J01 | Macro Paper Warehouse

The Effects of Mandatory Profit-Sharing on Workers and Firms

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

This paper studies the causal effects of mandatory profit-sharing on workers and firms using a quasi-experimental design arising from a 1990 French reform that lowered the eligibility threshold for mandatory profit-sharing from 100 to 50 employees. The institutional setting is the French RSP (Réserve Spéciale de Participation), a profit-sharing scheme in place since 1967 that requires firms above the threshold to distribute a fraction of their excess profits — defined as net income above 5% of book equity — to employees according to a formula scaled by the firm’s labor share. For the median firm, this amounts to roughly 10.5% of pre-tax income transferred to workers.

The authors employ two primary empirical strategies. First, a bunching analysis exploits the pre-reform distribution of firm employment around the 100-employee threshold as a revealed-preference test of whether firms perceive profit-sharing as a net cost. Second, a difference-in-differences design compares treated firms (55–85 employees in 1989–1990, who become newly subject to the regulation after 1991) against two control groups: small firms (35–45 employees, likely never subject) and large firms (120–300 employees, already subject). Data come from the universe of French corporate tax files (FICAS) and a linked employer-employee panel (DADS) covering approximately 4% of private-sector workers, spanning 1985–1997.

The bunching analysis documents a 22.3% excess density in the 95–99 employee bin before the reform, which disappears after 1991. Three tests — comparing wage bills per employee across the threshold, cross-checking with DADS employment records, and examining profitability patterns — collectively support the conclusion that bunching reflects genuine employment reductions rather than under-reporting. The implied employment loss is approximately 1.67% of total employment among affected firms.

The difference-in-differences results yield the following firm-level findings: (a) the total compensation share (wages plus profit-sharing divided by value added) rises by 1.8 percentage points for firms with positive excess profits; (b) 77% of this increase comes at the expense of firm owners — the profit share falls by 1.37 percentage points; (c) the remainder is borne by the government through a reduction in the corporate income tax share; (d) the wage share (base wages only) is unaffected, indicating that owners do not reduce wages to offset the cost of profit-sharing; (e) investment and total factor productivity show no statistically significant change — effects on productivity are bounded below ±1% for several TFP measures; and (f) the capital-labor ratio shows a small, mostly insignificant negative effect, consistent with a model-implied increase in the cost of capital of only 0.43 percentage points.

Worker-level analysis using the linked employer-employee data confirms that average total compensation rises by approximately 3.5% for workers in treated firms, with no decline in base wages. Critically, this average conceals distributional heterogeneity across the skill spectrum. For low- and medium-skill workers (blue-collar workers, clerks, supervisors, skilled technicians), total compensation rises while base wages are unchanged — consistent with wage rigidity binding for these groups. For high-skill workers (managers, engineers, executives), base wages fall by enough to leave total compensation unchanged, consistent with more flexible wages at the upper end of the skill distribution. This pattern implies that mandatory profit-sharing is a progressive policy within firms, redistributing excess profits predominantly to lower-skill workers.

The paper concludes that France’s mandatory profit-sharing scheme, as implemented, functions as a non-distortive redistributive tool: it transfers excess profits from shareholders to lower-skill workers without generating measurable productivity losses or large investment distortions. The fiscal cost is non-trivial: each dollar transferred to workers costs approximately 20 cents in foregone corporate income tax. The scheme also has an inherent inequality in its redistribution since it exclusively benefits workers in profitable firms, and firms’ excess profits are highly persistent.

Q: What is the French RSP and how does the formula work? A: The RSP (Réserve Spéciale de Participation) is a mandatory profit-sharing fund established by executive order in 1967. The formula is RSP = 0.5 × (wage bill / value added) × max(net income − 5% × book equity, 0). The 5% deduction represents lawmakers’ view of fair compensation to shareholders; any excess is split between shareholders and workers, with the split scaled by the firm’s labor share. For the median firm in the sample — ROE of 12%, labor share of 0.52, corporate tax rate of 37% — the formula yields roughly 9.5% of pre-tax income, and in post-1991 data the realized average is 10.5% of pre-tax income for firms with positive excess profits.

Q: Why can’t a standard regression discontinuity be used at the 100-employee threshold? A: Because firms strategically control their position relative to the threshold — the bunching analysis itself demonstrates this. When firms sort non-randomly around the cutoff, the local randomization assumption underlying RD is violated. The authors instead use a difference-in-differences design exploiting the time variation introduced by the 1990 reform.

