H0 | Macro Paper Warehouse

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.

Changing Opportunity: Sociological Mechanisms Underlying Growing Class Gaps

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

This paper documents sharp divergent trends in intergenerational economic mobility by race and class in the United States across the 1978 to 1992 birth cohorts, and investigates the causal mechanisms driving those changes. The core empirical facts are two: between 1978 and 1992 birth cohorts, the earnings gap between white children from high-income versus low-income families grew by approximately 28–30% (the “white class gap”), while the earnings gap between white and Black children from low-income families shrank by approximately 27–30% (the “white-Black race gap”). These twin trends — growing class gaps and shrinking race gaps — appear consistently across earnings, employment rates, educational attainment, SAT/ACT scores, incarceration, marriage, and mortality, and they hold in nearly every region of the country.

The data are drawn from de-identified federal income tax returns linked to decennial census records and the Numident database, covering 57 million children born between 1978 and 1992, with information on parental and child incomes, employment, marital status, mortality, and residential location, supplemented by ACS educational attainment and linked SAT/ACT records covering 24.8 million students. Children’s outcomes are measured primarily as household income percentile ranks at age 27.

In dollar terms, the white class gap (mean income difference between children raised at the 25th vs. 75th parental income percentile) grew from $17,720 to $20,950 in real 2023 dollars, while the white-Black race gap for low-income families fell from $20,810 to $14,910. The intergenerational rank-rank slope for white children increased from 0.23 to 0.29. The racial gap in intergenerational persistence of poverty — the probability of a child born to the bottom income quintile remaining there — shrank from 14.7 percentage points to 4.1 percentage points (a 72% reduction), driven roughly equally by improvement in Black children’s chances of escaping poverty and deterioration in low-income white children’s chances. The white class gap in early-adulthood mortality more than doubled, while the white-Black race gap in mortality fell by 77%.

The paper systematically rules out three alternative explanations. Observable family characteristics (parental education, wealth, occupation, and marital status) explain only 7% of the growing white class gap and none of the shrinking white-Black race gap. Neighborhood-level common shocks, tested by including childhood county or Census tract-by-cohort fixed effects, similarly explain only 7% of the class gap and none of the race gap. The divergent trends persist even among children raised in the same Census tract, pointing to forces that operate differentially across race and class groups within the same neighborhood.

The paper’s central finding is that changes in children’s outcomes across cohorts are strongly and positively correlated (r = 0.91 across subgroups) with changes in parental employment rates within the child’s social community, defined as families sharing the same race, class, and childhood county. Low-income white communities experienced sharp relative declines in parental employment rates; low-income Black communities experienced relative improvements. These community-level parental employment changes account for nearly all of the divergent trends.

To establish causation, the paper exploits variation in the age at which children move to counties with changing parental employment rates. Children who moved at younger ages (before age 8) to counties where parental employment was increasing experienced larger improvements in earnings than those who moved at older ages (after age 13), consistent with a causal exposure effect with greater impact for longer durations of exposure. Sibling comparisons — comparing outcomes of younger versus older siblings who moved together — confirm that the age gradient reflects causal exposure rather than family-level selection.

The social interaction mechanism is supported by two sources of variation: children’s outcomes are more strongly related to parental employment rates of their own birth cohort than adjacent cohorts (cohort specificity unlikely to be explained by resources), and outcomes are primarily driven by the employment rates of same-race, same-class community members, with cross-racial influence appearing only in counties where cross-racial interaction is greater (counties with small Black population shares or higher interracial marriage rates). The unified explanation the paper proposes is that children’s outcomes mimic those of the adults in their social communities, following Borjas (1992).

Q: What are the precise magnitudes of the growing white class gap and shrinking white-Black race gap in income percentile ranks? A: The white class gap — the difference in mean household income ranks between white children raised at the 25th versus 75th parental income percentiles — increased from 11.1 to 14.1 percentile ranks between the 1978 and 1992 birth cohorts, a 28% increase. The white-Black race gap for children from low-income families fell from 14.9 to 10.9 percentile ranks, a 27% decrease. The intergenerational rank-rank slope for white children increased from 0.23 to 0.29 (a 28% rise in persistence).

Q: How did the trends in poverty persistence versus upward mobility differ? A: The convergence in white-Black outcomes was driven almost entirely by changes in poverty persistence rather than upward mobility. The racial gap in the probability of remaining in the bottom income quintile shrank from 14.7 percentage points to 4.1 percentage points (a 72% reduction), with roughly half from Black children being less likely to remain at the bottom and half from white children being more likely to remain. By contrast, the white-Black gap in the probability of rising from the bottom quintile to the top quintile fell by only 1.9 percentage points (17%).

Q: How widespread geographically were the divergent trends? A: Outcomes declined for low-income white families in nearly every county, but the largest declines occurred in historically high-mobility areas such as the Great Plains and the coasts. For low-income Black families, outcomes improved in most areas, with the largest gains in historically low-mobility regions including the Southeast and the industrial Midwest. The correlation between county-level changes for low-income white versus low-income Black children is a positive 0.58, meaning the areas where Black families improved most tended to be areas where white families declined least, not most.

Q: Do the trends persist when using non-rank, inflation-adjusted dollar outcomes? A: Yes. The white class gap in mean household income grew from $17,720 to $20,950 in real 2023 dollars, and the white-Black race gap for low-income families narrowed from $20,810 to $14,910. The paper also reports similar patterns for individual earnings (as opposed to household income), ruling out changes in household composition as a driver.

Q: What do the pre-labor-market outcomes show? A: The divergent trends emerge before children enter the labor market. The white class gap in educational attainment grew by 20%, driven by growing gaps in four-year college completion. The white-Black race gap in educational attainment disappeared by the 1992 cohort, driven by narrowing gaps in high school graduation. The white class gap in the share of students taking the SAT/ACT increased by 12.1 percentage points between the 1980 and 1991 birth cohorts, while the white-Black race gap in SAT/ACT-taking decreased by 20.3 percentage points. The white class gap in mean SAT/ACT scores grew by 62% between the 1980 and 1997 birth cohorts among test-takers.

Q: How large is the mortality dimension of these trends? A: The white class gap in early-adulthood mortality (ages 24–27) more than doubled between the 1978 and 1992 birth cohorts, while the white-Black race gap in early-adulthood mortality decreased by 77%. These non-monetary outcomes are invariant to inflation and income measurement choices, confirming the robustness of the broader trends.

Q: How much do family-level characteristics explain? A: Controlling jointly for parental education, wealth, occupation, and marital status reduces the estimated growth in the white class gap by only 7% (from 3.37 to 3.13 percentile ranks). The same controls do not explain the shrinking white-Black race gap — the estimated reduction in the race gap actually becomes slightly larger (4.56 rather than 4.16 percentiles) after controlling for family characteristics, indicating that observable family factors work against the observed convergence.

Q: How much do neighborhood-level common shocks explain? A: Including childhood county fixed effects interacted with birth cohort explains only 7% of the growing white class gap and none of the shrinking white-Black race gap. Including Census tract fixed effects yields essentially identical results. The divergent trends persist among children growing up in the same Census tract, ruling out explanations based on differential exposure to neighborhood-level economic shocks.

