriptions by 4.0 percentage points (6.3 percent of the mean), consistent with threshold adjustment under lower diagnostic skill with asymmetric error costs. Downstream, patients treated by NPs incur similar opioid use disorder rates despite lower opioid prescribing, and higher infection-related return visit rates despite higher antibiotic prescribing.

Counterfactual analysis finds that allocating one quarter of ED patients to NPs increases net spending by $129 million per year to the VHA after accounting for NPs’ lower wages (approximately half of physicians’). However, deploying NPs exclusively to the least-complex quarter of cases reduces net spending to approximately one-fifth of this amount.

A distributional analysis deconvolving provider-specific IV estimates reveals that within-profession productivity variation substantially exceeds the average between-profession gap. The interquartile range in annual spending attributable to provider productivity within each profession is approximately $900,000, roughly three times the mean annual spending difference between the average NP and the average physician. A randomly chosen NP outperforms a randomly chosen physician in up to 38 percent of pairs. Within professions, individual provider productivity shows essentially no relationship with wages or case complexity assigned, whereas between professions, case assignment and wages are strongly sorted by professional class.

Q: What is the core research question? A: The paper asks whether NPs and physicians, who perform overlapping tasks in the ED but differ sharply in training, selectivity, and pay, differ in productivity, and how that average between-profession difference compares to productivity variation within each profession. It also asks what mechanisms drive any observed gap and how case assignment responds to provider skill differences.

Q: What is the identification strategy and why is it credible? A: The authors instrument patient assignment to NPs with the number of NPs on duty on the ED-day, conditional on ED-by-year, ED-by-month, ED-by-day-of-week, and ED-by-hour fixed effects. Credibility rests on: provider schedules being set months in advance, decoupling NP availability from arriving patient characteristics; patient characteristics being well balanced across values of the instrument conditional on fixed effects; IV estimates being stable across all 256 covariate-control combinations; and on-duty physician and NP characteristics also being balanced across the instrument.

Q: What are the main average effects of NPs on resource use? A: IV estimates show NPs increase patient length of stay by 11 percent (approximately 18 minutes) and ED cost by 7 percent (approximately $66 per visit). There is no significant average effect on inpatient admissions in the overall sample, though NPs significantly raise admissions for high-severity cases.

Q: What is the effect of NPs on patient health outcomes? A: NPs raise 30-day preventable hospitalizations by 0.25 percentage points, a 20 percent increase relative to the mean. The 95 percent confidence interval for 30-day mortality is -0.34 to 0.11 percentage points, implying no statistically significant mortality effect in the overall sample.

Q: Why do OLS and IV estimates have opposite signs? A: In observational data, NPs treat healthier patients than physicians: NP patients are younger (60.7 versus 62.5 years), have fewer Elixhauser comorbidities (3.2 versus 3.7), and have fewer prior inpatient stays (0.4 versus 0.7). This selection causes OLS estimates of NP effects to be negative. The IV corrects for this by exploiting quasi-random variation in NP availability; IV estimates are stable across all combinations of patient controls, consistent with the instrument being orthogonal to unobservable patient health.

Q: How does the NP-physician performance gap vary with case complexity and severity? A: For the highest-complexity quartile, NPs increase length of stay by 28 percent and ED costs by 12 percent without a significant preventable hospitalization effect. For cases at or above the 95th severity percentile, NPs increase length of stay by 99 percent, ED costs by 25 percent, and admissions by 26 percentage points (42 percent relative to the mean), while reducing 30-day preventable hospitalization by 3 percentage points. For lower-complexity quartiles, NPs show smaller cost and length-of-stay effects but significantly raise preventable hospitalizations, suggesting the higher care intensity at high severity compensates for lower skill.

Q: What does the heterogeneity by severity imply for optimal case assignment? A: The pattern is consistent with skill-task matching: NPs have a comparative and absolute disadvantage in complex cases, so optimal assignment directs less complex cases to NPs and fewer patients to NPs when physicians are more available. Empirically, NPs are indeed assigned healthier patients from the available pool, and are assigned a modestly smaller share when the ED is less busy.

