J71 | Macro Paper Warehouse

Equal Pay for Similar Work

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

Layer 1 — Overview

Research Question

This paper studies the labor market effects of “Equal Pay for Similar Work” (EPSW) policies — laws that require firms to pay equal wages to workers of different protected-class identities (e.g., different genders) who perform “similar” work within a firm. EPSW has become increasingly prevalent: as of January 2023, more of the U.S. workforce falls under state EPSW laws than state “Equal Pay for Equal Work” (EPEW) laws. Despite this spread, the equilibrium consequences of EPSW were previously unknown.

Theoretical Framework

The authors develop two theoretical models. The first is a static cooperative game (whose outcomes coincide with the Nash equilibria of a non-cooperative simultaneous-wage-offer game). Homogeneous firms with constant-returns-to-scale production compete for a continuum of heterogeneous workers. Workers belong to one of two groups A or B (e.g., men and women), with group A constituting a β ≥ 1 majority. Each worker’s productivity v is drawn from a group-specific distribution (FA or FB); firms’ willingness to pay equals each worker’s productivity, but can embed taste-based discrimination. The analysis is framed as applying “within job” in a local labor market — only workers performing “similar” work in the eyes of the law.

The second model is a dynamic search-and-bargaining framework with an arbitrary number of firms, search frictions, reallocation frictions, and Nash-in-Nash bargaining. EPSW is introduced as a surprise, and constrained firms choose whether to segregate for one group or remain desegregated (paying a common wage to all workers).

Main Theoretical Findings

Without EPSW, Bertrand competition among firms drives every worker’s wage to equal her productivity; any wage gap between groups A and B exactly reflects the difference in average productivities (EA(v) − EB(v)), whether or not those productivity differences stem from discrimination.

With EPSW, the equilibrium is qualitatively transformed. In the static model (Proposition 2), firms generically fully segregate their workforces: one firm hires all A-group workers and the other hires all B-group workers. EPSW functions as an enforcement mechanism for this segregation analogous to location choices in Hotelling’s model — poaching a worker from the competing firm is costly because EPSW then requires the poaching firm to pay equal wages to all workers it employs. In the core with EPSW (Proposition 3), the wage gap moves in favor of the majority group (A-group, β > 1) in the sense that all core outcomes except one strictly increase the A-group wage advantage. Moreover, firm profits and the magnitude of the wage gap co-move: firms benefit from selecting equilibria with larger wage gaps. The directional conclusion — EPSW benefits the majority group — holds regardless of the distributions of the two groups’ productivities, conditional only on β > 1 for the wage gap; for the log wage gap the additional regularity condition βEA[v] > EB[v] is required.

In the dynamic search model (Proposition 4), all firms eventually segregate under any equilibrium, with the long-run wage ratio moving in favor of the group toward which more firms segregate. Under equitable search and sufficiently low reallocation frictions (Proposition 5), more firms segregate toward the majority group when βEA[v] > EB[v]. Firms that are nearly segregated at the time of EPSW enactment segregate sooner than others (Proposition 6).

Empirical Setting and Design

The authors test these predictions using Chile’s 2009 EPSW (Law 20.348), the country’s first equal pay law, which prohibited paying women less than men (or vice versa) for similar work. Firms with 10 or more long-term workers at the time of announcement (June 2009) face formal grievance procedures and financial penalties (69–1,384 USD per worker-month of violation); firms below this threshold face no financial penalty, providing a clean threshold-based treatment assignment.

The data are matched employer-employee administrative records from the Chilean unemployment insurance system covering January 2005 – December 2013, a random sample of approximately 4% of all firms stratified by size. The main estimation sample restricts to firms with 6–13 total workers at announcement (41% of active firms), and the design is a difference-in-differences (event study) comparing treated (≥ 10 long-term workers) to control (< 10 long-term workers) firms. The identifying assumption is parallel trends between similarly sized firms.

Main Empirical Findings

First, EPSW increases full gender segregation across firms. The share of fully gender-segregated firms increases by 4.4 percentage points (baseline: 34.3% of firms were fully segregated at announcement). Simultaneously, the share of nearly-but-not-fully segregated firms (majority gender share ∈ [0.8, 1)) declines by 4.0 percentage points — a “missing mass” of near-segregated firms consistent with the search model’s prediction that firms on the margin of full segregation segregate most readily (e.g., by separating the sole worker of the “wrong” gender). Moreover, firms that are nearly segregated at announcement experience an 8.7 percentage point increase in full segregation post-EPSW, compared to 2.8 percentage points for firms not nearly segregated at announcement.

Second, EPSW shifts the gender wage gap in favor of the local labor market majority group. In male-majority local labor markets (defined by industry × county), EPSW increases the gender wage gap in favor of men by 4.3 percentage points. In female-majority local labor markets, EPSW decreases the gender wage gap (i.e., in favor of women) by 6.2 percentage points. The wage gap change is primarily driven by reductions in minority-group wages: women’s average wages in male-majority markets fall by 3.3 percentage points, and men’s average wages in female-majority markets fall by 4.5 percentage points; there are no statistically significant changes in majority-group wages. Because men dominate Chile’s overall labor market (approximately 5/6 of all workers are employed in majority-male local labor markets), the overall effect of EPSW is to increase the gender wage gap (in favor of men) by 2.7 percentage points. Pre-treatment coefficients are statistically indistinguishable from zero across all specifications, supporting the parallel trends assumption. These findings are robust across six alternative specifications covering different samples, fixed-effect structures, and controls.

Scope Conditions

Theoretical results apply within a set of “similar” workers in a given local labor market — the paper does not predict differential effects across job types within a firm (e.g., custodians vs. lawyers) that do not perform similar work. Empirical results are identified for firms with 6–13 workers and pertain to Chile’s formal sector (informal labor share ~25% in 2009). Predictions on the wage ratio (log wage gap) require the additional regularity condition βEA[v] > EB[v], which is consistent with the Chilean data.