Q: How large is the pre-reform bunching and what does it imply? A: The distribution of employment shows 22.3% excess density in the 95–99 employee bin relative to the post-reform counterfactual distribution. Interpreting this as real employment reduction (supported by three empirical tests), the implied employment loss is approximately 1.67% of total employment among firms in the 85–120 employee range. Dynamic bunching analysis shows this is persistent rather than temporary — the 100-employee threshold significantly constrained three-year employment growth for firms in the 85–99 range in the pre-reform period.

Q: How do the authors establish that bunching is real rather than under-reporting of employment? A: Three tests are conducted. First, wage bills per employee show no discontinuity around the 100-employee threshold in either period, ruling out systematic under-reporting of headcount while truthfully reporting wages. Second, employment from DADS payroll records — harder to manipulate — shows only a statistically insignificant gap of roughly 0.5 employees relative to tax-file employment just below the threshold, far too small to shift firms across the 100-employee bin. Third, profitability and value added per employee are significantly higher just below the threshold, consistent with more profitable firms having stronger incentives to bunch through genuine employment reductions.

Q: What is the main identification strategy for the firm-level analysis? A: A difference-in-differences design where treated firms have 55–85 employees in both 1989 and 1990 (newly subject to the mandate after 1991), compared to small control firms with 35–45 employees (likely never subject) and large control firms with 120–300 employees (likely always subject). Specifications include firm fixed effects and county-by-year and industry-by-year fixed effects. Parallel pre-trends are confirmed graphically and in event-study regressions. The design is intent-to-treat: by 1997, 26.7% of treated firms had shrunk below 50 employees and did not actually pay profit-sharing. LATE estimates are obtained via 2SLS.

Q: What are the main firm-level findings on compensation and profit shares? A: For treated firms with positive excess profits, the total compensation share rises by 1.8 percentage points. The wage share (base wages only, excluding profit-sharing) is precisely estimated at zero — owners do not reduce wages. The profit share falls by 1.37 percentage points, accounting for 77% of the increase in total compensation. The remaining approximately 23% is borne by the tax authority through a reduction in the corporate income tax share, since profit-sharing reduces the corporate income tax base. These findings are robust to balanced vs. unbalanced samples and to alternative control group definitions.

Q: Does mandatory profit-sharing raise or lower firm productivity? A: Across five different TFP estimators (Olley-Pakes, Olley-Pakes with Ackerberg-Caves-Frazer correction, Wooldridge, Levinsohn-Petrin, and Ackerberg-Caves-Frazer), the effect of mandatory profit-sharing on productivity is a precisely estimated zero. For several measures, effects larger than ±1% in magnitude can be rejected. Softer measures of effort — sick leave rates and the probability of working extra hours — also show no significant change. This null finding contrasts with the literature on voluntary profit-sharing adoption, which typically finds 3–5% productivity gains, likely reflecting selection bias in that literature.

Q: Does mandatory profit-sharing distort investment? A: The effect on investment is small and mostly statistically insignificant. The theoretical model shows why: the profit-sharing formula is based on excess profits (net income minus 5% of book equity), not total profits. When the firm’s actual cost of equity approximately equals the regulatory 5% benchmark, the distortion to the cost of capital is zero. The calibrated distortion to the user cost of capital is only 0.43 percentage points — approximately 1.9% of the standard user cost — implying an investment ratio reduction of about 0.84 percentage points using estimated elasticities from Chodorow-Reich et al. (2024). Empirically, capital-labor ratios show a small, largely insignificant negative effect.

Q: How does profit-sharing incidence differ across the skill distribution? A: The worker-level DADS analysis reveals that the average 3.5% increase in total compensation masks sharp heterogeneity. For low- and medium-skill workers (blue-collar workers, clerks, supervisors, skilled technicians), total compensation rises while base wages are unchanged. For high-skill workers (managers, engineers, executives), base wages decline sufficiently to leave their total compensation unchanged. The authors interpret this pattern as consistent with wage rigidity being more binding for lower-skill workers — due to the federal minimum wage and collective agreements — than for managers whose pay is more flexibly set.