Q: What mechanisms explain the average NP-physician gap? A: Three mechanisms are examined. First, experience: a one-standard-deviation increase in specific experience is associated with a 5.8 percent decline in the NP-physician length-of-stay gap, and general experience with a 10 percent decline; however, experience does not significantly narrow the preventable hospitalization gap. Second, information acquisition: NPs order more consults, CT scans, and X-rays, consistent with compensating for lower diagnostic skill. Third, prescription thresholds: NPs reduce opioid prescribing by 20 percent and raise antibiotic prescribing by 6.3 percent, consistent with threshold adjustment under asymmetric error costs, but downstream outcomes are not improved correspondingly.

Q: What do prescription patterns and downstream outcomes reveal about NP diagnostic skill? A: NPs prescribe fewer opioids yet patients treated by NPs obtain similar downstream opioid use disorder rates; NPs prescribe more antibiotics yet patients treated by NPs have higher rates of return visits with infections. This pattern is consistent with NPs exhibiting higher rates of both false positives and false negatives, not merely adjusted thresholds, suggesting genuinely lower diagnostic skill rather than threshold differences alone.

Q: What do counterfactual cost calculations show? A: Allocating one quarter of ED patients to NPs raises non-wage spending by $197 million per year to the VHA; after accounting for NP wages being half of physician wages (approximately $120,000 versus $240,000 per year), net cost is still $129 million per year. Restricting NP deployment to the least-complex quarter of cases reduces net spending to approximately one-fifth of this amount, illustrating that targeted case assignment substantially improves NP cost-effectiveness.

Q: How large is within-profession productivity variation relative to between-profession differences? A: The interquartile range in annual spending attributable to provider productivity within each profession is approximately $900,000, roughly three times the mean annual spending difference between the average NP and the average physician. A randomly chosen NP outperforms a randomly chosen physician in up to 38 percent of random pairs. The authors conclude that, despite stark differences in training and selection between professions, within-profession variation dominates.

Q: Is individual provider productivity reflected in wages or case assignment within professions? A: Within each profession, provider productivity shows essentially no relationship with wages or with the complexity of assigned cases. This contrasts sharply with between-profession patterns, where professional class strongly predicts both wages (NPs earn approximately $120,000 per year versus $240,000 for physicians) and assigned case complexity. The authors interpret this as evidence of informational and organizational frictions in recognizing individual productivity within professional classes, and note that professional class is a far stronger predictor of pay and case assignment than is individual productivity.

Q: How do complier characteristics relate to the broader patient population? A: Compliers — cases whose provider type is determined by the instrument — are healthier than the average case: younger, with fewer comorbidities, fewer prior inpatient stays, and lower predicted mortality. Never-takers are riskier than the average case. There are no always-takers since patients cannot be assigned to NPs on days when no NPs are on duty.

Q: How does this paper relate to the literature on NP scope-of-practice laws? A: The scope-of-practice literature estimates general-equilibrium effects of allowing NPs greater autonomy, including labor reallocation between professions. This paper instead estimates the partial-equilibrium causal effect of assigning a patient to an NP versus a physician, holding the broader labor market fixed. The two literatures are complementary: the heterogeneity findings here suggest that scope-of-practice expansions may be more beneficial in lower-complexity primary care settings where the NP-physician performance gap is smaller.

Q: What are the policy implications of the findings? A: Three implications are highlighted. First, the efficiency of using NPs depends critically on case assignment: deploying NPs on the least-complex cases reduces net costs to approximately one-fifth of indiscriminate deployment. Second, the substantial overlap between NP and physician productivity distributions provides support for NP use in less complex settings even within the ED context. Third, within-profession productivity variation far exceeding between-profession differences suggests that individual-level productivity assessment, rather than professional class, may be a more accurate guide to case assignment and compensation.

Quasi-experimental variation in NP availability: The identification strategy exploits day-to-day variation in the number of NPs scheduled to work in a given VHA ED, conditional on ED-by-time-category fixed effects, as an instrument for whether a patient is assigned to an NP versus a physician. Schedules are set months in advance, rendering the NP count orthogonal to arriving patient characteristics conditional on those fixed effects.