In depth

Q1. What is the core mechanism by which EPSW leads firms to fully segregate in the static model?

A: EPSW makes cross-group poaching prohibitively costly. If a firm that hires only A-group workers were to hire even a positive measure of B-group workers, EPSW would — by transitivity — require it to pay the same wage to all workers. This eliminates the firm’s ability to exploit productivity heterogeneity across workers; it would have to raise all wages to match the highest worker, destroying profit. As a result, firms segregate in equilibrium to avoid the bite of EPSW entirely: each firm caters to one group, and the within-group wage schedule remains unconstrained. The mechanism is analogous to Hotelling’s location model: segregation serves as the enforcement device for avoiding the equal-pay constraint.

Q2. How does the equal profit condition generate a wage gap in favor of the majority group?

A: In any core outcome under EPSW (Proposition 3), the Equal Profit Condition requires both firms to earn the same total profit. When there are β > 1 A-group workers (more than B-group workers), the firm serving A-group workers must pay higher average wages per worker to extract the same total profit from a larger pool, relative to the firm serving a smaller B-group. This mechanically raises A-group average wages relative to B-group average wages. Crucially, this directional conclusion — EPSW widens the majority-group wage advantage — holds regardless of the shapes of FA and FB, meaning it is robust to any underlying discriminatory or non-discriminatory productivity differences.

Q3. What is the baseline (without-EPSW) wage gap, and how does EPSW change it?

A: Without EPSW, Proposition 1 establishes that every worker is paid exactly her productivity in any core outcome (full employment, wages = productivity). Therefore, the wage gap equals EA(v) − EB(v) and the wage ratio equals EA(v)/EB(v): any gap reflects only productivity differences (including discrimination embedded in willingness to pay). Under EPSW, Proposition 3 shows that all core outcomes except a single (measure-zero) one strictly widen the wage gap beyond this level. The wage ratio result (Proposition 3, Part 4) requires the additional condition βEA[v] > EB[v] — that the majority group is not sufficiently less productive or more discriminated against to reverse the direction.

Q4. How does the dynamic search model modify the static predictions?

A: In the dynamic model (Proposition 4), full segregation is achieved in finite time T in any equilibrium, not instantaneously. Prior to T, firms make sequential segregation decisions; workers displaced by firm desegregation choices are replaced at rate ρ ∈ [0,1]. The long-run wage ratio is determined by the ratio nA/nB — the number of firms segregating toward group A versus B. If nA > nB, the long-run wage ratio moves in favor of A; if nA = nB, the policy has no long-run effect on the wage ratio. The key departure from the static model is that this outcome depends not only on the majority group size but also on search intensities and reallocation frictions (high firm tenure/low d can make segregating toward the majority costly if the firm already employs many minority-group workers).

Q5. Under what conditions does the dynamic model predict that more firms segregate toward the majority group?

A: Proposition 5 states that for sufficiently large d (fast worker turnover / low reallocation frictions) and equitable search (equal search intensity across firms within a group), the number of firms segregating toward A satisfies nA ∈ [xA−1, xA+1], where xA is defined by an equal-profit condition. Moreover, if βEA[v] > EB[v] (the majority group is collectively more valuable), then nA ≥ nB. Without equitable search, the conclusion holds under more stringent conditions: for any search intensity vector r, there exist d* and β* such that for d > d* and β > β*, any equilibrium yields nA > nB. Empirically, 94% of local-labor-market-by-month units in Chile exhibit more firms segregating toward the majority gender post-EPSW, consistent with these conditions being met.

Q6. Why do firms that are nearly segregated at announcement respond most strongly to EPSW?

A: Proposition 6 establishes that firms with a low ratio of minority-group to majority-group search intensity (i.e., nearly segregated in employment) segregate earliest, provided the discount rate is sufficiently low. The intuition is that for a nearly segregated firm, the cost of segregating — separating the few minority-group workers — is small relative to the costs of remaining desegregated (paying a common wage that compresses profit, and being unable to poach new workers). Empirically, firms nearly segregated at announcement (majority gender share ∈ [0.8,1) at announcement) show an 8.7 percentage point increase in full segregation post-EPSW, roughly three times larger than the 2.8 percentage point effect for firms not nearly segregated at announcement. This “missing mass” pattern (decline in near-segregation matched by increase in full segregation) is also consistent with Proposition 6.

Q7. What is the heterogeneous effect of EPSW on the wage gap by local labor market type?

A: The empirical design allows the wage gap effect to differ by local labor market (LLM) majority type (male vs. female). In male-majority LLMs (firm industry × county pairs where males comprise more than 50% of workers in June 2009), EPSW increases the gender wage gap in favor of men by 4.3 percentage points (SE = 0.0116). In female-majority LLMs, EPSW decreases the gender wage gap (in favor of women) by 6.2 percentage points (SE = 0.0234). These findings precisely match the theoretical prediction that EPSW benefits whichever group is in the majority of the local labor market. The dynamic event studies show no pre-trends in either subsample; effects begin at announcement (τ = 0) and grow over time.

Q8. What drives the wage gap change — majority wages rising or minority wages falling?

A: The change is primarily driven by a reduction in the minority group’s average wages, not an increase in majority wages. Women’s average wages in male-majority labor markets fall by 3.29 percentage points (SE = 0.0111) in treated versus control firms post-EPSW. Men’s average wages in female-majority labor markets fall by 4.45 percentage points (SE = 0.0178) in treated versus control firms post-EPSW. There are no statistically significant changes in the average wages of the majority group of workers within any LLM type. This is consistent with the model’s mechanism: segregation reduces competition for minority-group workers (fewer firms competing for them), depressing their wages.

