G3 | Macro Paper Warehouse

Politics at Work

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

Layer 1 — Overview

Research Question

Do individual political views shape firm behavior and labor market outcomes in the private sector? Specifically, do business owners sort copartisan workers into their firms, and does employers’ political discrimination drive this sorting?

Data and Setting

The paper studies the complete Brazilian formal labor market over 2002–2019, assembling a novel longitudinal worker-firm-owner-party matched dataset from three administrative sources: (1) RAIS (Relação Anual de Informações Sociais), the universe of formal-sector workers (87 million unique workers, 7.6 million unique firms); (2) the Receita Federal do Brazil (RFB) and Cadastro Nacional de Empresas (CNE), containing business ownership structures for all registered firms; and (3) the Tribunal Superior Eleitoral (TSE) registry of all party members (19.3 million individuals) over 2002–2019. Matching these sources yields political affiliation for 11.4% of all private-sector owners and 7.8% of all private-sector workers in the sample. Party affiliation in Brazil requires an active registration step and is interpreted as a signal of strong and visible political views, distinguishing affiliated from unaffiliated individuals who likely hold milder views. The 35 parties in the sample are highly fragmented; the top 7 account for nearly 70% of all party members.

Main Findings

Political assortative matching. Using a likelihood ratio index (Eika et al., 2019; Chiappori et al., 2020), the paper finds that workers and owners belonging to the same party are on average about twice as likely to match in the labor market relative to random matching. Once within-municipality geographical sorting is accounted for, this figure falls to approximately 55% excess probability of copartisan matching, and increases over time: from 1.41 in 2002–2006 to 1.67 in 2016–2019. A dyadic regression approach — constructing all worker-firm dyads within industry-municipality labor markets and controlling for shared gender, race, age, and education — confirms the result: across all years, a politically affiliated worker is between 41% and 75% more likely to be employed by a copartisan owner than by an owner affiliated with a different party. Political assortative matching is driven both by higher hiring probabilities (range: 32%–59% more likely for copartisans, hiring margin only) and by longer tenure: copartisan workers stay in the firm roughly 5.5% longer than otherwise comparable workers of a different party, even within the same firm and hire-year (column 3 of Table 2). In every year and by every method, the degree of political assortative matching exceeds that of gender (15%–31% excess probability under dyadic approach) and race (approximately 3.4%), which are themselves both positive and significant.

Mechanisms: political discrimination. Three sets of evidence point to employer political discrimination as a relevant driver. First, in the administrative micro-data: assortative matching decreases strongly with firm size — it is more than twice as large in firms with up to 10 employees than in medium firms and more than six times as large as in firms with more than 50 employees — and is stronger for higher occupational layers and for jobs requiring above-median social skills or interpersonal relationships. Political assortative matching is, if anything, larger for parties not in power locally, inconsistent with a patronage mechanism. An event study of 5,262 owners who switched party finds a sharp increase of about 0.2 standard deviations in hires from the new party and a corresponding drop in hires from the old party at the time of the switch, with the share of workers from the new party rising by roughly 5 percentage points persistently. Second, an incentivized resume rating (IRR) field experiment (150 business owners; nondeceptive design) shows that owners rate copartisan resumes 0.213 points higher on a 1–7 Likert scale (a 7.4% increase relative to the mean rating for different-party resumes, statistically significant at p < 0.05), with no significant effect on perceived candidate acceptance probability. Third, a representative survey of 891 owners and 1,003 workers finds that belief-based and taste-based discrimination are ranked as the leading explanations by both groups; 47% of owners and 58% of workers agree with the belief-based discrimination statement. Additionally, 29% of surveyed owners (22% say “Yes” and 7% “In some cases”) explicitly reveal that political views affect their hiring decisions.

Real consequences. Conditional on employment, copartisan workers are promoted faster: they are 0.448 percentage points more likely to be promoted from white-collar to managerial positions (against a base rate of 2.58%) and 0.44 percentage points more likely to be promoted from blue-collar to white-collar positions (base rate 2.98%). Workers from a different party than the owner face a promotion penalty of 0.104–0.180 percentage points for white-collar-to-manager promotions. On wages, copartisan workers earn 3.9% more than unaffiliated coworkers within the same firm and year (firm-year FE specification); the effect is 2.8% when restricting to the same occupation within the firm. Workers from a different party earn 1.6% less. Decomposing by tier: managers (copartisan premium 1.6%), white-collar workers (3.4%), blue-collar workers (1.5%). Despite better outcomes, copartisan workers are 2.1 percentage points (2.3% relative to the mean) less likely to be educationally qualified for their occupation, conditional on firm-year and controlling for a full set of demographics. Finally, a higher share of copartisan workers in the prior year is associated with lower firm employment growth (estimated β = −0.071), corresponding to approximately a 1 percentage point gap in annual growth rate for a one-standard-deviation difference in copartisan share — substantial relative to an average annual growth rate of 10%.