Q: Why does profit-sharing not affect base wages for low-skill workers? A: Two candidate explanations are considered. The risk channel — that profit-sharing is risky and thus less valuable to risk-averse workers, who demand wage compensation — is rejected empirically because profit-sharing only marginally increases the variability of workers’ total earnings. The wage rigidity channel is supported: France’s binding federal minimum wage and widespread collective agreements constrain downward adjustment in base wages for lower-skill workers, so firms cannot pass through profit-sharing costs as lower wages for this group.

Q: What is the fiscal cost of the profit-sharing scheme? A: Each dollar transferred to workers through mandatory profit-sharing costs approximately 20 cents in reduced corporate income tax receipts, since profit-sharing payments are deductible from taxable income. The paper notes this is a partial fiscal evaluation; a full assessment would also require analyzing personal income tax implications, which are left for future work.

Q: How does this scheme compare to a corporate income tax as a redistributive tool? A: Both instruments reduce firm profits and can benefit workers, but differ in three key respects. First, the tax base differs: profit-sharing targets excess profits above 5% of book equity whereas the corporate income tax applies to all corporate earnings, generating different distortions to investment. Second, profit-sharing goes directly to workers in the same firm, whereas corporate tax revenues are redistributed through general government spending — making the incidence more direct and more closely monitored by workers. Third, workers have stronger incentives to monitor firm compliance with profit-sharing (each euro of diverted excess profit reduces workers’ collective income by roughly 10–15 cents) than with corporate taxes.

Q: How does this paper compare to findings on mandatory profit-sharing in Peru? A: Tolentino (2022) studies a mandatory profit-sharing scheme in Peru exploiting a 20-employee eligibility threshold and finds larger distortions — reductions in both investment and productivity. The authors attribute this difference to two features: the Peruvian scheme applies to the entirety of post-tax profits rather than excess profits above an equity deduction, creating a broader and more distortionary base; and there is pre-existing bunching at the Peruvian threshold even before the scheme was introduced, suggesting confounding pre-existing regulations.

Q: What are the scope conditions on the external validity of the findings? A: The findings apply specifically to mandatory profit-sharing under the French RSP formula — which exempts a 5% equity return from the profit-sharing base, limiting distortions — during 1985–1997, for firms in the 55–300 employee range. The null productivity effect may not generalize to voluntary schemes, where selection on anticipated gains likely produces positive correlations. The redistributive finding (benefiting lower-skill workers) is specific to a context with binding minimum wages and collective agreements that constrain wage adjustment for that group. The fiscal cost calculation also excludes personal income tax effects.

Excess profits: Defined in the paper as net income minus 5% of book equity — the amount above what lawmakers considered fair compensation to shareholders. Only excess profits (not total profits) are subject to the mandatory profit-sharing formula.

RSP formula (Réserve Spéciale de Participation): The statutory formula RSP = 0.5 × (wage bill / value added) × max(net income − 5% × book equity, 0), scaled by the firm’s labor share to reflect labor’s contribution to production. Unchanged since 1967.

Total compensation share: The ratio of (wage bill plus profit-sharing) to value added — the paper’s primary measure of workers’ overall claim on firm output, as distinct from the wage share (wage bill alone divided by value added).

Wage incidence parameter (λ): The fraction of profit-sharing that firms pass through to workers as lower base wages. λ = 1 means full incidence (workers’ total compensation unchanged); λ = 0 means no incidence (workers fully benefit). The paper’s empirical findings are consistent with λ ≈ 0 for low-skill workers and λ ≈ 1 for high-skill workers.

Bunching: The empirical phenomenon whereby firms cluster employment just below the 100-employee regulatory threshold to avoid mandatory profit-sharing. The paper uses the pre- vs. post-reform shift in the employment distribution as a revealed-preference test of whether firms perceive the scheme as a net cost.

Intent-to-treat (ITT) design: The empirical design comparing firms that were in the newly eligible size range (55–85 employees) just before the 1990 reform against firms that were either always or never eligible, regardless of whether treated firms actually ended up paying profit-sharing post-reform. LATE estimates are obtained via 2SLS to recover effects on actual compliers.

Distortion to user cost of capital: The additional cost of capital induced by profit-sharing, equal to ϕ × γ(1−λ) / [1 − γ(1−τ)] × (re − ρ), where ρ = 5% is the regulatory equity benchmark. When the firm’s actual cost of equity equals the 5% benchmark, this distortion is zero — a feature that distinguishes the French scheme from a standard corporate income tax.