Q9. What is the aggregate (economy-wide) effect of EPSW on the gender wage gap in Chile?

A: Because approximately 5/6 of all Chilean workers are employed in male-majority local labor markets (men have higher labor force participation, with female labor force participation at roughly 30% in 2009), the overall effect of EPSW is to increase the gender wage gap in favor of men by 2.74 percentage points (SE = 0.0102). This is a net effect that averages the positive (pro-male) gap increase in male-majority markets and the negative (pro-female) gap decrease in female-majority markets, weighted by market sizes.

Q10. How does the identification strategy deal with anticipation and compositional changes?

A: Treatment status is assigned based on firm size at the time of policy announcement (June 2009) rather than enactment (November 2009), creating an intent-to-treat framework: some “treated” firms may fall below the threshold by enactment, and some “control” firms may rise above it, both attenuating the estimates (implying estimated effects are plausible lower bounds). The no-anticipation assumption is supported by the absence of statistically significant pre-trends in either the segregation or wage-gap specifications. To address compositional changes in worker characteristics across LLMs induced by EPSW itself, the wage regressions include time fixed effects interacted with human capital dimensions (education, contract type, age decade) and firm comparison groups, controlling for observable composition shifts. Placebo tests at alternative firm-size thresholds find no statistically or economically meaningful effects, supporting the causal interpretation.

Q11. How does EPSW in Chile compare to EPEW theoretically and in the literature?

A: EPEW requires equal pay only for workers doing exactly equal work, which creates an easily exploitable loophole: firms can proliferate job titles or marginally differentiate duties to avoid compliance. EPSW closes this by requiring equal pay across a coarser “similar work” category, making evasion harder. Theoretically, the prior EPEW literature (Bhaskar et al. 2002, Kaas 2009, Lagerlöf 2020, Lanning 2014) generated ambiguous directional predictions — equal pay laws could either increase or decrease wage disparities within the same paper. The authors attribute this ambiguity to EPEW models’ requirement that workers be exactly equally productive. By contrast, EPSW applies across workers with heterogeneous productivities, and the authors derive unambiguous predictions: full segregation and a wage gap shift toward the majority group, both of which are confirmed empirically.

Q12. What is the analogy to “best-price guarantees” in product markets?

A: The paper draws a methodological parallel to most-favored-customer (MFC) clauses in product markets. MFC clauses commit firms to rebating past consumers if prices fall, which directly equalizes payments across buyers but unintentionally raises firm market power. In the EPSW setting, the policy plays the role of a best-wage guarantee — but because firms compete for workers, the constraint binds off the equilibrium path. Firms segregate so that no firm is ever exposed to the equal-pay constraint in equilibrium, yet the threat of the constraint (if a firm deviates and hires from both groups) effectively differentiates labor costs across groups, driving the unintended wage effects. This is related to “artificial” switching costs that create local market power in consumer markets (Klemperer, 1987).

Key Concepts

Equal Pay for Similar Work (EPSW): A legal constraint requiring that within a firm, workers belonging to different protected-class identities (e.g., different genders) who perform “similar” work receive equal wages. Distinguished from “Equal Pay for Equal Work” (EPEW) by its coarser similarity standard, which cannot be evaded by minor job-title differentiation. In the model, this constraint is formalized as: a firm cannot hire positive measures of workers from two different groups such that all workers in one group receive strictly higher wages than all workers in the other group; by transitivity, a firm hiring from both groups must pay almost all workers the same wage.

Core Outcome: The solution concept used in the static model, drawing on cooperative game theory (Shapley–Shubik assignment game). An outcome (specifying which firm hires each worker and at what wage) is in the core if no firm and subset of workers can form a blocking coalition that makes both the firm and each worker in the coalition strictly better off. The paper uses this concept because its pure-strategy Nash equilibrium outcomes (in the associated non-cooperative simultaneous wage-offer game) exactly coincide with the core outcomes under the restriction that firms pay the same wage to all workers of the same type.

Full Segregation: A labor market outcome in which each firm employs workers from only one group (all A-group workers at one firm, all B-group workers at the other). The paper proves (Proposition 2) that EPSW generically forces full segregation in equilibrium, because any deviation to hire from both groups exposes the firm to the equal-pay constraint. Empirically measured as a binary indicator for whether all workers at a given firm in a given month are of the same gender.

Near Segregation: A firm-level state in which the majority gender constitutes 80–99% of the firm’s workforce (the majority gender share is in [0.8, 1)). The paper uses this as a complementary outcome to full segregation; theory (Proposition 6) predicts a decline in near segregation post-EPSW because firms in this state face the lowest cost of transitioning to full segregation. Empirically, the near-segregation share falls by 4.0 percentage points post-EPSW, mirroring the 4.4 percentage point rise in full segregation.

Local Labor Market (LLM): Defined in the empirical analysis as a firm’s geographic county interacted with its industry code, creating 321 × 21 potential cells. The LLM is classified as male-majority or female-majority based on the share of female workers across all firms in the industry-county pair in June 2009. This is the unit at which the “majority group” for Proposition 3’s wage gap prediction is defined, and the level at which the heterogeneous wage effects of EPSW are estimated.

Equal Profit Condition: A necessary condition of any core outcome (with or without EPSW): both firms must earn the same total profit in equilibrium. Under EPSW with full segregation, this condition determines the relative average wages of the two groups — because firm sizes differ (β A-group workers vs. 1 B-group worker), equal profit requires the firm serving the larger group to pay higher average wages, mechanically moving the wage gap in favor of the majority group.