Scope Conditions

All findings pertain to the formal private sector in Brazil over 2002–2019. Political affiliation in the Brazilian system requires an active step and signals strong views; results apply to the approximately 7.8%–11.4% of workers and owners who are party-registered. The field experiment sample is limited to 150 business owners affiliated with major Brazilian parties who were actively seeking to hire. The firm growth result is explicitly characterized as suggestive, without a source of exogenous variation.

In depth

Q1. What is the likelihood ratio index and what does it show for political matching in Brazil?

The likelihood ratio index measures how many times more likely a match between a worker and owner of the same party is, relative to the expected frequency under random matching (conditional on the population shares of each party). Across 2002–2019, the unconditional index ranges from 1.56 to 1.85, implying workers and employers of the same party are on average about twice as likely to match as under random matching. After accounting for geographic sorting within municipalities, the index ranges from approximately 1.41 (2002–2006 average) to 1.67 (2016–2019 average), showing a clear increasing trend. The corresponding gender and race indexes average about 1.2 and 1.35, respectively, in the basic specification, both significantly lower than the party index in every year of the sample.

Q2. How do the dyadic regression estimates control for omitted characteristics, and what do they find?

The dyadic regression constructs all possible worker-firm pairs within each municipality-industry labor market in a given year. The dependent variable is an indicator for whether worker i is employed by firm f. The key coefficient of interest is the differential probability of employment for a copartisan pair relative to a different-party pair, controlling for indicators for shared gender, race, age bracket, and education level, as well as worker occupation fixed effects and experience. This controls for the concern that politically affiliated individuals share non-political traits that correlate with employment choices. After these controls, a politically affiliated worker is 41%–75% more likely (depending on year) to be employed by a copartisan owner than by a different-party owner. The effect stems primarily from copartisan workers being preferentially hired (not just from unaffiliated owners preferring any affiliated worker indiscriminately). The analogous dyadic estimate for shared gender is 15%–31% and for shared race is approximately 3.4%, both lower than the party estimate in all years.

Q3. How is political assortative matching decomposed into hiring versus retention margins?

To isolate the hiring margin, the authors estimate the dyadic regression restricting to newly hired workers (not present in the firm in year t-1). They find that the probability of being hired by a copartisan owner is 32%–59% higher than by a different-party owner across years. The retention (tenure) margin is estimated by regressing the share of subsequent years a worker remains at the firm on partisan alignment at the time of hire. In the most stringent specification (year-of-hire × firm fixed effects), copartisan hires stay 5.5 percentage points longer (as a share of post-hire years) than different-party hires from the same firm and hire-year cohort. Both margins are significant, and both exhibit stronger political sorting than equivalent estimates for gender or race.

Q4. What is the evidence against political patronage as the primary driver of political assortative matching?

If political patronage (parties pressuring owners to hire copartisans) were the main driver, we would expect political assortative matching to be stronger when the owner’s party is in power locally, as those parties have greater leverage over business owners. The authors estimate a modified dyadic regression distinguishing between cases where the owner’s party is in the ruling coalition of the municipal mayor or state governor versus not in power. The results show that political assortative matching is, if anything, larger for parties not in power. This is inconsistent with patronage being the dominant mechanism and consistent with the discrimination channel being driven by owner preferences rather than external political pressure.

Q5. What does the event study of owner party changes show?

The event study tracks 5,262 owners who switch party affiliation during 2002–2019, comparing their firms to control firms in the same market whose owners remain affiliated to the original party. At the time of the switch, there is a sharp increase of approximately 0.2 standard deviations in hires from the owner’s new party and a corresponding sharp decrease in hires from the old party. Hires from other parties and unaffiliated hires also decline modestly. The share of the workforce affiliated with the new party increases by roughly 5 percentage points and remains elevated in subsequent years. Because nonpolitical network ties (shared school, neighborhood, sports team) are unlikely to dissolve abruptly when an owner changes party, this design provides additional evidence that the change in hiring is driven by a direct change in the owner’s political preferences rather than by network overlap.