The Impact of Incarceration on Employment, Earnings, and Tax Filing

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

Overview

This paper estimates the causal effect of incarceration on employment, wage earnings, self-employment, and tax filing behavior using administrative criminal justice data linked to Internal Revenue Service (IRS) records for approximately half a million felony defendants in two U.S. states: North Carolina and Ohio. The study period covers cases filed from the early 2000s through 2014, with outcomes tracked through 2020 using IRS W-2 and 1040 records.

Research Question

The central question is whether incarceration itself — as distinct from arrest, conviction, and other criminal justice interactions that precede or accompany it — causes lasting reductions in defendants’ labor market outcomes. The paper explicitly holds fixed upstream interactions (conviction, arrest) to isolate the effect of the incarceration sentence.

Data and Sample

Criminal justice records from Ohio (Common Pleas courts in Franklin, Cuyahoga, and Hamilton counties, covering Columbus, Cleveland, and Cincinnati) and North Carolina (Administrative Office of the Courts and Department of Public Safety) are linked to de-identified IRS records via name, date of birth, sex, address, and partial Social Security Numbers. Match rates are 92% in Ohio and 95% in North Carolina. The sample is restricted to defendants aged 18–50 at time of offense with cases filed 2002–2014. IRS records include employer-reported W-2 wages (regardless of individual tax filing), self-employment income from Schedule C/SE, non-employee compensation (1099-MISC), and gig-economy earnings from 1099 returns. All dollar figures are adjusted to 2016 dollars using the PCE deflator.

Empirical Strategy

Two independent quasi-experimental research designs are used:

North Carolina — Sentencing guideline discontinuities: North Carolina’s structured sentencing guidelines map offense class (E through I, the five least severe felony classes) and prior record points (a numerical criminal history score) into permissible punishment types (incarceration vs. probation) and sentence lengths. Allowable punishment types change discretely at five cell boundaries, generating discontinuities in incarceration sentences for otherwise similar defendants. The paper uses these five boundary discontinuities as excluded instruments in a parameterized regression discontinuity design stacked across offense classes. First-stage F-statistic = 115.
Ohio — Random assignment to judges: Cases are randomly assigned by computer to judges at arraignment in the three counties studied. Judge leave-out mean sentence length is used as an instrument for individual sentence length. The design follows Norris et al. (2021) and yields F-statistic = 321. The instrument shifts sentences along both the extensive margin (any vs. no incarceration) and intensive margin (longer vs. shorter sentences).

Both designs produce complier populations for whom at least 37–45% are shifted on the extensive margin (from no incarceration to some incarceration), based on partial identification bounds using linear programming.

Main Findings

The paper’s central finding is that incarceration generates large short-run reductions in labor market activity during the incapacitation period, but no detectable long-run reductions in annual employment or earnings once defendants have been released and the incapacitation effects have dissipated.

In the first year after case filing, when incarceration rates peak (roughly 75–100 additional days incarcerated for a 12-month sentence), employment falls by approximately 10 percentage points and total W-2 earnings contract commensurately.
Within 3–4 years of filing, employment effects return to near zero and are statistically insignificant in both states.
Five to nine years after filing, when effects on contemporaneous incarceration have dissipated, the estimated effect of a 12-month sentence on annual earnings is positive or near zero in both states. The combined 95% confidence interval rules out reductions in annual wages greater than $231 (approximately 5% of the untreated complier mean) and rules out any adverse employment effects.
Despite no long-run level effects, losses during incapacitation are never recouped. A one-year sentence reduces cumulative earnings over five years by approximately $2,914 — a 13% reduction relative to the complier mean.
Effects on self-employment, independent contracting, 1040 filing, adjusted gross income, EITC take-up, and interstate migration are similarly null in the long run.

Incapacitation vs. Post-Release Scarring

The paper provides two tests for whether short-run earnings losses reflect incapacitation alone or also post-release scarring (e.g., human capital depreciation, employer discrimination, or discouragement effects):

A “visual IV” regression of year-t earnings effects on year-t days-incarcerated effects yields an R² of 0.83–0.85 across states, with the intercept near zero (positive and small), indicating that virtually all dynamic earnings impacts flow through contemporaneous incapacitation and not through a post-release channel.
Constructed outcomes that impose the null of pure incapacitation (scaling pre-case average earnings or covariate-predicted earnings by the share of the year free from prison) closely track actual earnings effects in both states, further confirming that incapacitation is the dominant mechanism.