30-day preventable hospitalization: A standardized quality-of-care outcome defined by the Agency for Healthcare Research and Quality, measuring hospitalizations occurring within 30 days of ED discharge that are classified as preventable given adequate prior outpatient management. Used by the paper as the primary downstream health outcome beyond the ED visit itself.

Elixhauser comorbidities: A set of 31 binary indicators for chronic conditions (e.g., cancer, diabetes) based on medical histories in the prior 365 days, used in this paper to measure and stratify case complexity into quartiles for heterogeneity analysis.

Productivity distributions within professions: Provider-specific productivity estimates derived from a just-identified IV model that instruments assignment to individual providers by indicators for on-duty providers, then deconvolved into underlying distributions using the Efron (2016) and Kline-Rose-Walters (2022) method. These distributions characterize the spread of productivity within each professional class, separate from measurement error.

Prescription threshold adjustment: The mechanism, formalized in Chan, Gentzkow, and Yu (2022), by which providers with lower diagnostic skill optimally adjust treatment thresholds in response to asymmetric costs of false-positive versus false-negative errors. In this paper’s application, NPs lower the opioid prescription rate (where false positives carry higher costs: addiction and overdose) and raise the antibiotic prescription rate (where false negatives carry higher costs: untreated infection), but downstream outcomes do not improve correspondingly.

Skill-task matching: The organizational economics principle (Acemoglu and Autor 2011) that efficiency requires assigning more complex tasks to higher-skilled workers. The paper documents that between professions, case assignment broadly follows this principle (NPs receive less complex patients on average), but within professions, essentially no matching between individual provider productivity and case complexity is observed.

Full practice authority (VHA, December 2016): The VHA policy that allowed NPs to treat patients independently without physician supervision at VHA facilities, superseding state-level restrictions. This policy change defines the start of the paper’s sample period and establishes the institutional context in which the quasi-experiment occurs, as it removed the requirement for physician oversight that previously constrained NP independence.

Why Is Workplace Sexual Harassment Underreported? The Value of Outside Options amid the Threat of Retaliation

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

Layer 1 — Summary

Research question and argument

Dahl and Knepper address the long-standing puzzle of why workplace sexual harassment is chronically underreported despite high estimated prevalence. Survey evidence indicates that no fewer than 1 in 28 U.S. workers report annual victimization, yet only 1 in 11,000 workers files a formal charge with the Equal Employment Opportunity Commission (EEOC). Even following the #MeToo movement, formal charges rose only about 10%, leaving an enormous gap unexplained.

The paper’s central hypothesis is that employers coerce victims into silence through the credible threat of retaliatory firing. The key mechanism: because reporting constitutes a “protected activity” triggering employer notification, workers who fear losing their jobs will suppress claims. This threat is most binding when a worker’s outside options are weak — when it is hard to find a new job or when unemployment insurance (UI) benefits are thin. The paper tests this hypothesis by asking whether external shocks that reduce the value of outside options increase the threshold of harassment severity above which workers are willing to report.

Measurement strategy

Measuring underreporting directly is impossible by definition. The authors’ key methodological insight is to use the selectivity of filed charges as an indirect proxy. Under mild assumptions, if workers become more selective about which incidents they report, the average quality of filed charges must rise. The authors measure quality using the EEOC’s own merit determination: a charge is deemed meritorious if the employer settles, the claimant withdraws upon receipt of benefits, or the EEOC finds reasonable cause after investigation. The merit rate thus serves as an observable proxy for the (unobservable) degree of underreporting.

Baseline descriptive evidence supports the mechanism’s relevance: across 2000–2015, sexual harassment charges were nearly 50% more likely to be meritorious than non-harassment charges (27.0% vs. 18.6%), and more than twice as likely to involve employer retaliation (63.4% vs. 30.7%). The proportion of EEOC sexual harassment cases involving retaliation rose from 52% in 2000 to 72% in 2015, a period over which the annual volume of filed charges fell by 37%.