Nash-in-Nash Bargaining: The bargaining protocol used in the dynamic search model, following Horn and Wolinsky (1988). Each bilateral worker-firm bargain splits the available surplus in proportion to exogenous bargaining power parameter Δ ∈ (0,1), taking as given the outcome of all other bilateral bargains. A worker’s disagreement point is the wage she would receive from bargaining with the next firm in her search order. This generates the result that a worker’s realized payoff is increasing in the number of segregated (non-EPSW-constrained) firms competing for her, connecting firm segregation decisions to wage determination.

Reallocation Friction: In the dynamic search model, represented by a low departure probability d ∈ (0,1) for existing employees. When d is low, firms retain a large fraction of their workforce across periods, making segregation costly because the firm must separate from any existing workers of the “wrong” group. The paper shows (Proposition 5) that for sufficiently large d (low frictions), the equal-profit condition approximately pins down the number of firms segregating toward each group, and for d above a threshold, the majority group attracts weakly more segregating firms.

Silence to Solidarity: How Communication About a Minority Affects Discrimination

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

This paper examines how two types of communication about a minority group affect discriminatory behavior: (i) horizontal communication between majority-group members, and (ii) top-down communication from agents of authority such as the legal system. The setting is urban Chennai, India, where the paper measures discrimination against thirunangai — a community of transgender women who are India’s most visible LGBTQ+ group — in a field experiment with 3,397 participants.

Discrimination is measured using incentivized hiring choices. Participants are offered a free grocery delivery and make 10 binary choices over which worker will carry out the delivery, with worker gender (cisgender male, cisgender female, or transgender) varying across options. The stakes are real: one choice is randomly selected and implemented 2–9 weeks later. Participants in the control condition are highly discriminatory: they are 19 percentage points (32%) less likely to hire a transgender worker than a non-transgender worker (p<0.001), and are willing to sacrifice grocery items worth 1.9 times their median daily per capita food expenditure to avoid a 15-minute interaction with a transgender worker.

The first main treatment involves randomly assigning participants to a 3-person group discussion with two neighbors, in which they discuss and make collective hiring choices over the same options. The key outcome is participants’ subsequent private, individual hiring choices. The discussion eliminates anti-transgender discrimination on average: participants in the discussion arm are 17 percentage points (42%) more likely to select a transgender worker in their private post-discussion choices relative to the control group (p<0.001), so that discrimination is no longer statistically distinguishable from zero (p=0.30). The discussion’s effect is partially persistent: approximately one month later, discussion participants are still 4 percentage points more likely to select transgender workers in hypothetical hiring choices (p=0.03), representing roughly 25% of the short-run effect.

The second main treatment cross-randomizes a video shown before hiring choices. The legal rights video informs participants of a Supreme Court ruling affirming that transgender people hold the same fundamental constitutional rights as other citizens. This reduces discrimination by 10.3 percentage points (p<0.001). A rights messaging video — which argues that transgender people should have equal rights without invoking legal authority — reduces discrimination by a smaller 5.8 percentage points (p=0.001), and there is some evidence the legal-authority version is more effective (p of difference in [0.01, 0.12]). However, the legal rights video’s effect is only 59% as large as the discussion’s effect (p of difference in [0.002, 0.04]), and it does not persist at the one-month follow-up (p in [0.12, 0.51]).

The paper rules out two candidate mechanisms for the discussion’s effects and supports a third. First, the discussion does not work primarily through correcting misperceived norms: while control-group participants do overestimate peer discrimination by 5 percentage points, the discussion reduces predicted discrimination by 24 percentage points — far more than a corrected misperception could explain (at most 21% of the effect under generous assumptions). Second, the discussion does not work through virtue signaling alone: a “No discussion (public)” arm in which participants make individually-visible choices shows no reduction in discrimination on average (p=0.83). Third, the paper provides affirmative evidence for a persuasion channel: participants in a “listener” arm, who silently observe a 2-person discussion without participating, discriminate 13 percentage points less than the control group (p<0.001), an effect that is highly persistent at the 2–9 week follow-up (11 percentage points, p<0.001). The persuasion mechanism is further supported by the finding that pro-trans participants are more vocal: each additional transgender worker chosen in post-discussion private choices is associated with a 32% higher probability of speaking first (p=0.03) and a 27% higher probability of dominating the discussion (p=0.02). Statements about transgender workers during discussions were 5.7 times more likely to be positive than negative. Listeners who heard moral argumentation about equality, rights, and giving opportunities subsequently discriminated less (p<0.001).

Scope conditions: the study is conducted among urban Chennai residents (85% female), where transgender identity is visually recognizable and socially salient, awareness of the 2014 Supreme Court ruling is low (36% could not identify a single legal right transgender people hold), and a wedge exists between descriptive norms (high actual discrimination) and prescriptive norms (93% of the control group rate explicit discrimination as wrong). The model’s “sweet spot” logic implies these effects may not generalize to settings where discrimination is either near-universal (no privately pro-trans individuals to be vocal) or already minimal (no incentive to persuade).

Q: How is anti-transgender discrimination measured in the experiment? A: Participants make 10 incentive-compatible binary hiring choices over grocery delivery workers, with one choice randomly selected and implemented 2–9 weeks later. Discrimination is defined as the reduction in the probability of selecting the alternative worker when that worker is transgender versus non-transgender, conditional on other option characteristics such as items offered and reliability score. Participants are told they will have a 15-minute conversation with the selected worker, ensuring anticipated social contact. The design is framed as market research to obfuscate the study’s purpose; only 8% correctly guessed the true focus.