Pre-existing Labor Market Detachment

A key scope condition is defendants’ severe labor market disadvantage prior to their case. Fewer than 50–60% of defendants are employed in the year before filing; average pre-case W-2 earnings (including zeros) are below $6,000. Among employed defendants, only 10% earn more than $22,000 per year. Untreated complier means for earnings in the year after case filing are below $4,000, with virtually no earnings or employment growth over the following nine years. The paper concludes that returning to pre-filing earnings levels is sufficient for incarcerated defendants to match their non-incarcerated peers — a low bar that is readily met.

Policy Implications

Back-of-envelope aggregation implies incapacitation losses of approximately $6.16 billion per year in foregone earnings for the U.S. prison population, concentrated in communities heavily affected by incarceration. However, a marginal reduction in incarceration rates would increase average earnings by only $51 for white men and $213 for black men, suggesting incarceration’s direct contribution to labor market inequality is modest relative to the $21,100 black-white earnings gap estimated by Bayer and Charles (2018). The paper concludes that upstream factors — other criminal justice interactions, human capital deficits, and broader socioeconomic disadvantage — are more plausibly responsible for low earnings among the formerly incarcerated.

In depth

Q1. What is the exact treatment variable, and what is the counterfactual?

The treatment variable is months of incarceration sentenced in the focal case (a continuous, weakly positive ordered treatment). The counterfactual for non-incarcerated defendants in North Carolina is probation (all defendants are convicted by construction under structured sentencing guidelines). In Ohio, the authors cannot reject that all compliers who do not receive a prison sentence are still convicted, implying the counterfactual is also conviction and probation. All compliers therefore acquire a criminal record regardless of sentence. The treatment effect is thus the effect of incarceration conditional on conviction, holding fixed the criminal record.

Q2. How are effects interpreted given multiple instruments and continuous treatment?

Under a “weakly positive ordered treatment” assumption and standard LATE conditions, the 2SLS estimates can be interpreted as Average Causal Responses (ACRs) — weighted averages of the marginal dose effects (12 vs. 11 months, 6 vs. 5 months, 1 vs. 0 months, etc.) for complier subgroups shifted by each instrument. In North Carolina with five parameterized RD instruments, the estimate averages ACRs weighted by first-stage strength. In Ohio with a leave-out mean instrument, the estimate is a convex average of ACRs under the assumption that the linear first-stage model is a good approximation. Dosage weights for both states put mass on a wide range of sentence lengths including both extensive and intensive margins, though Ohio’s weights are more skewed toward shorter sentences.

Q3. How large are the first-stage effects, and how strong is the instrument?

In North Carolina, sentences jump by 50% or more at sentencing guideline cell boundaries where allowable punishment types change to include incarceration. The first-stage F-statistic is 115. In Ohio, defendants assigned to the most severe judge receive incarceration sentences approximately six months longer than those assigned to the least severe judge (roughly 30% of the average non-zero sentence), with a slope of approximately 0.8 in the first-stage regression; F-statistic = 321. At least 37% of compliers in North Carolina and 45% in Ohio are shifted on the extensive margin (from no incarceration to some positive incarceration), with upper bounds as high as 95%.

Q4. What evidence supports instrument validity (exclusion restriction and independence)?

Instrument validity is tested by estimating 2SLS “effects” on pre-case outcomes measured 2–4 years before the focal case. In both states, the instruments show no relationship with pre-case employment, W-2 wages, total days previously incarcerated, or binary severe prior incarceration. The probability of being matched to IRS records and the quality of the match are also uncorrelated with the instruments. In Ohio, potential exclusion restriction violations from judges affecting conviction (not just sentence) are addressed empirically: nearly 90% of defendants are convicted, the most severe judge is only 0.7 p.p. more likely to convict than the least severe judge (t-stat = 1.53), and the estimated conviction rate among untreated compliers is 0.972 (s.e. 0.018), so one cannot reject that all non-incarcerated compliers are convicted.

Q5. How does the paper test for the incapacitation mechanism against post-release scarring?