Analysis 1 — Labor market conditions (2000–2015)

The first empirical design exploits monthly variation in state-industry unemployment rates over 2000–2015 using EEOC microdata on individual charges. The regression controls for industry, state, and time fixed effects, isolating within-state-industry variation in unemployment. The identifying assumption is that a worker’s willingness to file depends only on her outside options and the severity of harassment she experiences, conditional on fixed effects.

The results indicate that each one percentage point increase in a state-industry’s monthly unemployment rate is associated with a 0.5–0.7% increase in the probability that a filed charge is deemed meritorious by the EEOC. This is consistent with the hypothesis that workers become more reluctant to report as outside labor market options weaken.

Heterogeneity analysis using linked EEO-1 establishment data strengthens the interpretation. The effect is amplified in industries that employ a larger fraction of men and in establishments where male managers account for a higher share of supervisory roles. Oﬀending establishments in the sample have, on average, 2.8 percentage points more male employees and 5 percentage points more male managers than non-offending establishments. The selectivity-unemployment gradient is larger in these male-dominated environments, consistent with a role for gendered power disparities in enabling employer retaliation.

Analysis 2 — North Carolina UI reform (quasi-experiment)

The second design exploits North Carolina’s 2013 UI reform as a plausibly exogenous reduction in the value of outside options. In response to the near-insolvency of its UI trust fund following the Great Recession, North Carolina simultaneously reduced maximum weekly benefits by approximately 35% (from $535 to $350 per week) and cut maximum benefit duration from 26 to 20 weeks. Together, these changes reduced the maximum total regular UI benefit available to North Carolinians by approximately 50%, from roughly $14,000 to $7,000. These reforms also violated the Congressional non-reduction rule, making individuals ineligible for an additional 47 weeks of federal Emergency Unemployment Compensation benefits, further amplifying the effective cut. North Carolina was the only state to simultaneously reduce both the level and duration of benefits.

The authors implement a difference-in-differences design comparing North Carolina to other Southern states that did not change their UI programs, controlling for state and month-year fixed effects. Pre-reform parallel trends are documented via event study. Administrative UI recipiency data show that the short-term UI recipiency rate in North Carolina fell from 33% to 10% — a 59% decline relative to control states — within roughly two years of the reform.

The main finding is that the selectivity of sexual harassment charges filed in North Carolina increased by approximately 7 percentage points following the reform, representing more than a 30% increase relative to control states. This is consistent with the hypothesis that reduced UI generosity raises the cost of a retaliatory firing, causing workers to suppress all but the most severe harassment incidents.

The authors note that North Carolina also reduced corporate and personal income taxes shortly after the UI reform. Because tax cuts should increase both labor demand and labor supply (insofar as substitution effects dominate income effects), this would tend to reduce the reporting threshold, leading them to interpret the 30%+ estimate as a lower bound on the causal effect of the UI reform on selectivity.

Formal model

The paper presents a threshold model of reporting behavior adapted from Boone and Van Ours (2006). Workers choose a reporting threshold: the minimum harassment severity above which they will file a charge. The threshold rises when the value of outside options falls, either because the probability of finding a new job declines (recession) or because unemployment benefits shrink. The model predicts that the merit rate of filed charges will rise as outside options weaken. The model explicitly does not predict the volume of charges, because firm behavior — which may adjust endogenously to higher reporting thresholds — is not modeled.

Scope conditions

All findings concern formal EEOC charges filed in the United States between 2000 and 2015 (analysis 1) and through the post-2013 reform period (analysis 2). The EEOC definition of illegal harassment requires severity sufficient to create a “hostile or offensive work environment” or an adverse employment action. The paper’s merit measure captures harassment that exceeded this legal threshold; non-meritorious charges may still involve some level of misconduct. The sample for establishment-level heterogeneity analyses covers private firms with 100 or more employees (EEO-1 filers), approximately 40% of U.S. employees. The mechanism specifically concerns retaliation-driven suppression of formal reporting; effects on informal or anonymous reporting cannot be assessed.

In depth

Q1. Q: What is the core mechanism the paper proposes to explain underreporting?