Q: What is the community-level parental employment correlation, and what does it explain? A: Changes in children’s earnings, SAT/ACT scores, and educational attainment across cohorts are strongly positively correlated with changes in parental employment rates within the child’s community (same race, same class, same county), controlling for the employment status of the child’s own parents. The correlation between changes in children’s outcomes and changes in community parental employment rates across all race and class subgroups is 0.91. This single community-level factor — as proxied by parental employment rates — accounts for nearly all of the divergent trends by race and class.

Q: What is the quasi-experimental design for estimating causal effects, and what does it assume? A: The paper compares outcomes of children who moved to counties with increasing parental employment rates at younger versus older ages, across earlier versus later birth cohorts. The identification assumption is “constant selection by age”: any selection of families into moving to a given county in years when parental employment is higher may differ across cohorts, but those selection differences must not themselves vary systematically with the age at which children move. The paper treats this as a “constant selection by age” assumption standard in the neighborhood effects literature.

Q: What do the causal exposure results show? A: Children who moved before age 8 to communities where parental employment was increasing show systematically higher earnings in later birth cohorts, while children who made the same move after age 13 show little difference in earnings across cohorts. This pattern — larger effects at younger ages — is consistent with a causal exposure effect of growing up in an improving community, with effects proportional to the duration of exposure.

Q: How do sibling comparisons validate the identification assumption? A: When siblings move together to a community with increasing parental employment rates, the younger sibling — who receives more years of exposure to the higher-employment environment — earns significantly more than the older sibling. The earnings difference is proportional to the age gap between siblings. This rules out explanations based on fixed unobserved family characteristics and supports the constant-selection-by-age assumption.

Q: What evidence distinguishes social interaction mechanisms from economic resource mechanisms? A: Two sources of variation are used. First, children’s outcomes are much more strongly related to the parental employment rates of peers in their own birth cohort than peers in adjacent cohorts — a cohort-specificity that is implausible for economic resource channels (school budgets, local tax bases) which would not vary sharply across adjacent cohorts. Second, outcomes of low-income white children are driven primarily by the employment rates of low-income white parents, not by low-income Black or high-income white parents’ employment rates, and vice versa for low-income Black children — consistent with interaction patterns being stratified by race and class.

Q: What role does cross-racial interaction play? A: In counties where Black children constitute a small share of the population (making cross-racial interaction more likely), Black children’s outcomes are also related to low-income white parental employment rates. Similarly, in counties with higher interracial marriage rates (a proxy for cross-racial interaction), Black children’s outcomes are related to white parental employment rates even after controlling for racial composition. This cross-sectional variation supports the interpretation that the influence channel is social interaction rather than parallel economic shocks.

Q: How do the findings for Hispanic, Asian, and AIAN children compare? A: Changes in economic mobility for Hispanic, Asian, and AIAN children between 1978 and 1992 birth cohorts were much more modest than for white and Black children. For children from low-income families, mean household income ranks were essentially unchanged for Asian children and rose by only about 0.5 percentiles for Hispanic and AIAN children. However, the same community-level parental employment rate mechanism explains the (smaller) changes for these groups as well; the correlation between changes in children’s outcomes and changes in community parental employment rates is 0.91 across all subgroups.

Q: What is the paper’s unified theoretical account of all the divergent trends? A: The paper concludes that a parsimonious theory — that children’s outcomes mimic those of the parents in their social communities, following Borjas (1992) — explains the divergent trends by race and class. Because social interaction is stratified by race and class even within neighborhoods, changes in parental outcomes in the parent generation propagate differentially to white versus Black and high-income versus low-income children, producing growing class gaps and shrinking race gaps through the same underlying mechanism.

Q: What does the paper imply about the malleability of economic mobility disparities? A: Because the causal exposure effects of community environments on children’s outcomes can be detected within a 14-year span (1978 to 1992 birth cohorts), the paper implies that differences in economic mobility by race and class may be malleable in policy-relevant timeframes. This is despite the fact that long-standing disparities partly trace back to historical factors such as slavery, Jim Crow laws, redlining, and the Great Migration.

White class gap: The difference in mean household income ranks in adulthood for white children born to families at the 25th versus 75th percentiles of the national parental income distribution; increased from 11.1 to 14.1 percentile ranks (28%) between the 1978 and 1992 birth cohorts.

White-Black race gap: The difference in mean household income ranks in adulthood for white versus Black children born to families at the 25th percentile of the national parental income distribution; decreased from 14.9 to 10.9 percentile ranks (27%) between the 1978 and 1992 birth cohorts.

Social community: In this paper’s usage, other families who share the same race, class category, and childhood county as a given child; the unit within which community-level parental employment rates are measured and found to be predictive of children’s outcomes.

Causal exposure effect: The effect on a child’s adult outcomes of an additional year spent growing up in a community with higher parental employment rates, estimated quasi-experimentally by comparing children who moved to counties with changing parental employment rates at younger versus older ages; larger effects at younger ages imply a causal, duration-sensitive exposure channel.

Constant selection by age: The identification assumption underlying the quasi-experimental design; requires that any systematic differences in the types of families who move to a county when parental employment is high versus low do not themselves vary with the age at which children move to that county.

Intergenerational rank-rank slope: The OLS slope coefficient from regressing child income percentile rank on parental income percentile rank; for white children, increased from 0.23 in the 1978 birth cohort to 0.29 in the 1992 birth cohort, indicating greater persistence of economic status.

Cohort-specificity of community effects: The empirical pattern that children’s outcomes are more strongly related to the parental employment rates of peers in their own birth cohort than those of adjacent cohorts, used in the paper as evidence favoring social interaction over economic resource channels as the mediating mechanism.

Firm Accommodation After Workplace Disability: Labor Market Impacts and Implications for Subsidy Design

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

Layer 1 — Overview

Research Question

This paper studies (1) how firm accommodation decisions respond to financial incentives in the context of workplace disability under workers’ compensation, (2) what the causal effect of accommodation is on workers’ subsequent labor market outcomes, and (3) whether the equilibrium level of accommodation is socially efficient, and what the welfare implications of wage subsidies for accommodation are.

Empirical Context and Data

The analysis uses the universe of Oregon workers’ compensation claims from 2005 through 2017 — over 131,000 disabling claims — linked to longitudinal quarterly earnings records from the Oregon Employment Department. The setting exploits Oregon’s Employer at Injury Program (EAIP), which subsidizes employers who provide “transitional work” accommodations (primarily through wage subsidies) to workers with temporary workplace disabilities. EAIP accounts for roughly 25 percent of claims on average, with the wage subsidy component representing over 96 percent of EAIP expenses.

Identification Strategy

The authors exploit a policy change in July 2013 that reduced the EAIP wage subsidy rate from 50 percent to 45 percent. They construct a firm-level “exposure” measure — the fraction of a firm’s claims that used EAIP in a baseline period (2005–2009) — and estimate a continuous difference-in-differences specification in which the interaction of exposure and a post-2013 indicator instruments for accommodation. The identifying assumption is strong parallel trends: firms with low baseline exposure are unlikely to respond to the subsidy reduction, while high-exposure firms respond more, generating cross-firm variation in accommodation rates after 2013. An MTE framework (Heckman and Vytlacil 2005) is then used to explore heterogeneous treatment effects along an unobserved resistance-to-treatment dimension.