Q: How large is baseline discrimination in the control group? A: In the No discussion (private) control condition, participants are 19 percentage points (32%) less likely to hire a transgender worker than a non-transgender worker (p<0.001). In willingness-to-pay terms, participants sacrifice grocery items worth 1.9 times their median daily per capita food expenditure (Rs. 127 on a base of Rs. 67) to avoid selecting a transgender worker. Even when a transgender worker dominates on both items and reliability score, participants in the control group still select the non-transgender worker 47% of the time.

Q: What is the main effect of the 3-person group discussion on subsequent discrimination? A: Participants who engage in a group discussion with two neighbors are 17 percentage points more likely to select a transgender worker in their subsequent private individual choices (p<0.001). This eliminates average discrimination entirely: in the discussion arm, the probability of selecting a transgender worker is not statistically distinguishable from the probability of selecting a non-transgender worker (p=0.30). The willingness-to-pay to avoid a transgender worker falls from Rs. 127 to Rs. 13 (p of difference < 0.001), and is no longer significantly different from zero (p=0.265).

Q: How persistent are the effects of the group discussion? A: At the 2–9 week follow-up survey (mean 35 days), discussion participants are approximately 4 percentage points more likely to select transgender workers in hypothetical hiring choices (p=0.03). This represents approximately 25% of the short-run 17 percentage point effect, a decay rate comparable to the persistence of US political advertising effects in the political science literature (Hill et al., 2013, estimate 10–15% remaining after 30 days).

Q: What is the effect of the legal rights video, and how does it compare to the discussion? A: The legal rights video — informing participants of the Supreme Court ruling affirming transgender people’s fundamental constitutional rights — increases the probability of selecting a transgender worker by 10.3 percentage points (p<0.001). The rights messaging video, which argues that transgender people should have equal rights without invoking legal authority, increases it by 5.8 percentage points (p=0.001). The legal rights video’s effect is only 59% as large as the discussion’s 17 percentage point effect (p of difference in [0.002, 0.04]), and unlike the discussion, neither video’s effect is detectable at the one-month follow-up (p in [0.12, 0.51]).

Q: Does the legal rights video work through a different channel than the rights messaging video? A: There is evidence that the legal authority of the Supreme Court matters beyond the content of the rights message. The legal rights video is more effective than the rights messaging video at reducing discrimination (p of difference in [0.01, 0.12]), and the legal rights video (but not the rights messaging) affects participants’ beliefs about the legal status of transgender people (as measured by a summary index). Both videos shift perceived descriptive norms — participants predict others will select transgender workers more, by 2–6 percentage points — but neither significantly affects attitudes as measured by a list experiment or disapproval questions.

Q: Does the discussion work through correcting misperceived norms? A: This channel can account for at most a small fraction of the effect. Control-group participants do overestimate peer discrimination by 5 percentage points in incentivized predictions (p<0.001, as measured by predicted probability of selecting a transgender worker). However, the discussion reduces predicted discrimination by 24 percentage points (p<0.001), far exceeding the initial misperception. Even under generous assumptions in which the misperception is precisely corrected, this mechanism could account for no more than 21% of the discussion’s treatment effect (95% CI: [8.9%, 32.5%]).

Q: Does the discussion work through virtue signaling? A: The evidence rules out virtue signaling as the primary channel. The “No discussion (public)” treatment arm makes participants’ individual hiring choices visible to their group members, exogenously increasing social image concerns in the absence of a discussion. This has no detectable average effect on discrimination (p=0.83), indicating that social image concerns alone — without the persuasive content of an actual discussion — do not explain the reduction in discrimination generated by the group discussion.

Q: What is the evidence for the persuasion mechanism? A: The “listener” treatment arm provides direct evidence. In this arm, one participant silently observes a 2-person discussion without speaking, then makes private individual choices. Listeners discriminate 13 percentage points less than the control group (p<0.001), an effect statistically indistinguishable from full discussion participants. Since listeners changed their behavior based solely on what they heard and saw, this constitutes evidence of persuasion. The listener effect is highly persistent at the 2–9 week follow-up (11 percentage points, p<0.001) and holds on a robustness outcome designed to be completely private. The implied persuasion rate is 29%, described as high relative to values in the literature (DellaVigna & Gentzkow, 2010).

Q: Why do pro-trans participants persuade others — what drives the discussion’s content? A: Pro-trans participants are disproportionately vocal. Each additional transgender worker chosen in post-discussion private choices (a proxy for pro-trans private attitudes) is associated with a 32% higher probability of speaking first (p=0.03) and a 27% higher probability of dominating the discussion (p=0.02), but only when discussing a choice involving a transgender worker. The overall tone of discussions is strongly pro-trans: statements about transgender workers are 5.7 times more likely to be positive than negative. Participants who hear moral argumentation about equality, rights, and giving opportunities subsequently discriminate significantly less (p<0.001).

Q: Does the discussion work by changing statistical (belief-based) discrimination? A: Partially, baseline discrimination in the control group is partly statistical: despite transgender workers having the same average reliability scores as others, participants rate them as less likely to complete a delivery, and revealing the true reliability score makes participants 2.9 percentage points more likely to select a transgender worker (an effect unique to transgender workers). However, the discussion does not significantly affect beliefs about transgender workers’ reliability, and there is no detected reduction in the belief-based component of discrimination in the discussion arm (though the test is underpowered).

Q: Are the effects of the discussion and the legal rights video additive? A: The two interventions appear to combine approximately linearly for the legal rights video: there are no detected interaction effects (p in [0.83, 0.96]). By contrast, there is weak evidence of a negative interaction between the rights messaging video and the discussion, suggesting these two may be substitutes — consistent with the rights messaging video’s content being similar to the pro-trans moral argumentation already present in discussions.