A: Employers threaten workers with retaliatory firing for engaging in protected activity (filing an EEOC charge). Because the EEOC notifies the named employer within 10 days of receiving a charge, worker anonymity is rarely preserved. When a worker’s outside options are weak — because unemployment is high or UI benefits are thin — the expected cost of a retaliatory firing is higher, raising the severity threshold above which a victim is willing to report. Workers therefore “tough it out” rather than risk their current job.

Q2. Q: How does the paper measure something that is, by definition, not reported?

A: By using the quality of filed charges as a proxy for the degree of underreporting. Under the threshold model, if workers only report when harassment exceeds a higher bar, the average quality of what does get filed must rise. The EEOC’s own merit determination (settlement, withdrawal with benefits, or reasonable-cause ruling) provides an objective, externally-assessed quality measure. An increase in the merit rate signals that the population of filed charges has become more selected — that is, that the unreported fraction has grown.

Q3. Q: What does the 0.5–0.7% figure mean, and what is its interpretation?

A: Each one percentage point increase in a state-industry’s monthly unemployment rate is associated with a 0.5–0.7 percentage point increase in the probability that a filed sexual harassment charge receives a merit designation from the EEOC. This is interpreted as evidence that workers become more selective — filing only more severe cases — as outside options weaken, consistent with higher underreporting at lower harassment thresholds.

Q4. Q: Why did the number of EEOC sexual harassment charges fall by 37% between 2000 and 2015, even as retaliation rates rose?

A: The paper offers the interpretation that firms have become more effective at credibly threatening retaliation to suppress reporting. The 37% volume decline does not imply harassment has diminished; it may reflect a rising fraction of victims staying silent. The authors note the model does not make a prediction about volume because firm behavior is not modeled — volume depends on both worker reporting thresholds and employer conduct.

Q5. Q: Why is North Carolina’s UI reform particularly well-suited as a natural experiment?

A: Four features make it attractive. First, the reform was motivated by trust fund insolvency rather than local labor market conditions, making it more plausibly exogenous to harassment reporting trends. Second, it was implemented during a period of historically high unemployment, when the social safety net was unusually relevant to workers considering risky actions. Third, the cuts affected both the intensive margin (benefit level, down ~35%) and the extensive margin (duration, from 26 to 20 weeks; added eligibility restrictions), with total maximum benefits cut by approximately 50%. Extensive-margin cuts are likely particularly salient for workers worried about a retaliatory firing. Fourth, the cuts to regular UI were permanent and primary, rather than affecting supplemental federal programs.

Q6. Q: What role does industry and establishment gender composition play?

A: The underreporting effect — proxied by the merit-unemployment gradient — is amplified in industries with a larger fraction of male coworkers and in establishments with a higher fraction of male managers. Establishments named in sexual harassment charges have, on average, 2.8 percentage points more male employees and 5 percentage points more male managers than non-respondent establishments. The male-manager underreporting gradient is further amplified by higher unemployment, suggesting gendered power disparities interact with labor market conditions to suppress reporting.

Q7. Q: Does the paper make predictions about the volume of charges, not just their quality?

A: No. The threshold model explicitly does not model firm behavior and makes no prediction about charge volume. Whether volume rises or falls following a labor demand shock is theoretically ambiguous: firms may respond to higher reporting thresholds by escalating harassment (increasing both incidence and severity), or may not respond at all. The identifying assumption requires only that a worker’s willingness to file depends on her outside options and the severity of harassment she experiences — not on firm behavior.

Q8. Q: What is the “value of a statistical harassment” (VSH) figure, and how does it relate to the paper’s motivation?

A: Hersch (2018) estimates the VSH for serious cases at approximately $7.6 million, roughly comparable to the value of a statistical life (VSL). Dahl and Knepper cite this figure to underscore the magnitude of the underreporting problem: with an estimated 5 million workers victimized annually, the social costs of suppressed reporting are substantial. The comparison to VSL motivates why closing the reporting gap matters for welfare, not just legal compliance.

Q9. Q: What is the ex-ante moral hazard interpretation of the UI results?

A: Most UI research focuses on ex-post effects — how benefit generosity affects job search behavior for workers who have already lost their jobs. Dahl and Knepper document an ex-ante moral hazard effect: UI generosity affects the behavior of currently employed workers by changing the expected cost of actions (reporting harassment) that might trigger job loss. Lower UI generosity raises the effective cost of a retaliatory firing, discouraging reporting. This is analogous to, but in the opposite direction from, Lusher et al. (2020), who find that UI expansions reduced productivity among currently employed workers.