Main Empirical Findings

The subsidy reduction from 50% to 45% decreased accommodation rates by 2.9 percentage points (9.3 percent) for claims in firms with average exposure, implying a subsidy elasticity of accommodation of 0.9.
The policy change led to a 0.95 percentage point decrease in employment and a $120 decrease in quarterly earnings four quarters after disability for claims in average-exposure firms (roughly 1.3–1.5 percent declines relative to means), with no significant effect on worker turnover to other firms.
IV estimates of the effect of accommodation itself (using predicted EAIP as instrument) show accommodation increases the probability of employment four quarters after disability by 33 percentage points and increases quarterly earnings by approximately $4,100.
The MTE analysis reveals negative selection on gains: workers with workplace disabilities who are least likely to receive accommodation have the highest potential gains from it, driven largely by severe disabilities with high accommodation costs.
Descriptive and IV evidence is consistent with accommodation operating primarily as general human capital investment: accommodation has no statistically significant effect on the probability of moving to a new firm, and earnings gains are not systematically lower for workers who change employers after accommodation.

Structural Model and Counterfactual Findings

A two-period frictional labor market model with risk-averse workers, risk-neutral firms, Nash bargaining, imperfect experience rating in workers’ compensation, and firm accommodation as human capital investment is developed and estimated. Two inefficiency sources are identified: (1) a human capital externality — because accommodation builds general human capital, firms cannot capture the full surplus when workers separate, reducing accommodation incentives; and (2) a fiscal externality — imperfectly experience-rated firms do not fully internalize the workers’ compensation cost savings from accommodation, further depressing it below the efficient level. Counterfactual simulations show:

Eliminating wage subsidies (from 50% to 0%) reduces accommodation rates from 33% to 11%, leading to a 7% decline in post-disability employment and a 15% decline in post-disability quarterly wages (roughly $1,358).
A revenue-neutral reform eliminating wage subsidies reduces average welfare and the welfare of more than 90% of workers.
Welfare gains from the subsidy are larger for low-skilled workers than high-skilled workers.
Conditional on experiencing disability, eliminating wage subsidies decreases welfare by about 10%, while increasing the subsidy to 100% raises welfare for disabled workers by around 30%.
Firm profit is maximized at a subsidy rate around 80%, after which higher taxes offset accommodation gains.

In depth

Q1. What is the Employer at Injury Program (EAIP), and how does it differ from standard workers’ compensation?

A1: EAIP is an optional component of Oregon’s workers’ compensation system that subsidizes employers for the costs of accommodating workers with temporary disabilities during a transitional return-to-work period. Unlike standard workers’ compensation premiums (which are experience-rated at the firm level), EAIP is funded through a flat payroll tax on all firms that is not experience-rated — meaning firms that use EAIP do not pay higher premiums. The wage subsidy component accounts for over 96 percent of EAIP expenses; other reimbursable costs (worksite modifications up to $5,000, retraining up to $1,000, clothing up to $400) are rarely used. Eligible employers must be the employer at which the disability occurred, and accommodation is limited to a transitional period during which workers cannot simultaneously receive time-loss benefits.

Q2. How is firm-level “exposure” constructed, and what is the rationale for using it as an instrument?

A2: Exposure is the fraction of a firm’s workers’ compensation claims that used EAIP during a five-year baseline period from 2005 to 2009 — a separate historical period chosen to reduce volatility and avoid mean-reversion. The rationale draws on prior work (Aizawa et al., 2022) showing that firm fixed effects account for nearly 25 percent of variation in accommodation, far more than worker or disability characteristics (1 and 3 percent, respectively), suggesting permanent firm-level heterogeneity in the relative benefits and costs of accommodation. Firms with zero historical exposure are unlikely to change accommodation behavior in response to a subsidy reduction, while high-exposure firms respond more, creating differential quasi-experimental variation in accommodation rates after July 2013.

Q3. What are the first-stage and reduced-form results from the DID specification?

A3: The first-stage DID coefficient shows that a ten-percentage-point increase in exposure is associated with a one-percentage-point decrease in EAIP take-up after 2013, implying a 2.9 percentage point decrease for claims in firms with average exposure (mean 0.27). The corresponding reduced-form results show a 0.35 percentage point decrease in employment four quarters post-disability and a $45 decrease in quarterly earnings for every ten-percentage-point increase in exposure, scaling to 0.95 percentage points and $120 at average exposure. There is no statistically significant effect on the probability of moving to a new firm. Pre-trend tests show parallel accommodation trends across exposure terciles prior to 2013, supporting the identifying assumption.

Q4. What do the IV estimates imply about the causal effect of accommodation on labor market outcomes?

A4: Under the exclusion restriction that the subsidy change affects labor market outcomes only through accommodation, the IV estimates imply that receipt of accommodation increases the probability of employment four quarters after disability by 33 percentage points (against a mean of 72 percent) and increases quarterly earnings by approximately $4,100 (against a mean of $7,807). There is no significant effect on the probability of working at a new firm four quarters later. The authors note these large estimates reflect local average treatment effects for compliers — workers whose accommodation status was changed by the instrument — who disproportionately have high unobserved resistance to treatment and high accommodation returns, explaining the magnitude.

Q5. What does the MTE framework reveal about the distribution of accommodation effects and selection?

A5: The MTE curves show that workers with the highest unobserved resistance to treatment (least likely to receive accommodation) have the highest potential employment and earnings gains from accommodation. This negative selection on gains arises because these workers tend to have worse employment outcomes in the untreated state, consistent with more severe disabilities commanding higher accommodation costs. IV weights are concentrated at high-resistance values, explaining the large IV estimates. Negative selection on gains is also found along observable dimensions: workers in self-insured firms, healthcare support occupations, women, and those with wounds/cuts/burns show larger gains but lower likelihood of receiving accommodation.

Q6. What evidence supports characterizing firm accommodation as general rather than firm-specific human capital investment?

A6: Three pieces of evidence point toward general human capital. First, the IV estimate shows accommodation has no statistically significant effect on the probability of working at a new firm four quarters after disability. Second, a triple-interaction specification (DID interacted with new-firm indicator) yields suggestive evidence of even larger earnings gains for workers who move to a new firm post-accommodation, though this is not statistically significant — a pattern inconsistent with firm-specific human capital. Third, the subset of claims that receive non-wage EAIP benefits (worksite modifications, retraining) do show lower mobility, but this comprises fewer than 5 percent of the sample, meaning the predominant form of investment in the context is general in nature.

Q7. What are the two sources of market inefficiency in accommodation identified in the model?

A7: The first is a human capital externality operating through worker turnover. Because accommodation builds general human capital that workers carry to new employers, a firm accommodating a worker does not capture the portion of future surplus that accrues to future employers upon separation. In a Nash bargaining framework with lack of commitment, this dynamic inefficiency is larger when industry-wide turnover rates are higher — consistent with the descriptive finding that accommodation rates are strongly negatively associated with industry separation rates. The second is a fiscal externality from imperfect experience rating: firms whose workers’ compensation premiums are not fully linked to their own claim costs do not fully internalize the cost-savings from accommodation (i.e., reduced time-loss benefit payments), leading them to accommodate at inefficiently low rates.