Q6. What was the design of the incentivized resume rating experiment and why does it identify political discrimination?

The experiment was conducted with 150 Brazilian business owners recruited from the administrative data (who are already known to be affiliated with one of six major parties), targeting owners with active hiring interest through a leading job platform. Owners rated 20 synthetic resumes with fully randomized features (education, experience, training, skills, formatting). Sixteen resumes had no partisan cues; two contained cues signaling copartisanship with the rating owner; two signaled a party from the opposite side of the political spectrum. Incentives were provided by committing to send respondents real job-seeker profiles from the platform chosen by machine learning based on revealed preferences. Because all resume features other than the partisan cue were randomized, the experiment shuts down shared nonpolitical networks and patronage as explanations; the only channel is the employer’s direct preference for the candidate’s partisan affiliation. The response rate was 11% and the survey was conducted March–May 2022.

Q7. What is the quantitative magnitude of the field experiment result?

Owners rate copartisan resumes 0.213 points higher on the 1–7 Likert scale relative to resumes from the opposite side of the political spectrum (statistically significant at p < 0.05), representing a 7.4% increase relative to the mean rating of different-party resumes (2.950). When resume-level controls (gender, high-skill experience flag, years of experience, programming skills, training) are added, the estimate is 0.254. There is no statistically significant effect on owners’ perceived likelihood that a candidate would accept a job offer (coefficient 0.150–0.158, not significant), suggesting that the observed difference in interest ratings reflects a genuine direct preference for copartisans, not an expectation that copartisans are more likely to accept.

Q8. What do the survey findings add about mechanisms and the prevalence of political discrimination?

The survey of 891 owners and 1,003 workers (response rate 26.84%) presents five candidate mechanisms and asks respondents to evaluate each. Both groups rank belief-based discrimination (owners believe copartisans would be more productive) as the most likely explanation: 47% of owners and 58% of workers partially or strongly agree. Taste-based discrimination is second (36% owners, 52% workers agree), followed by networks (39% owners, 49% workers). Patronage and workers’ preferences attract little agreement from either group. Among owners ranked by single strongest agreement, 29.7% most strongly agree with belief-based discrimination and 22.0% with taste-based, while 29% of all surveyed owners explicitly stated that political views do affect their hiring decisions. These patterns are broadly similar regardless of the respondent’s own political affiliation status.

Q9. How large are the political promotion and wage premia, and how do they compare to gender and race effects?

For promotions, copartisan white-collar workers are 0.448 percentage points more likely to be promoted to manager (relative to unaffiliated co-workers hired in the same firm-year), against a base promotion rate of 2.58% — an effect of approximately 17% of the mean. For blue-collar-to-white-collar promotion, the copartisan premium is 0.44 percentage points against a base rate of 2.98%. For wages, copartisans earn 3.9% more than unaffiliated co-workers within the same firm and year; restricting to the same occupation within the firm, the premium is 2.8%. The political wage premium (3.9%) exceeds the gender wage premium (1.5%) and the race wage premium (1.0%) in the same specification. Workers from a different party than the owner earn 1.6% less than unaffiliated co-workers within the same firm-year.

Q10. Are copartisan workers better qualified than those they displace, and what does this imply for firm performance?

Copartisan workers are significantly less qualified in terms of education relative to their occupation: they are 2.1 percentage points less likely to be educationally qualified for their position than their unaffiliated co-workers within the same firm-year (2.3% relative to the mean qualification rate of 93.2%), with the largest effects for managers. Workers of a different party show only a small and economically negligible qualification gap. The fact that copartisans are paid more, promoted faster, and yet are less qualified is consistent with political discrimination substituting for competence in personnel decisions. The qualification shortfall is specifically attributed to copartisanship and not to shared gender, race, age, or education between owner and worker, as those coefficients are economically small.

Q11. What is the evidence on firm growth and what are the limitations of that evidence?