Q: What alternative explanations are ruled out? A: The paper tests and finds no support for: (i) photo characteristics such as perceived caste driving results; (ii) social image concerns affecting even post-discussion private choices (the “extra private” robustness outcome designed to be unobservable by neighbors yields similar results); (iii) increased contemplation or deliberation about choices; (iv) experimenter demand effects or social desirability bias (treatment effects do not differ for the 8% who guessed the study’s purpose); (v) increased salience of the transgender category; and (vi) cheap talk from low stakes (choices were incentive-compatible and implemented).

Q: What is the study’s theoretical model for why pro-trans participants speak out? A: The paper develops a model combining social signaling (people want to fit in with their group; Bénabou & Tirole, 2006) with direct persuasion (participants can change each other’s preferences through messages). Under the right conditions, only pro-trans participants send persuasive pro-trans messages. This occurs in a “sweet spot” range: when average discrimination is not so strong that no one is privately pro-trans, and not so weak that pro-trans participants lack an incentive to persuade (since they are already in the majority). The context in Chennai — high actual discrimination but strong social norms against it — satisfies this sweet spot condition.

Q: What are the policy implications regarding horizontal versus top-down communication? A: In this context, facilitating horizontal communication between neighbors is a more effective tool for reducing discrimination than top-down communication about legal rights: the discussion’s effect is 1.7 times larger than the legal rights video (17 p.p. vs. 10.3 p.p.) and partially persists at one month, whereas the legal rights video’s effect does not persist. However, the legal rights video does reduce discrimination relative to the rights messaging video, suggesting that communicating the legal authority of the Supreme Court carries independent weight beyond rights advocacy messaging. Both interventions are complementary when combined.

Horizontal communication: Communication between members of the majority group about a minority, as distinct from contact between majority and minority groups or top-down communication from authority. In this paper, operationalized as a group discussion among three neighbors who make collective hiring choices.

Top-down communication: Communication from agents of authority — here, the legal system — about a minority group’s rights. Measured via a video informing participants of a Supreme Court ruling affirming transgender people’s constitutional rights.

Anti-transgender discrimination: In the paper’s own measurement, the reduction in the probability that a worker is chosen because they are transgender (relative to being non-transgender), conditional on other delivery option characteristics. Measured in incentivized, privately-elicited binary hiring choices.

Expressive law hypothesis: The theory that changes in the law affect behavior by changing people’s perception of the prevailing social norm, not (only) through deterrence. The paper tests this by comparing a legal rights video (invoking Supreme Court authority) to a rights messaging video with identical content but no legal backing, finding the legal-authority version more effective.

Persuasion channel: The mechanism by which discussion participants change each other’s preferences through persuasive messages, particularly moral arguments about equality and rights. Distinguished in the paper from virtue signaling (publicly visible pro-trans behavior) and norm correction (updating misperceived beliefs about peer behavior).

Pluralistic ignorance: A setting in which people misperceive how common discriminatory attitudes are among their peers, potentially hiding genuine minority support for the discriminated group. The paper tests this as a candidate mechanism and finds it can account for at most 21% of the discussion effect.

Sweet spot condition: The range of average group discrimination levels in which pro-trans participants have both the motivation and opportunity to speak out persuasively — discrimination is not so universal that no one is privately pro-trans, and not so minimal that the pro-trans participants feel no need to persuade others. The paper argues the Chennai context satisfies this condition.

Why Is Workplace Sexual Harassment Underreported? The Value of Outside Options amid the Threat of Retaliation

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

Layer 1 — Summary

Research question and argument

Dahl and Knepper address the long-standing puzzle of why workplace sexual harassment is chronically underreported despite high estimated prevalence. Survey evidence indicates that no fewer than 1 in 28 U.S. workers report annual victimization, yet only 1 in 11,000 workers files a formal charge with the Equal Employment Opportunity Commission (EEOC). Even following the #MeToo movement, formal charges rose only about 10%, leaving an enormous gap unexplained.

The paper’s central hypothesis is that employers coerce victims into silence through the credible threat of retaliatory firing. The key mechanism: because reporting constitutes a “protected activity” triggering employer notification, workers who fear losing their jobs will suppress claims. This threat is most binding when a worker’s outside options are weak — when it is hard to find a new job or when unemployment insurance (UI) benefits are thin. The paper tests this hypothesis by asking whether external shocks that reduce the value of outside options increase the threshold of harassment severity above which workers are willing to report.

Measurement strategy

Measuring underreporting directly is impossible by definition. The authors’ key methodological insight is to use the selectivity of filed charges as an indirect proxy. Under mild assumptions, if workers become more selective about which incidents they report, the average quality of filed charges must rise. The authors measure quality using the EEOC’s own merit determination: a charge is deemed meritorious if the employer settles, the claimant withdraws upon receipt of benefits, or the EEOC finds reasonable cause after investigation. The merit rate thus serves as an observable proxy for the (unobservable) degree of underreporting.

Baseline descriptive evidence supports the mechanism’s relevance: across 2000–2015, sexual harassment charges were nearly 50% more likely to be meritorious than non-harassment charges (27.0% vs. 18.6%), and more than twice as likely to involve employer retaliation (63.4% vs. 30.7%). The proportion of EEOC sexual harassment cases involving retaliation rose from 52% in 2000 to 72% in 2015, a period over which the annual volume of filed charges fell by 37%.

Analysis 1 — Labor market conditions (2000–2015)

The first empirical design exploits monthly variation in state-industry unemployment rates over 2000–2015 using EEOC microdata on individual charges. The regression controls for industry, state, and time fixed effects, isolating within-state-industry variation in unemployment. The identifying assumption is that a worker’s willingness to file depends only on her outside options and the severity of harassment she experiences, conditional on fixed effects.

The results indicate that each one percentage point increase in a state-industry’s monthly unemployment rate is associated with a 0.5–0.7% increase in the probability that a filed charge is deemed meritorious by the EEOC. This is consistent with the hypothesis that workers become more reluctant to report as outside labor market options weaken.