Q8. How is heterogeneity incorporated in the structural estimation, and what do the estimated parameters show?

A8: The model incorporates observed heterogeneity (firm insurance status, worker skill type — measured by pre-disability wages — firm baseline exposure, and pre/post policy change) and unobserved heterogeneity mapped to the MTE framework’s unobserved resistance to treatment. Indirect inference matches cross-sectional accommodation rates, earnings by subgroup, and the DID coefficients. Key findings: net output during the disability period is negative (accommodation is a costly short-run investment), while post-disability output is higher for accommodated workers. Low-skilled workers experience larger productivity gains from accommodation than high-skilled workers. Accommodation cost shock variance is lower for higher unobserved types, meaning high-gain workers are also more sensitive to subsidy changes, consistent with the large IV estimates. The model fits the DID coefficients for accommodation, employment, and wages well.

Q9. What do the counterfactual simulations show about the welfare effects of varying the subsidy rate?

A9: Eliminating wage subsidies from the current 50% rate reduces the accommodation rate from 33% to 11% and lowers post-disability employment by 7 percentage points and post-disability quarterly wages by 15% ($1,358). From a welfare perspective, eliminating subsidies in a revenue-neutral reform reduces average ex-ante worker welfare and lowers welfare for more than 90% of workers. Conditional on experiencing disability, eliminating subsidies reduces welfare by about 10% while raising the subsidy to 100% increases welfare of disabled workers by around 30%. Firm profit is increasing in the subsidy rate up to about 80%, then decreases. Ex-ante worker welfare gains from the current 50% subsidy relative to no subsidy are modest in consumption-equivalent terms (at most 0.6% increase in consumption), partly because the disability probability is low (2.2%) and because unaccommodated workers still receive two-thirds wage replacement through time-loss benefits.

Q10. What distributional implications do wage subsidies have across worker and firm types?

A10: Welfare gains from higher wage subsidies are larger for low-skilled workers than high-skilled workers, so the subsidy has a redistributive dimension beyond efficiency correction. Welfare gains are also larger for workers in imperfectly experience-rated firms, where the fiscal externality creates the greater wedge from the efficient level. Self-insured firms, which already internalize workers’ compensation cost savings and thus accommodate closer to the optimal rate, benefit less from the subsidy and can even be made worse off if subsidies are set very high (since they bear higher flat payroll taxes with smaller marginal accommodation gains). The fraction of worker-firm matches experiencing welfare gains exceeds 90% under the benchmark subsidy level, indicating broad rather than narrowly concentrated gains.

Q11. How do the experience-rating channel and the worker-turnover channel interact in comparative statics?

A11: Model comparative statics show that reducing the job-to-job transition rate of workers with disabilities to one-quarter of its estimated value substantially raises accommodation rates, and this effect is more pronounced for imperfectly experience-rated firms than for self-insured firms. This occurs because self-insured firms already have a strong incentive to accommodate (to reduce workers’ compensation premiums), so turnover is less marginal for them. Forcing all firms to be self-insured (perfect experience rating) would substantially increase accommodation rates in currently imperfectly rated firms. Lowering the accommodation cost during the disability period (increasing net output during the disability period) also raises accommodation rates for both firm types.

Key Concepts

Firm Accommodation (EAIP): In this paper’s specific sense, accommodation refers to a firm’s decision to offer a worker with a temporary workplace disability “transitional work” — alternative tasks, modified duties, or flexible arrangements — during their recovery period, funded in part through Oregon’s Employer at Injury Program wage subsidy. Accommodation is distinct from simple early return to work; it functions as a form of human capital investment by potentially providing skill development opportunities and preventing human capital depreciation.

Exposure (Instrument): A firm-level continuous measure defined as the fraction of a firm’s workers’ compensation claims that used EAIP during a five-year baseline period (2005–2009). Exposure captures permanent, time-invariant firm-level propensity to accommodate, and is used to construct a difference-in-differences instrument for the causal effect of accommodation by interacting exposure with a post-2013 indicator (when the subsidy rate was cut from 50% to 45%).

Imperfect Experience Rating: The degree to which a firm’s workers’ compensation insurance premium adjusts to reflect that firm’s own claims costs, rather than being set at an industry average. Fully experience-rated (self-insured) firms internalize 100% of claim costs and thus have strong incentives to accommodate. Partially experience-rated firms face a fiscal externality: because their premiums do not fully reflect their own time-loss benefit expenditures, they do not capture all the cost savings from accommodating workers, leading to under-accommodation relative to the social optimum.

Human Capital Externality (Dynamic Inefficiency in Accommodation): The mechanism — analogous to Acemoglu and Pischke (1999) and Fang and Gavazza (2011) — by which worker turnover reduces firms’ incentives to invest in general human capital (here, accommodation). When accommodation raises workers’ general productivity, part of the future surplus from this investment accrues to future employers upon job-to-job separation. With Nash bargaining and lack of commitment (re-bargaining in the second period), the accommodating firm cannot capture this surplus, creating a dynamic inefficiency that is more severe in high-turnover industries.

Negative Selection on Gains: The empirical finding, established via the MTE framework, that workers with workplace disabilities who are least likely to receive accommodation (highest unobserved resistance to treatment) have the largest potential employment and earnings gains from accommodation. This pattern arises because workers with more severe disabilities have high accommodation costs (making firms unwilling to accommodate them) but also face far worse counterfactual labor market outcomes without accommodation, creating large potential gains.

Marginal Treatment Effect (MTE): Following Heckman and Vytlacil (2005), the treatment effect of accommodation evaluated at a specific quantile of unobserved resistance to treatment — defined here as the propensity score value at which a worker is indifferent between treatment and non-treatment. The MTE curve maps out the full distribution of treatment effects and reveals who benefits (and by how much), how IV estimates are weighted averages over this distribution, and which compliers drive the large IV estimates.

General vs. Firm-Specific Human Capital (in Accommodation Context): Accommodation is characterized as general human capital investment if the productivity and earnings gains it produces are transferable across employers — i.e., if accommodated workers who move to new firms retain their wage gains. It is firm-specific if gains are tied to the current match. In this paper, general human capital is supported by the null effect of accommodation on new-firm employment probability, suggestive evidence of non-lower (possibly larger) earnings gains for new-firm movers, and the observation that fewer than 5% of claims use non-wage EAIP benefits associated with firm-specific investment.

Revenue-Neutral Counterfactual: A counterfactual policy experiment in which the wage subsidy rate for accommodation is varied while imposing that both the time-loss benefit program and the EAIP wage subsidy program remain budget-balanced. Higher subsidy rates raise firm accommodation, reduce time-loss benefit payouts (lowering base premiums for imperfectly experience-rated firms), but require a higher flat EAIP payroll tax on all firms, some of which is passed through to workers via lower first-period wages.

Selection in Surveys: Using Randomized Incentives to Detect and Account for Nonresponse Bias

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

This paper addresses nonresponse bias in surveys — the distortion that arises when survey participants differ systematically from nonparticipants in ways that correlate with the survey’s outcomes of interest. The authors develop and apply methods to detect and correct for nonresponse bias using randomized financial incentives embedded in the survey design itself.