Firms with a higher share of copartisan workers in the prior year grow less. The estimated coefficient β = −0.071, and a one-standard-deviation difference in the copartisan share is associated with approximately a 1 percentage point gap in annual employment growth, relative to a mean growth rate of 10%. The specification compares firms of the same size and with the same number of affiliated workers in the same year. The result is robust to adding municipality and municipality-industry fixed effects. The authors explicitly characterize this evidence as suggestive, noting the absence of an exogenous source of variation in political discrimination. The negative association is more consistent with taste-based discrimination (Becker, 1957) — in which politically homogeneous firms sacrifice productivity for the owners’ amenity of employing copartisans — than with accurate belief-based discrimination.

Q12. How is political assortative matching distributed across parties and does it depend on party ideology?

The likelihood ratio index shows large assortative matching across the entire political spectrum. For most years, relatively more ideologically extreme parties — on the left (PT, PDT) and on the right (PP, DEM) — display higher assortative matching than more centrist parties (PMDB, PSDB). This pattern is consistent with stronger partisan identity at the extremes leading to stronger preferences for copartisan workers, but the paper does not formally model the mechanism behind this heterogeneity.

Q13. What is the role of workers’ preferences as opposed to employers’ discrimination, and how can wages distinguish them?

If workers have a preference for working with copartisan owners (treating this as a job amenity), compensating differentials theory would predict a negative wage premium for copartisan workers — they would accept lower wages in exchange for working with like-minded owners. The data show the opposite: copartisan workers earn significantly more, not less, than their unaffiliated co-workers. This evidence is inconsistent with workers’ preferences being the primary driver of political assortative matching, and is instead consistent with employers’ discrimination. The survey evidence corroborates this: both owners and workers assign low priority to the “workers’ preferences” mechanism.

Key Concepts

Political assortative matching: The phenomenon by which workers and business owners belonging to the same political party are matched in the labor market at rates significantly exceeding what would occur under random matching within the local labor market. Measured via the likelihood ratio index and dyadic regressions that control for shared demographic characteristics. In this paper, political assortative matching is larger in magnitude than assortative matching along gender or racial lines.

Likelihood ratio index (S): A measure of assortative matching defined as the weighted sum of the ratios of observed same-party co-occurrence probabilities to their expected probabilities under random matching. S > 1 indicates positive assortative matching. The paper uses both a basic version and a geography-adjusted version that computes the index within municipalities to control for geographic concentration of party membership.

Dyadic regression: A regression approach that constructs all possible worker-firm pairs within a defined labor market (municipality × 2-digit industry) to estimate the differential probability that a worker is employed by a copartisan firm relative to a different-party firm. The key advantage is the ability to control simultaneously for multiple shared demographic characteristics between worker and owner, accounting for the correlation of assortative criteria.

Incentivized resume rating (IRR) experiment: A nondeceptive field experiment design (following Kessler et al., 2019) in which business owners rate synthetic resumes with fully randomized characteristics. Truthful rating is incentivized because respondents are told that their revealed preferences will be used to select real job-seeker profiles sent to them by a partner platform via machine learning. This design allows direct identification of employer preference for copartisan candidates while ruling out alternative channels such as shared nonpolitical networks or patronage.

Political wage premium: The percentage wage difference earned by copartisan workers relative to unaffiliated co-workers within the same firm-year (and occupation), after controlling for a full set of socio-demographic characteristics. A positive political wage premium is the paper’s primary piece of evidence that workers’ compensating differentials cannot explain political assortative matching, since amenity-based sorting would predict a negative premium.

Political promotion premium: The differential probability that a copartisan worker is promoted to a higher organizational layer (blue-collar to white-collar, or white-collar to manager) relative to an unaffiliated co-worker hired in the same firm and year, net of demographic controls.

Educational mismatch (Qualified): An indicator variable equal to one if a worker’s educational level meets or exceeds the educational level required by their specific occupation in the CBO (Classificação Brasileira de Ocupações) classification. Used to assess whether politically favored (copartisan) workers are less competent along this observable dimension.

Belief-based discrimination vs. taste-based discrimination: Two distinct theoretical channels for employer political discrimination. Belief-based discrimination (Phelps, 1972; Arrow, 1973) occurs when employers perceive copartisans to be more productive — e.g., because shared political views reduce intra-firm conflict. Taste-based discrimination (Becker, 1971) occurs when employers have a direct utility-affecting preference for copartisan workers, independent of productivity beliefs. The paper treats these as observationally distinct from patronage and network overlap, and uses the negative correlation between political homogeneity and firm growth as suggestive evidence favoring the taste-based channel.

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.