Q10. Q: What does the parallel-trends evidence show for the NC difference-in-differences?

A: The paper presents an event study documenting parallel pre-reform trends in the merit rate between North Carolina and control states. The control group is other Southern states that did not change their UI programs during the sample period, excluding AR, FL, GA, and SC (which made changes) and the West South Central division (which exhibited differential pre-trends). The UI recipiency rate tracks closely between NC and control states prior to July 2013, then diverges sharply thereafter, dropping from 33% to 10% in North Carolina within two years — a 59% decline relative to controls.

Key Concepts

Merit determination (EEOC): The EEOC assigns a merit designation to a sexual harassment charge if the named employer settles with the employee, the claimant withdraws the charge upon receipt of benefits, or the EEOC itself determines after investigation that there is “reasonable cause” to believe harassment occurred. As used in this paper, merit designations capture cases where harassment exceeded the legal threshold of a “hostile or offensive work environment” or produced an adverse employment decision — not all cases involving some level of misconduct.

Selectivity of charges: The fraction of filed EEOC sexual harassment charges that receive a merit designation. In the paper’s framework, higher selectivity (a higher merit rate) signals that workers are filing only more severe cases — i.e., that underreporting of less severe cases has increased. Selectivity is used as an observable proxy for the (unobservable) degree of underreporting.

Reporting threshold (ᾱ): In the paper’s threshold model, the minimum level of harassment severity above which a worker will file an EEOC charge. The threshold is determined by the equality between the expected gains from reporting (probability of success times compensation plus elimination of harassment) and the expected costs (probability of retaliation times the gap between current wage and unemployment value). The threshold rises when outside options weaken — either through lower job-finding probabilities or reduced UI benefits.

Outside options: In this paper, the expected value to a worker of becoming unemployed: a weighted average of the wage at a new job (weighted by job-finding probability) and unemployment benefits (weighted by the probability of not finding a job). Outside options determine the cost a worker bears if retaliatory firing follows an EEOC charge. The paper’s two empirical analyses correspond to two separate shocks to outside options: aggregate labor demand (unemployment rate) and institutional safety net generosity (UI benefits).

Retaliation: Defined by the EEOC as punishment for engaging in a protected activity, such as filing a charge. Retaliation arose in 63.4% of all EEOC sexual harassment charges filed between 2000 and 2015 — more than double the rate for non-harassment charges — and rose from 52% of harassment cases in 2000 to 72% in 2015. In the paper’s model, the probability of a retaliatory firing is denoted θ, and is treated as fixed (not a function of harassment severity for tractability).

Ex-ante moral hazard (UI): The effect of UI benefit generosity on the behavior of currently employed workers, rather than on those already unemployed. In this paper’s context, higher UI generosity reduces the cost of a potential retaliatory firing for currently employed workers, making them more willing to report harassment. The North Carolina UI reform provides evidence of this ex-ante channel: when benefits were cut, the selectivity of harassment charges rose, consistent with workers becoming less willing to risk their jobs.

EEO-1 data: A mandatory annual survey of private establishments in the United States with 100 or more employees, covering approximately 40% of all U.S. employees. Collected by the EEOC, these data report the gender, race, and occupational distribution of workers within each establishment. In this paper, the EEO-1 files are linked to EEOC charge microdata to analyze how the gender composition of co-workers and managers moderates both the incidence of reported harassment and the degree of underreporting.

Summary based on IZA Discussion Paper 14740. AI-assisted, human review pending.

American Economic Review | Macro Paper Warehouse

A Theory of Price Caps on Non-Renewable Resources

Layer 1: Overview

In depth

Q1. What is the core conceptual contribution about how a price cap operates?

Q2. Why does a perfect price cap make the producer extract MORE, counter to policymaker intuition?

Q3. What are the four forces in the supply-curve decomposition and what governs them?

Q4. What is the empirical evidence presented, and what is the identification?