The empirical application is the “Norge i Koronatid” (NiK) survey, conducted by Statistics Norway in April–May 2020 to study the immediate labor market consequences of Norway’s COVID-19 lockdown. The NiK survey has two features that make it unusually well-suited for studying nonresponse bias: (1) it is linked to full-population administrative data, providing a verifiable ground truth for the entire Norwegian adult population; and (2) survey invitees were randomly assigned to one of five financial incentive levels (0%, 1%, 5%, 7%, or 10% probability of receiving a 1,000 NOK prepaid card), generating exogenous variation in participation rates. The final sample of 10,000 randomly drawn adults achieved a 47.4% participation rate.

The administrative data reveal large, statistically significant nonresponse bias across all six labor market outcomes examined. Participants in the high-incentive arm had on average roughly 930 USD (30%) higher monthly pre-lockdown earnings than the full population, and were 10.8 percentage points (19%) more likely to be employed. Standard corrections for selection on observable characteristics — including propensity-score reweighting on age, gender, immigration status, schooling, and municipality-level variables — fail to eliminate this bias. For the high-incentive arm, reweighting on individual characteristics more than doubles the nonresponse bias for earnings loss and employment loss measures relative to unweighted estimates, meaning that observable-based corrections can make things worse, not better.

A key finding is that higher participation rates do not imply lower nonresponse bias. The high-incentive arm, with the highest response rate, exhibited larger nonresponse bias than the no-incentive arm. Marginal participants — those induced to respond by higher incentives — had much stronger pre-lockdown labor market attachment (average earnings of 6,806 USD/month vs. 3,666 USD/month for inframarginal participants) but suffered substantially greater lockdown impacts: 32.3% became furloughed or unemployed versus only 3.4% of inframarginal participants.

Existing methods designed to handle selection on unobservables also perform poorly. Worst-case (Manski) bounds contain the truth but are very wide: employment before lockdown is bounded between 30% and 83% against a true value of 57%. Monotone response selection assumptions produce bounds that do not contain the population quantities for any of the six outcomes, because the marginal survey response function is empirically non-monotone. A Heckman parametric selection model produces point estimates inconsistent with the ground truth (e.g., estimating 51% pre-lockdown employment against the true 57%).

Investigation of participation timing reveals that reminder emails attract a qualitatively different type of respondent than incentives do. This motivates the paper’s central methodological contribution: a two-dimensional participation model that distinguishes “active” nonparticipants (those who received the invitation and chose not to respond because the incentive was insufficient) from “passive” nonparticipants (those who never received or attended to the invitation but who may respond to reminders). These two groups have labor market outcomes that differ from participants in opposite directions, which is why single-dimensional monotone selection models fail. The two-dimensional model, exploiting both incentive randomization and the timing of responses, produces bounds that contain or are closer to the ground truth than all other methods examined — for example, bounding pre-lockdown employment at [48%, 63%] around the true value of 57%.

The paper is scoped to a high-quality, randomly sampled, administrative-data-linked survey conducted during a period of acute economic disruption. The authors note the patterns observed may differ outside crisis periods, though the methods developed apply generally.

Q: How prevalent is nonresponse bias discussion in economics research, and what methods do researchers currently use? A: A systematic review of survey-based papers in top-five economics journals from January 2015 to August 2020 found that nearly half of studies omit any discussion of nonresponse bias despite often high nonresponse rates. Among studies using researcher-collected survey data, the average nonresponse rate is 50%; rates reach as high as 87%. When researchers do address nonresponse, 47% of own-survey papers compare sample means to a reference population and 16% apply reweighting on observables; virtually none use methods that address selection on unobservables.

Q: How was the NiK survey designed to enable testing for nonresponse bias? A: The 10,000-person random sample was assigned to five incentive groups with probabilities of receiving a 1,000 NOK credit card set at 0%, 1%, 5%, 7%, and 10%, yielding expected payoffs ranging from 1.1 USD to 11 USD. Because group assignment was random, the groups are probabilistically identical ex ante, so differences in average responses across groups — given an exclusion restriction that incentives do not directly affect answers — provide a direct test for nonresponse bias. Participation rates across the aggregated no/low/high incentive groups were 45.7%, approximately 47.6%, and approximately 51.7%, respectively; the joint test of equal participation across groups rejects with p-value < 0.01.

Q: How large is nonresponse bias in the NiK survey as measured against the administrative ground truth? A: Across all six administrative outcomes and all three incentive arms, joint tests of no nonresponse bias are rejected with p-values < 0.01. High-incentive arm participants had pre-lockdown monthly earnings roughly 930 USD (30%) above the population mean, and were 10.8 percentage points (19%) more likely to be employed. The high-incentive arm’s estimated post-lockdown employment rate of 58% overstates the true rate by 8 percentage points; a researcher comparing this to the true pre-lockdown rate of 57% would erroneously conclude employment was essentially unchanged, when in fact it dropped 7 percentage points.

Q: Does correcting for observable characteristics remove nonresponse bias? A: No. After reweighting by propensity scores constructed from age, gender, immigration status, schooling, and municipality or individual-level characteristics, joint tests of zero remaining nonresponse bias are rejected with p-values < 0.01 for each specification and incentive arm. In some cases, reweighting on individual characteristics more than doubles the nonresponse bias — for example, for earnings loss and employment loss measures in the high-incentive arm — meaning that standard observable-based corrections can amplify rather than reduce bias. Robustness checks using machine learning algorithms, class weights, imputation, and richer covariate sets including lagged outcomes yield the same conclusion.

Q: Does nonresponse bias in survey responses (not just administrative outcomes) differ across incentive arms? A: Yes. For survey-elicited outcomes, average responses differ significantly across incentive arms, with all joint equality tests rejected at p < 0.1. For example, 10.4% of high-incentive participants reported applying for UI benefits versus 7.5% in the no-incentive group. Estimated UI expenditure as a share of Norway’s 2020 social insurance budget varies from 13.2% (no-incentive arm) to 18.4% (high-incentive arm), illustrating the policy stakes.

Q: Do higher response rates reduce nonresponse bias? A: Not in this survey. The no-incentive arm, with the lowest participation rate (45.7%), exhibits smaller nonresponse bias than the high-incentive arm (51.7% participation). This finding contradicts standard guidance from the U.S. Office of Management and Budget and J-PAL research guidelines, which equate higher response rates with lower bias risk. The authors note that J-PAL has subsequently updated its guidance in response to this paper’s findings.

Q: How do marginal participants (induced by higher incentives) differ from inframarginal participants? A: Marginal participants — those who participate only under high incentives but not without them — had average pre-lockdown monthly earnings of 6,806 USD versus 3,666 USD for inframarginal participants (p-value 0.08), indicating much stronger pre-lockdown labor market attachment. Post-lockdown, both groups had similar earnings (approximately 3,600–3,800 USD/month). Consistent with this, 32.3% of marginal participants became furloughed or unemployed after the lockdown versus 3.4% of inframarginal participants. Notably, marginal and inframarginal participants do not differ significantly on observable background characteristics (age, gender, immigrant status, schooling; joint test p-value 0.70), confirming that selection is on unobservables.