Heterogeneity analysis using linked EEO-1 establishment data strengthens the interpretation. The effect is amplified in industries that employ a larger fraction of men and in establishments where male managers account for a higher share of supervisory roles. Oﬀending establishments in the sample have, on average, 2.8 percentage points more male employees and 5 percentage points more male managers than non-offending establishments. The selectivity-unemployment gradient is larger in these male-dominated environments, consistent with a role for gendered power disparities in enabling employer retaliation.

Analysis 2 — North Carolina UI reform (quasi-experiment)

The second design exploits North Carolina’s 2013 UI reform as a plausibly exogenous reduction in the value of outside options. In response to the near-insolvency of its UI trust fund following the Great Recession, North Carolina simultaneously reduced maximum weekly benefits by approximately 35% (from $535 to $350 per week) and cut maximum benefit duration from 26 to 20 weeks. Together, these changes reduced the maximum total regular UI benefit available to North Carolinians by approximately 50%, from roughly $14,000 to $7,000. These reforms also violated the Congressional non-reduction rule, making individuals ineligible for an additional 47 weeks of federal Emergency Unemployment Compensation benefits, further amplifying the effective cut. North Carolina was the only state to simultaneously reduce both the level and duration of benefits.

The authors implement a difference-in-differences design comparing North Carolina to other Southern states that did not change their UI programs, controlling for state and month-year fixed effects. Pre-reform parallel trends are documented via event study. Administrative UI recipiency data show that the short-term UI recipiency rate in North Carolina fell from 33% to 10% — a 59% decline relative to control states — within roughly two years of the reform.

The main finding is that the selectivity of sexual harassment charges filed in North Carolina increased by approximately 7 percentage points following the reform, representing more than a 30% increase relative to control states. This is consistent with the hypothesis that reduced UI generosity raises the cost of a retaliatory firing, causing workers to suppress all but the most severe harassment incidents.

The authors note that North Carolina also reduced corporate and personal income taxes shortly after the UI reform. Because tax cuts should increase both labor demand and labor supply (insofar as substitution effects dominate income effects), this would tend to reduce the reporting threshold, leading them to interpret the 30%+ estimate as a lower bound on the causal effect of the UI reform on selectivity.

Formal model

The paper presents a threshold model of reporting behavior adapted from Boone and Van Ours (2006). Workers choose a reporting threshold: the minimum harassment severity above which they will file a charge. The threshold rises when the value of outside options falls, either because the probability of finding a new job declines (recession) or because unemployment benefits shrink. The model predicts that the merit rate of filed charges will rise as outside options weaken. The model explicitly does not predict the volume of charges, because firm behavior — which may adjust endogenously to higher reporting thresholds — is not modeled.

Scope conditions

All findings concern formal EEOC charges filed in the United States between 2000 and 2015 (analysis 1) and through the post-2013 reform period (analysis 2). The EEOC definition of illegal harassment requires severity sufficient to create a “hostile or offensive work environment” or an adverse employment action. The paper’s merit measure captures harassment that exceeded this legal threshold; non-meritorious charges may still involve some level of misconduct. The sample for establishment-level heterogeneity analyses covers private firms with 100 or more employees (EEO-1 filers), approximately 40% of U.S. employees. The mechanism specifically concerns retaliation-driven suppression of formal reporting; effects on informal or anonymous reporting cannot be assessed.

In depth

Q1. Q: What is the core mechanism the paper proposes to explain underreporting?

A: Employers threaten workers with retaliatory firing for engaging in protected activity (filing an EEOC charge). Because the EEOC notifies the named employer within 10 days of receiving a charge, worker anonymity is rarely preserved. When a worker’s outside options are weak — because unemployment is high or UI benefits are thin — the expected cost of a retaliatory firing is higher, raising the severity threshold above which a victim is willing to report. Workers therefore “tough it out” rather than risk their current job.

Q2. Q: How does the paper measure something that is, by definition, not reported?

A: By using the quality of filed charges as a proxy for the degree of underreporting. Under the threshold model, if workers only report when harassment exceeds a higher bar, the average quality of what does get filed must rise. The EEOC’s own merit determination (settlement, withdrawal with benefits, or reasonable-cause ruling) provides an objective, externally-assessed quality measure. An increase in the merit rate signals that the population of filed charges has become more selected — that is, that the unreported fraction has grown.

Q3. Q: What does the 0.5–0.7% figure mean, and what is its interpretation?

A: Each one percentage point increase in a state-industry’s monthly unemployment rate is associated with a 0.5–0.7 percentage point increase in the probability that a filed sexual harassment charge receives a merit designation from the EEOC. This is interpreted as evidence that workers become more selective — filing only more severe cases — as outside options weaken, consistent with higher underreporting at lower harassment thresholds.

Q4. Q: Why did the number of EEOC sexual harassment charges fall by 37% between 2000 and 2015, even as retaliation rates rose?

A: The paper offers the interpretation that firms have become more effective at credibly threatening retaliation to suppress reporting. The 37% volume decline does not imply harassment has diminished; it may reflect a rising fraction of victims staying silent. The authors note the model does not make a prediction about volume because firm behavior is not modeled — volume depends on both worker reporting thresholds and employer conduct.

Q5. Q: Why is North Carolina’s UI reform particularly well-suited as a natural experiment?

A: Four features make it attractive. First, the reform was motivated by trust fund insolvency rather than local labor market conditions, making it more plausibly exogenous to harassment reporting trends. Second, it was implemented during a period of historically high unemployment, when the social safety net was unusually relevant to workers considering risky actions. Third, the cuts affected both the intensive margin (benefit level, down ~35%) and the extensive margin (duration, from 26 to 20 weeks; added eligibility restrictions), with total maximum benefits cut by approximately 50%. Extensive-margin cuts are likely particularly salient for workers worried about a retaliatory firing. Fourth, the cuts to regular UI were permanent and primary, rather than affecting supplemental federal programs.