Two complementary exercises are conducted. First, a “visual IV” plot regresses year-t earnings effects on year-t days-incarcerated effects across all post-filing years. If incapacitation is the sole channel, all points should lie on a line through the origin. The R² is 0.83 in North Carolina and 0.85 in Ohio, the estimated intercept is near zero (positive and small) in both states, and the slope (earnings lost per day incarcerated) is approximately $12. This implies cumulative earnings losses of $12 × 268 days = $3,216, very close to the directly estimated $2,914. Second, constructed outcomes that scale pre-case earnings or covariate-predicted earnings by the share of the year not incarcerated closely track actual earnings effects throughout the post-filing period, and both converge to zero as incapacitation effects fade — consistent with pure incapacitation and no net scarring.

Q6. What are the long-run (5–9 years) earnings and employment estimates, and how precisely are null effects ruled out?

Averaged across both states using inverse-variance weights, the estimated effect of a 12-month sentence on annual W-2 earnings five to nine years after filing is positive but statistically indistinguishable from zero. The 95% confidence interval rules out reductions in annual wages greater than $231 (approximately 5% of the untreated complier mean of roughly $4,500–$5,000). The 95% CI also rules out any adverse employment effects. The untreated complier mean for employment 5–9 years post-filing is approximately 40% in North Carolina and slightly above 40% in Ohio.

Q7. What happens to cumulative earnings over five years despite null long-run level effects?

Even though long-run annual earnings are unaffected, earnings losses during incapacitation are never made up. A one-year sentence reduces cumulative employment (measured as years with any W-2) and cumulative earnings over five years by approximately $2,914 — a 13% reduction relative to the complier mean. This reflects the mechanical loss of earnings during the period of physical incapacitation, without a subsequent compensating period of higher earnings after release.

Q8. Do defendants with stronger pre-case labor market attachment show different long-run patterns?

The sample is split between defendants employed in at least 2 of the 4 years prior to the case (53–57% of the sample across states) and those less attached. Both groups show zero long-run earnings and employment effects. Previously employed defendants experience much larger short-run earnings drops — more than three times larger in the first year post-filing — and their earnings recover more slowly, reaching zero effect approximately six years after filing (vs. three years for the previously unemployed). For a stricter cut (pre-case average earnings above $15,000, representing only 12–15% of the sample), the long-run earnings effect is −$1,426 (8% of the untreated complier mean), significant only at the 10% level, and partly attributable to residual incapacitation (19.6 additional days incarcerated 5–9 years post-filing). For defendants with pre-case earnings below $15,000, incarceration slightly increases long-run employment (2.4 pp, p = 0.01) and earnings ($400, p = 0.03), possibly reflecting rehabilitative benefits (GED or educational programs) for labor-market-detached individuals.

Q9. Does first-time incarceration (extensive-margin exposure) have larger long-run effects than repeat exposure?

The paper tests this by splitting the sample into defendants with and without prior incarceration history. Among defendants with no prior incarceration, the instruments generate large differences in lifetime exposure: a 12-month sentence increases the probability of ever being incarcerated over the next 5–9 years by 26 p.p. (North Carolina) and 41 p.p. (Ohio). Among those not receiving a sentence, 48% (North Carolina) and 19% (Ohio) are eventually incarcerated anyway, implying treatment causes a 52 and 81 p.p. increase in lifetime incarceration probability for extensive-margin compliers. Despite these large differences in lifetime exposure, long-run earnings and employment effects remain small and statistically insignificant in both subsamples. The difference in long-run effects between previously and never incarcerated defendants is not statistically significant (p = 0.29 for employment, p = 0.82 for earnings).

Q10. Are there heterogeneous effects by race, sex, or criminal history?

There is no evidence of long-run scarring for any demographic or criminal history subgroup. Effects for black and non-black defendants are both positive for long-run earnings and employment. Non-black defendants show somewhat larger cumulative losses (consistent with marginally higher counterfactual earnings), but differences are not statistically significant. Estimates for women are imprecise due to small sample size. Among defendants with and without prior felony charges in the four years preceding the case, there are neither economically nor statistically significant long-run earnings or employment effects. Cumulative losses are somewhat larger for defendants without prior felony charges (p = 0.07), reflecting their higher pre-case earnings.

Q11. How does the paper handle potential migration bias in outcomes?