Q: Why do existing methods designed to handle selection on unobservables fail? A: Worst-case (Manski) bounds contain the truth but are too wide to be informative — pre-lockdown employment is bounded at [30%, 83%] against a true value of 57%. Adding randomized incentives as instruments tightens bounds only modestly (8.5% width reduction for employment before lockdown). Monotone response selection assumptions fail because the empirically estimated marginal survey response function is non-monotone: for employment, the probability first decreases and then increases as a function of willingness-to-participate. The Heckman parametric selection model gives point estimates inconsistent with the ground truth for most outcomes (e.g., 51% estimated pre-lockdown employment vs. 57% true).

Q: What motivates the two-dimensional participation model? A: Analysis of participation timing shows that reminder emails attract a qualitatively different type of respondent than incentives alone. Reminders have a larger proportional effect on participation in the no-incentive group than in the high-incentive group, both in absolute and proportional terms. Early respondents (responding to initial contact) had lower pre-lockdown earnings and employment than late respondents (responding to reminders). This implies that the two types of unobservables — resistance to incentive and probability of receiving the invitation — are associated with outcomes that move in opposite directions, producing a non-monotone marginal survey response function that single-dimensional models cannot capture.

Q: How does the two-dimensional model work and what are its results? A: The model distinguishes active nonparticipants (saw the invitation, declined because the incentive was too low — more likely to be employed and higher earners) from passive nonparticipants (did not receive or attend to the invitation — more likely to have been adversely affected by the lockdown). By exploiting both the randomized incentive variation and the timing of responses (initial contact vs. reminder), the model partially identifies population mean outcomes under shape restrictions on the joint distribution of the two unobservables. For pre-lockdown employment, the model produces bounds of [48%, 63%] bracketing the true value of 57%, compared to worst-case bounds of [34%, 83%] and monotone selection bounds that do not contain the truth. Improvements are largest for pre-lockdown levels outcomes where the two types of nonparticipants differ most.

Q: What are the practical recommendations for survey researchers? A: Embedding randomized incentives in surveys at little or no additional cost enables an inexpensive test for nonresponse bias that does not require linked administrative data. When such a test detects bias, researchers should apply the two-dimensional model rather than relying on observable-based reweighting or conventional selection models. The question of who participates matters at least as much as how many participate; surveys should be designed to characterize and correct for selection, not merely to maximize response rates.

Nonresponse bias: The difference between the mean response among survey participants and the true population mean, arising when the decision to participate is correlated with the outcome of interest. Distinct from sampling bias; it persists even with a randomly drawn sample.

Selection on unobservables: Nonresponse bias that remains after conditioning on all observed characteristics. In the NiK survey, marginal and inframarginal participants are indistinguishable on observable demographics but differ dramatically in labor market outcomes, providing direct evidence that unobservables drive selection.

Marginal vs. inframarginal participants: Under the Imbens-Angrist monotonicity condition, inframarginal participants would respond at any incentive level; marginal participants respond only at higher incentive levels. Their average responses are separately identified using an IV regression with the incentive as instrument.

Marginal survey response (MSR): The function m(u) = E[Y*_i | U_i = u], giving the average outcome for individuals at the uth quantile of willingness to participate. The MSR is nonparametrically identified for u in [0, p(z_high)]; its empirically non-monotone shape in the NiK data explains why monotone selection assumptions produce bounds that miss the ground truth.

Active vs. passive nonparticipants: Active nonparticipants received the survey invitation and declined because the incentive was insufficient; they tend to have higher labor market attachment. Passive nonparticipants never received or attended to the invitation but may respond to reminders; they tend to have been more adversely affected by the lockdown. This distinction motivates the two-dimensional model.

Two-dimensional participation model: A model of survey participation with two unobservables — resistance to incentive (determining active nonresponse) and probability of receiving the invitation (determining passive nonresponse). By exploiting both incentive randomization and the timing of responses (initial contact vs. reminder), the model produces bounds or point estimates on population means that are narrower and closer to ground truth than single-dimensional alternatives.

Exclusion restriction for incentives: The assumption that randomly assigned incentives affect participation rates but do not directly affect participants’ answers to survey questions. This is required for incentives to serve as valid instruments for testing and correcting nonresponse bias; the authors test and find no evidence that it is violated.

The Social Tax: Redistributive Pressure and Labor Supply

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

Layer 1 — Overview

Research Question

This paper asks whether informal redistributive pressure — the social obligation to share earned income with kin and social networks — distorts labor supply in low-income communities. The authors conceptualize such pressure as a “social tax” on earnings and develop the first direct causal test of whether it reduces labor supply, output, and earnings among full-time workers.

Setting and Sample

The study works with 474 full-time piece-rate factory workers (464 of whom are women) employed in cashew processing plants run by Olam in Côte d’Ivoire. Workers are paid biweekly in cash entirely through piece rates for individual nut-peeling output, creating a direct mapping between labor supply and income. At baseline, workers report transferring 25–35% of their income to individuals outside their household, with 77% having made at least one transfer in the previous 3 months. Workers also strongly believe that earning more triggers more transfer requests: 77% agree that if someone starts earning more by working harder, people will ask that person more often for financial help.

Intervention

The authors introduce a blocked savings account into which workers can deposit any earnings above a self-chosen threshold (set at least as high as their own baseline average earnings). Earnings above the threshold are automatically deposited by the factory directly into the account with the Banque Populaire de Côte d’Ivoire; the cash component of pay is unchanged. Funds cannot be withdrawn until the end of the blocked period (9 months in Phase 1; 3 months in Phase 2). The key design feature is that the account reduces the effective social tax rate only on earnings increases above baseline, thereby eliminating income effects and generating only a pure substitution effect — an unambiguous positive prediction on labor supply if a social tax exists.

Experimental Design

Workers are randomized into three conditions: (1) Control (no account); (2) Private account (existence unknown to anyone outside the worker); (3) Non-private account (existence and forthcoming unblock date revealed to network members via promotional text messages). The contrast between Private and Non-private isolates the role of redistributive pressure specifically — holding constant all other features of the blocked account product. The experiment runs in two cross-randomized phases conducted between 2018 and 2019.

Main Findings

Take-up of blocked accounts is dramatically higher when accounts are private: 60% in Phase 2 (Private) versus 14% (Non-private), a 77% decline (p<0.001). Among workers who declined Non-private accounts, 96% cite anticipated increases in transfer requests as an important factor.

Being offered a Private account sharply raises labor supply. Pooling both phases, the Private arm increases average daily earnings by 175.9 FCFA, or 11.4% (p=0.012), relative to Control or Non-private arms. This is accompanied by a 6.2 percentage point (9.7%) increase in daily work attendance (p=0.023), with the entire attendance effect driven by reduced absenteeism rather than turnover. Effects in Phase 1 (Private vs. Control: +11.3%, p=0.032) and Phase 2 (Private vs. Non-private: +11.5%, p=0.043) are nearly identical in magnitude, indicating the results are not sensitive to cross-phase design. The treatment effect magnitude is equivalent to each worker working an additional 1.19 days in every two-week paycycle. Because 89% of workers have no income outside the factory, these constitute increases in total earned income.