Q6. Q: What role does industry and establishment gender composition play?

A: The underreporting effect — proxied by the merit-unemployment gradient — is amplified in industries with a larger fraction of male coworkers and in establishments with a higher fraction of male managers. Establishments named in sexual harassment charges have, on average, 2.8 percentage points more male employees and 5 percentage points more male managers than non-respondent establishments. The male-manager underreporting gradient is further amplified by higher unemployment, suggesting gendered power disparities interact with labor market conditions to suppress reporting.

Q7. Q: Does the paper make predictions about the volume of charges, not just their quality?

A: No. The threshold model explicitly does not model firm behavior and makes no prediction about charge volume. Whether volume rises or falls following a labor demand shock is theoretically ambiguous: firms may respond to higher reporting thresholds by escalating harassment (increasing both incidence and severity), or may not respond at all. The identifying assumption requires only that a worker’s willingness to file depends on her outside options and the severity of harassment she experiences — not on firm behavior.

Q8. Q: What is the “value of a statistical harassment” (VSH) figure, and how does it relate to the paper’s motivation?

A: Hersch (2018) estimates the VSH for serious cases at approximately $7.6 million, roughly comparable to the value of a statistical life (VSL). Dahl and Knepper cite this figure to underscore the magnitude of the underreporting problem: with an estimated 5 million workers victimized annually, the social costs of suppressed reporting are substantial. The comparison to VSL motivates why closing the reporting gap matters for welfare, not just legal compliance.

Q9. Q: What is the ex-ante moral hazard interpretation of the UI results?

A: Most UI research focuses on ex-post effects — how benefit generosity affects job search behavior for workers who have already lost their jobs. Dahl and Knepper document an ex-ante moral hazard effect: UI generosity affects the behavior of currently employed workers by changing the expected cost of actions (reporting harassment) that might trigger job loss. Lower UI generosity raises the effective cost of a retaliatory firing, discouraging reporting. This is analogous to, but in the opposite direction from, Lusher et al. (2020), who find that UI expansions reduced productivity among currently employed workers.

Q10. Q: What does the parallel-trends evidence show for the NC difference-in-differences?

A: The paper presents an event study documenting parallel pre-reform trends in the merit rate between North Carolina and control states. The control group is other Southern states that did not change their UI programs during the sample period, excluding AR, FL, GA, and SC (which made changes) and the West South Central division (which exhibited differential pre-trends). The UI recipiency rate tracks closely between NC and control states prior to July 2013, then diverges sharply thereafter, dropping from 33% to 10% in North Carolina within two years — a 59% decline relative to controls.

Key Concepts

Merit determination (EEOC): The EEOC assigns a merit designation to a sexual harassment charge if the named employer settles with the employee, the claimant withdraws the charge upon receipt of benefits, or the EEOC itself determines after investigation that there is “reasonable cause” to believe harassment occurred. As used in this paper, merit designations capture cases where harassment exceeded the legal threshold of a “hostile or offensive work environment” or produced an adverse employment decision — not all cases involving some level of misconduct.

Selectivity of charges: The fraction of filed EEOC sexual harassment charges that receive a merit designation. In the paper’s framework, higher selectivity (a higher merit rate) signals that workers are filing only more severe cases — i.e., that underreporting of less severe cases has increased. Selectivity is used as an observable proxy for the (unobservable) degree of underreporting.

Reporting threshold (ᾱ): In the paper’s threshold model, the minimum level of harassment severity above which a worker will file an EEOC charge. The threshold is determined by the equality between the expected gains from reporting (probability of success times compensation plus elimination of harassment) and the expected costs (probability of retaliation times the gap between current wage and unemployment value). The threshold rises when outside options weaken — either through lower job-finding probabilities or reduced UI benefits.

Outside options: In this paper, the expected value to a worker of becoming unemployed: a weighted average of the wage at a new job (weighted by job-finding probability) and unemployment benefits (weighted by the probability of not finding a job). Outside options determine the cost a worker bears if retaliatory firing follows an EEOC charge. The paper’s two empirical analyses correspond to two separate shocks to outside options: aggregate labor demand (unemployment rate) and institutional safety net generosity (UI benefits).

Retaliation: Defined by the EEOC as punishment for engaging in a protected activity, such as filing a charge. Retaliation arose in 63.4% of all EEOC sexual harassment charges filed between 2000 and 2015 — more than double the rate for non-harassment charges — and rose from 52% of harassment cases in 2000 to 72% in 2015. In the paper’s model, the probability of a retaliatory firing is denoted θ, and is treated as fixed (not a function of harassment severity for tractability).

Ex-ante moral hazard (UI): The effect of UI benefit generosity on the behavior of currently employed workers, rather than on those already unemployed. In this paper’s context, higher UI generosity reduces the cost of a potential retaliatory firing for currently employed workers, making them more willing to report harassment. The North Carolina UI reform provides evidence of this ex-ante channel: when benefits were cut, the selectivity of harassment charges rose, consistent with workers becoming less willing to risk their jobs.

EEO-1 data: A mandatory annual survey of private establishments in the United States with 100 or more employees, covering approximately 40% of all U.S. employees. Collected by the EEOC, these data report the gender, race, and occupational distribution of workers within each establishment. In this paper, the EEO-1 files are linked to EEOC charge microdata to analyze how the gender composition of co-workers and managers moderates both the incidence of reported harassment and the degree of underreporting.

Summary based on IZA Discussion Paper 14740. AI-assisted, human review pending.