Q5. How does the model incorporate market power and how is it endogenous?

Q6. How is the ’leaky’ cap modeled and what is the shut-in strategy?

Q7. What is the welfare and profit impact of a leaky cap?

Q8. How is cap non-credibility (temporariness) modeled?

Q9. What is the sanctions possibility frontier and how is the optimal cap chosen?

Q10. How does this paper relate to and differ from prior work?

Q11. What robustness checks are reported?

Q12. What are the scope conditions and caveats on the policy conclusions?

Key Concepts

Market Opacity and Fragility: Why Liquidity Evaporates When It Is Most Needed

Layer 1: Overview

In depth

Q1. What is the core mechanism that turns a benign illiquidity hike into a liquidity rout?

Q2. How is this an ‘identification’/equilibrium-selection question rather than an empirical one?

Q3. How does the model distinguish a ’liquidity dry-up’ from a ‘flash crash’?

Q4. What does the WAPI measure add and why is it needed?

Q5. What is the role of the contrarian marketable order by second-period hedgers?

Q6. What heterogeneity across equilibria and cohorts is documented?

Q7. What are the welfare results and their scope conditions?

Q8. What is the transparency-versus-dealer-participation trade-off?

Q9. How does the paper relate to and differ from prior fragility literature?

Q10. How does the model map to fragmentation and OTC markets?

Q11. What robustness and extension checks are reported?

Q12. What real-world episodes does the model claim to rationalize, and how is the empirical case made?

Key Concepts

Monetary Policy without Commitment

Layer 1: Overview

In depth

Q1. What is the identification/solution strategy, and what makes the model tractable?

Q2. What is the core economic mechanism generating higher long-run inflation under lack of commitment?

Q3. Why does inflation overshoot in the transition rather than monotonically rise?

Q4. Why are the quantitative magnitudes so large?

Q5. What is the central bank’s reaction function and how does it compare to a Taylor rule?

Q6. How does the comparative static differ between the labor-wedge shock and the elasticity-of-substitution shock?

Q7. What is the welfare comparison and how is welfare measured?

Q8. How does this paper relate to and differ from prior work on credibility and non-linear monetary policy?

Q9. What are the transition dynamics of the macro variables in the calibrated exercise?

Q10. What are the policy implications and their scope conditions?

Q11. What are the main caveats and directions for future research the authors flag?

Key Concepts

Remote Work and City Structure

Layer 1: Overview

In depth

Q1. What is the core economic mechanism, and how does it generate multiple equilibria?

Q2. What is the identification/quantification strategy and its main threats?

Q3. How do the authors rule out competing explanations (pure productivity/preference shocks, congestion, establishment size, occupational shift)?

Q4. What heterogeneity across cities is documented and how does it map to the theory?

Q5. What robustness checks are run?

Q6. How does this paper differ from closely related prior work?

Q7. What are the policy implications and their scope conditions?

Q8. What are the main caveats and abstractions?

Q9. Why is there a discrepancy between the abstract’s welfare figures and per-city numbers?

Key Concepts

Self-Fulfilling Fluctuations in HANK Economies

Layer 1: Overview

In depth

Q1. What is the central claim and how does it overturn the RANK benchmark?

Q2. How is the ’natural rate’ defined here, and how does it differ from standard usage?

Q3. What distinguishes this source of multiplicity from prior determinacy literature?

Q4. How does the paper relate to Ravn and Sterk (2021), the only other HANK global-indeterminacy paper?

Q5. Why isn’t eliminating the untargeted steady state sufficient for global determinacy?

Q6. What is the proposed monetary-policy fix and its scope conditions?

Q7. What is the fiscal-policy alternative and the mechanism?

Q8. Do other standard monetary rules rescue determinacy?

Q9. How robust are the results to the functional form of countercyclical risk?

Q10. Does the multiplicity survive introducing predetermined variables?

Q11. What are the headline calibrated magnitudes and how credible are they?

Q12. What are the policy implications and their caveats?

Q13. What is the broader methodological lesson?

Key Concepts

Taxing Top Wealth: Migration Responses and their Aggregate Economic Implications

Layer 1: Overview