Heterogeneity is consistent with the hypothesized mechanism: among workers who report difficulty saving due to redistributive pressure, the Private treatment increases earnings by 15.0% (p=0.018); among those not reporting such difficulty, the estimated effect is near zero and insignificant (p=0.95). Among workers who report transfers to acquaintances (the most likely social-tax-motivated transfers), the effect is 17.5% (p=0.014). Workers without a partner — for whom intra-household redistribution is irrelevant — experience a 15.8% earnings increase (p=0.017), indicating that extra-household pressure drives the results.

Outgoing transfers do not decline. The design leaves cash-on-hand unchanged by construction, and consistent with this, there is no significant change in the likelihood or amount of transfers from treated workers to their networks. Total outgoing transfers are if anything higher among Private account workers (p=0.049), suggesting no loss in redistribution to the network.

Social Tax Rate Estimation

Combining the 11.4% treatment effect on output with a labor supply elasticity estimated from an end-of-experiment piece-rate randomization (intensive-margin elasticity of 0.17; total elasticity of approximately 1.11), the authors estimate the social tax rate for the average worker in the sample at 9–14%. For the subset who actually take up Private accounts, the implied social tax rate is 19–23%.

Scope Conditions

Results pertain to full-time female piece-rate workers in formal cashew processing plants in Côte d’Ivoire, with average tenure of 1.7 years. Because the intervention lowers the tax only on earnings above baseline (not on all earnings), the estimates do not directly capture the total distortion from eliminating all redistributive pressure. Alternative confounds — fairness/morale effects, self-control, privacy concerns, goal-setting — are each tested and ruled out as primary drivers.

In depth

Q1. What is the theoretical basis for predicting that Private accounts unambiguously increase labor supply?

The authors model redistributive pressure as a social tax rate τ₁ on gross earnings. The blocked account reduces this tax to τ₂ < τ₁ only on earnings above baseline labor supply e₁, creating a kink in the budget constraint. Starting from e₁, the worker faces only a pure substitution effect (no income effect) when τ₂ falls, because her net earnings at e₁ are unchanged. Equation (2) in the paper shows formally that the income effect term drops out, and the derivative of labor supply with respect to τ₂ is unambiguously negative (i.e., reducing τ₂ increases effort). This “clean” prediction — no income effect, no ambiguity — is the central design advantage relative to simply shielding existing earnings.

Q2. How do take-up rates differ between Private and Non-private accounts, and what do workers say explains the difference?

In Phase 2, take-up of Private accounts is 60% versus only 14% for Non-private accounts — a 77% reduction (p<0.001). Among workers who declined a Non-private account, 96% cite the anticipation of increased transfer requests from network members knowing about the account as an important factor in their decision. Only 5% cite any other reason. This pattern is strong direct evidence that the fear of redistribution — not other features of the accounts — drives take-up differences.

Q3. What are the treatment effects on earnings and attendance, and how consistent are they across phases and subsamples?

Pooled across both phases, the Private arm raises daily earnings by 175.9 FCFA (11.4%, p=0.012) and attendance by 6.2 percentage points (9.7%, p=0.023). In Phase 1 alone (Private vs. Control), earnings rise 11.3% (p=0.032). In Phase 2 alone (Private vs. Non-private), earnings rise 11.5% (p=0.043). Restricting to workers not previously treated in Phase 1, the effect is 12.8% (p=0.034); restricting further to workers new to the study in Phase 2 only, the effect is 17.3% (p=0.020). The authors cannot reject that effects across these three Phase 2 subsamples are statistically the same (p=0.427), ruling out sensitivity to the cross-randomized design.

Q4. How does treatment effect heterogeneity support the redistributive pressure mechanism?

Workers who report difficulty saving because “someone else will need it for something urgent” see earnings increase by 15.0% (p=0.018) from the Private treatment; those not reporting this difficulty see near-zero, insignificant effects (p=0.95). Workers who make transfers to acquaintances — transfers especially unlikely to reflect altruism — see earnings rise 17.5% (p=0.014). Workers with below-median baseline earnings, potentially those facing the strongest relative disincentive to work, see larger effects. Each of these heterogeneous patterns is in the direction predicted if the social tax is the operative mechanism.

Q5. Do the treatment effects reflect substitution away from outside earnings or genuine total income gains?

No. The paper finds no treatment effects on earnings outside the factory. At baseline, 89% of workers report zero outside earnings, and on average 93% of total income comes from factory wages. Consequently, the 11.4% earnings increase represents a near-one-for-one increase in total earned income.

Q6. Do Private accounts reduce transfers to the network?

No. The design ensures that cash-on-hand is unchanged by construction — workers receive the same or slightly higher take-home cash pay (the difference is positive but insignificant). Consistent with this, neither the probability of making transfers (p=0.37) nor transfers to family (p=0.35) or non-family (p=0.93) change significantly. Total outgoing transfers in the endline survey are if anything higher in the Private arm (p=0.049, though this may partly reflect redistribution of unblocked savings). The net transfer amount is positive but insignificant (p=0.32). The authors conclude the intervention did not make others in workers’ networks worse off.

Q7. How do the authors rule out morale or fairness effects as an explanation?

Treatment assignment was conducted by lottery with ID numbers drawn in front of workers, clearly dissociating it from employer favoritism. More directly, the authors test for morale effects using the 3–4 week “announcement period” between treatment disclosure and account activation. If disgruntlement among non-Private workers drove results, output should fall during this period — but estimated announcement effects are near zero (0.8% of control mean, p=0.859 in Phase 2). In contrast, effects arise immediately in the first active paycycle: earnings jump 11.4% (p=0.082) even before workers have seen any deposits occur. The fairness story also cannot explain why effects are concentrated precisely among workers who report more redistributive pressure.

Q8. How do the authors test and rule out self-control as the primary mechanism?

Self-control cannot explain why Non-private accounts — which offer the same commitment benefit — have dramatically lower take-up than Private accounts. Separately, the authors test a core prediction of time inconsistency models by surprising workers with an option to opt out of the next deposit, randomly varying whether the offer comes 4 days before payday or on payday itself. Under quasi-hyperbolic preferences, workers should be more likely to opt out on the payday itself. Counter to this prediction, 94% of workers keep their earnings in the account on payday, compared to 86% four days before — and these means are not statistically distinguishable, with the relative magnitudes actually running opposite to time inconsistency predictions.

Q9. How do the authors address the concern that Non-private accounts may raise the tax rate above the baseline, inflating treatment effect estimates?

The concern is that Non-private SMS alerts could make network members more aware of available cash than under the status quo, pushing the effective comparison above the Control level. The authors note that (a) paydays are already publicly known in this setting and workers regularly face transfer requests around them; (b) workers must physically withdraw savings from a bank after the unblock date, and can even re-block funds; and (c) the magnitude of effects when comparing Private to Control is nearly identical to the effect when comparing Private to Non-private (11.3% vs. 11.5%), suggesting the Non-private condition does not materially raise the tax above the status quo.

Q10. How do the authors rule out privacy concerns (rather than redistributive pressure) as the driver of low Non-private take-up and treatment effects?