Tax filing and W-2 receipt in the state of sentencing are used to proxy for whether defendants remain in the same state. Among untreated compliers, 88% of those with a tax footprint maintain it in the state of sentencing. No statistically significant effects of incarceration on migration (measured as filing or receiving a W-2 in North Carolina or Ohio) are detected, suggesting prior studies of recidivism measured within-state are unlikely to be severely biased by migration responses.

Q12. What effect does incarceration have on mortality?

Incarceration reduces five-year mortality by approximately 0.8 percentage points (about 20% of the untreated mean). The authors note this is too small to explain the null long-run labor market effects: even if all defendants whose death was averted were employed, removing them from the employment count would reduce the employment effect of a 12-month sentence only to approximately zero.

Q13. How do the paper’s findings compare to prior studies, particularly Mueller-Smith (2015)?

Mueller-Smith (2015) finds large and persistent negative incarceration effects on labor market outcomes in Texas using a structural decomposition and Lasso-based judge-covariate interactions as instruments. The paper argues methodological differences are the likely explanation: the Lasso-selected interacted instruments can be susceptible to many-weak instruments bias toward OLS. It notes that Mueller-Smith’s simpler 2SLS specifications (analogous to those used here) show no statistically significant earnings effects. North Carolina and Ohio are documented to be broadly similar to Texas (and the U.S. average) in rehabilitation program participation, recidivism rates, and incarceration rates, reducing the likelihood that genuine geographic heterogeneity explains the divergence.

Q14. What is the paper’s aggregate extrapolation of incapacitation earnings losses?

Scaling the estimated $2,914 cumulative loss per 12-month sentence by the ratio of days exposed to total days in a year gives a per-day loss of approximately $12. Applied to the 1,435,500 people incarcerated in U.S. prisons on any given day in 2019 (excluding the more than 700,000 in jail), the implied aggregate yearly earnings loss from incapacitation is approximately $6.16 billion.

Key Concepts

Incapacitation effect: The mechanical reduction in earnings and employment that occurs while a defendant is physically confined in prison and unable to work, as distinct from any post-release scarring effect. The paper shows this is the dominant — and essentially sole — causal channel through which incarceration affects labor market outcomes in their sample.

Post-release scarring: Persistent reductions in earnings or employment that persist after a defendant is released from prison, caused by mechanisms such as employer discrimination based on incarceration history, human capital depreciation, loss of job contacts, or psychological discouragement effects. The paper finds no evidence of scarring in either state.

Average Causal Response (ACR): The weighted average of the marginal dose effects of incarceration (e.g., effect of 12 vs. 11 months, 1 vs. 0 months) for groups of defendants whose sentence lengths are shifted by a given instrument. Contrasted with a binary LATE, the ACR averages across the full dosage distribution for compliers.

Complier: An individual whose incarceration sentence is shifted by the instrument — either from zero to some positive sentence (extensive margin) or from a shorter to a longer sentence (intensive margin). Counterfactual outcome means for compliers sentenced to zero months provide the baseline for evaluating effect magnitudes.

Sentencing guideline discontinuity: The discrete jump in permissible punishment types and minimum sentence lengths at specific criminal history score thresholds within North Carolina’s structured sentencing grid. Defendants just above a threshold are more likely to be incarcerated than otherwise similar defendants just below, generating quasi-experimental variation exploited as an instrument.

Leave-out mean judge instrument: In Ohio, each defendant’s assigned judge’s average incarceration sentence length computed over all other cases that judge handles (excluding the defendant’s own case), residualized on court-by-month fixed effects. Because judges are randomly assigned to cases, this measure is conditionally independent of defendant potential outcomes and serves as an instrument for sentence length.

Control complier mean: The estimated mean potential outcome for compliers under the counterfactual of receiving zero months of incarceration. Used as a benchmark to evaluate the magnitude of treatment effects and to characterize how low the earnings baseline is for the population driving the causal estimates.

Extensive vs. intensive margin of incarceration: The extensive margin refers to the binary shift from receiving no prison sentence to receiving any prison sentence; the intensive margin refers to increasing sentence length conditional on some incarceration. The paper argues that neither margin appears to produce long-run labor market scarring, and uses linear programming bounds to estimate that at least 37–45% of compliers in each state are shifted on the extensive margin.