Four arguments are provided. First, Phase 1 effects (Private vs. Control, no Non-private arm) are the same magnitude as Phase 2 effects, yet Phase 1 cannot be confounded by privacy concerns. Second, among workers who refused Non-private accounts, 96% cite transfer request anticipation; none volunteer generic privacy concerns. Third, heterogeneity effects — concentrated among high-redistributive-pressure workers — have no obvious connection to privacy preferences. Fourth, two placebo SMS exercises: 95% of Non-private workers grant permission to send generic bank promotional texts, and 88% of workers who had Phase 1 Private accounts grant permission for messages about their past (already-spent) savings — indicating no inherent aversion to having some financial information shared with networks. Since these workers forgo 11.5% of full-time earnings by refusing Non-private accounts, privacy concerns alone are implausible as a full explanation.

The authors combine the 11.4% ITT treatment effect (used as the ratio e₁/e₂) with a compensated labor supply elasticity ζ estimated from an end-of-experiment piece-rate randomization. The piece-rate experiment (varying piece rates over four values from −15% to +30% of baseline over 6 days) yields an intensive-margin elasticity of 0.17. Using the ratio of attendance to intensive-margin effects from Table 3, the implied extensive-margin elasticity is 0.94, giving ζ ≈ 1.11. With this elasticity and assuming τ₂ = 0 (most conservative), the ITT-implied social tax rate is 9%; assuming τ₂ = 5%, it is 14%. For compliers (workers who actually take up Private accounts), the estimated rate is 19–23%. If instead the lower elasticity estimate of 0.32 (comparable to Goldberg 2016) is used, the ITT tax rate would be at least 29%.

Q12. What are the broader implications discussed by the authors?

The authors propose that if redistributive pressure distorts work incentives, it may also distort other costly income-generating actions: technology adoption, human capital investment, and formal sector participation. They note that 74% of workers believe taking a formal job would increase transfer requests, even though network members could also access such jobs. A speculative but highlighted policy implication is that formal safety nets (health or unemployment insurance) could reduce social tax burdens on non-recipients by absorbing demand for redistribution, potentially generating positive productivity externalities.

Key Concepts

Social Tax: The paper’s central concept. Redistributive pressure from kin and social networks is modeled as a tax rate τ₁ on gross earnings — not altruistic transfers, but transfers made under social pressure that workers would prefer to avoid. The “tax” analogy captures that the obligation is proportional to visible income and reduces the private return to earning more. The paper explicitly does not take a stance on the underlying microfoundation (risk-sharing, cultural norms, or a mix).

Blocked Savings Account: A date-based savings account (implemented with Banque Populaire de Côte d’Ivoire) into which any earnings above a worker-chosen threshold are automatically deposited by the factory. Funds are inaccessible until the blocked period ends (3–9 months). Workers cannot withdraw during the period, making deposited earnings unavailable to fulfill transfer requests and therefore effectively reducing the social tax rate on earnings increases.

Private vs. Non-private Treatment: The paper’s key experimental contrast. A Private account’s existence is unknown to anyone in the worker’s network. A Non-private account triggers SMS messages to network members disclosing that the worker is saving and announcing when the unblock date approaches. The contrast isolates whether the shielding of income from social visibility — not the commitment device per se — drives take-up and labor supply.

Substitution Effect without Income Effect: The paper’s design deliberately places the tax reduction only on earnings above baseline, creating a kink in the budget constraint. Starting from the existing labor supply level, there is no change in net earnings at the margin — eliminating the income effect of a tax reduction — so any labor supply response is a pure compensated (substitution) effect. This makes any observed increase in labor supply an unambiguous signal that a distortionary social tax exists.

Intent to Treat (ITT) vs. Treatment on the Treated (ToT): The ITT estimate (11.4% earnings increase) reflects the effect of being offered a Private account on all offered workers, including those who did not take up. The ToT estimate — relevant for workers who actually used the accounts — implies a higher social tax rate (19–23%) because only roughly half of offered workers take up the accounts and only those workers face a materially reduced effective tax rate.

Compensated (Hicksian) Labor Supply Elasticity (ζ): The ratio used to infer the social tax rate from the observed treatment effect. The paper estimates ζ ≈ 1.11 (extensive margin ζₐ ≈ 0.94, intensive margin ζₑ ≈ 0.17) from an end-of-experiment piece-rate randomization. The social tax rate is recovered as τ₁ = 1 − (1−τ₂)(e₁/e₂)^(1/ζ) from Equation (5).

Piece Rate Setting: Workers earn a linear piece rate for every kilogram of cashews peeled, with no fixed pay component. This setting ensures that every unit of additional effort by a worker translates directly into higher earnings, and that any observed earnings changes cleanly reflect labor supply responses rather than hour or schedule effects.

H0 | Macro Paper Warehouse

A Welfare Analysis of Policies Impacting Climate Change

Changing Opportunity: Sociological Mechanisms Underlying Growing Class Gaps

Firm Accommodation After Workplace Disability: Labor Market Impacts and Implications for Subsidy Design

Layer 1 — Overview

In depth

Q1. What is the Employer at Injury Program (EAIP), and how does it differ from standard workers’ compensation?

Q2. How is firm-level “exposure” constructed, and what is the rationale for using it as an instrument?

Q3. What are the first-stage and reduced-form results from the DID specification?

Q4. What do the IV estimates imply about the causal effect of accommodation on labor market outcomes?

Q5. What does the MTE framework reveal about the distribution of accommodation effects and selection?

Q6. What evidence supports characterizing firm accommodation as general rather than firm-specific human capital investment?

Q7. What are the two sources of market inefficiency in accommodation identified in the model?

Q8. How is heterogeneity incorporated in the structural estimation, and what do the estimated parameters show?

Q9. What do the counterfactual simulations show about the welfare effects of varying the subsidy rate?

Q10. What distributional implications do wage subsidies have across worker and firm types?

Q11. How do the experience-rating channel and the worker-turnover channel interact in comparative statics?

Key Concepts

Selection in Surveys: Using Randomized Incentives to Detect and Account for Nonresponse Bias

The Social Tax: Redistributive Pressure and Labor Supply

Layer 1 — Overview

In depth

Q1. What is the theoretical basis for predicting that Private accounts unambiguously increase labor supply?

Q2. How do take-up rates differ between Private and Non-private accounts, and what do workers say explains the difference?

Q3. What are the treatment effects on earnings and attendance, and how consistent are they across phases and subsamples?

Q4. How does treatment effect heterogeneity support the redistributive pressure mechanism?

Q5. Do the treatment effects reflect substitution away from outside earnings or genuine total income gains?

Q6. Do Private accounts reduce transfers to the network?

Q7. How do the authors rule out morale or fairness effects as an explanation?

Q8. How do the authors test and rule out self-control as the primary mechanism?

Q9. How do the authors address the concern that Non-private accounts may raise the tax rate above the baseline, inflating treatment effect estimates?

Q10. How do the authors rule out privacy concerns (rather than redistributive pressure) as the driver of low Non-private take-up and treatment effects?

Q11. How is the social tax rate estimated and what does the range look like?

Q12. What are the broader implications discussed by the authors?

Key Concepts