Banning Gendered Job Ads: Kuhn & Shen (2023)

What this is. This is a distilled skeleton of the paper. Read the original (doi:10.1257/aer.20211127) to replicate or extend the analysis.

TL;DR

On March 1, 2019, XMRC.com (a private Chinese job board serving the Xiamen metropolitan area) removed its standardized “preferred gender” field from all job ads overnight, without advance notice to employers or workers. Using internal job-board records spanning a full year around the ban, Kuhn and Shen (2023) estimate the causal effects of this sudden policy change on workers’ application behavior and the gender composition of successful (callback) applicant pools. The ban raised women’s share of callbacks to jobs that had previously requested men by 2.94 percentage points (61 percent), and raised men’s share of callbacks to jobs that had previously requested women by 9.91 percentage points (146 percent). The main mechanism was a large surge in gender-mismatched applications, which employers treated relatively well: workers who applied to jobs of the “wrong” gender received callbacks at 65 to 87 percent of the rate of gender-matched applicants, both before and after the ban. The ban did not increase matching frictions: aggregate application match quality rose slightly and callback rates per application showed no detectable change. The effect was asymmetric: men entered formerly female jobs at a far greater rate than women entered formerly male jobs, which the paper links to gender differences in ambiguity aversion and the greater industry-specificity of the most male-dominated job titles. Integration concentrated in relatively low-wage positions; the most strongly gendered titles (drivers, electricians, nurses, receptionists) were essentially untouched.

Core results

#	Result	Locator	Magnitude as reported
R1	Women’s share of callbacks to M (male-requesting) jobs rose after ban	Table 2 col 4, p. 1027	+2.94 pp (+61%), from base 4.79%
R2	Men’s share of callbacks to F (female-requesting) jobs rose after ban	Table 2 col 4, p. 1027	+9.91 pp (+146%), from base 6.78%
R3	Women’s share of applications to M jobs rose after ban	Table 1 col 4, p. 1026	+4.01 pp (+72%), from base 5.59%
R4	Men’s share of applications to F jobs rose after ban	Table 1 col 4, p. 1026	+13.40 pp (+133%), from base 10.06%
R5	Total daily applications to F jobs increased	Table 4 panel C col 2, p. 1038	+0.0228/day (+12.2%); all new applications gender-mismatched
R6	Total daily applications to M jobs increased	Table 4 panel D col 2, p. 1038	+0.0165/day (+8.5%); all new applications gender-mismatched
R7	Women reduced their applications to F jobs after ban removed female invitation	Table 4 panel C col 3, p. 1038	-0.0160 applications/day (sig.); men did not reduce M-job applications
R8	Mean application match quality rose slightly	Table 5 panel A col 2, p. 1040	+0.0169 SD (significant, 5% level)
R9	Callback rate per application submitted: null result	Table 6 panel A col 2, p. 1041	-0.0028 (SE 0.0026), not significant
R10	Employers’ gender requests largely matched the incumbent gender composition of job titles	Figure 3, p. 1029	The share of ads requesting women or men rose with the corresponding incumbent gender share across job titles
R11	Women entered less historically male M titles than the average M title, while men entered F titles closer to their average incumbent mix	Table 3 panels A-B, p. 1030	M titles: 0.878 all vs 0.677 entered, gap 0.201; F titles: 0.785 all vs 0.735 entered, gap 0.050
R12	Integration differed in the most gendered titles	Figure 4, p. 1031; text p. 1032	In titles >80% male, women’s callback share rose 1.87 pp (p=0.131); in titles >80% female, men’s rose 6.57 pp (p=0.000). None of the 80 most gender-dominated titles appeared among the 40 titles accounting for most ban effects (text p. 1034)
R13	Ban-induced entry reached underrepresented genders at job-title, position, workplace, and firm levels	Table 3 panel C, p. 1030	Incumbent male share for women entrants: 0.677 titles, 0.795 positions, 0.597 workplaces, 0.562 firms; incumbent female share for men entrants: 0.735, 0.856, 0.577, 0.546, respectively
R14	Job titles entered after the ban were lower-wage than all titles in the same request group	Table 3 panel D, p. 1030	M jobs: 8.738 vs 8.621 entered (difference -0.117), compared with 8.858 for N jobs; F jobs: 8.634 vs 8.524 (difference -0.110), compared with 8.858 for N jobs
R15	The ban modestly increased applications to all ads	Table 4 panel A col 2, p. 1038	+0.0058 applications per ad-day (SE 0.0015), about 3.2% of the 0.182 mean
R16	Applications to untreated non-gendered jobs were essentially unchanged	Table 4 panel B col 2, p. 1038	+0.0015 applications per ad-day (SE 0.0017), not significant
R17	Match quality rose most for men applying to F jobs	Table 5 panel C col 4, p. 1040	+0.1064 SD (SE 0.0569), significant at 10%
R18	Gender shares in non-gendered jobs changed little	Tables 1-2 col 4, pp. 1026-1027	Female share: applications +0.53 pp (SE 0.11 pp); callbacks +0.48 pp (SE 0.40 pp, not significant)
R19	Relative callback success by applicant gender did not change in F or M jobs	Table 6 notes, p. 1041	F jobs: p=0.954; M jobs: p=0.860 for tests of changes in women’s relative success
R20	The main gender-mix and application-flow results remained stable under placebo dates and alternative identifying specifications	Text pp. 1028, 1043-1044 (summary of online Appendices 5-11, 18)	Authors describe the findings as highly stable across specification checks; placebo-ban and DiD checks preserve the reported patterns
R21	The ban’s application effects were smaller when gender preferences remained elsewhere in the ad	Text p. 1044 (summary of online Appendix 6)	Effects were 54-60% smaller in ads with embedded requests and 8-9% larger in ads without them
R22	The application increase also came from workers with dormant profiles	Text pp. 1015, 1044-1045 (summary of online Appendix 14)	Effects were highly significant among profiles inactive for at least eight weeks; all additional applications were gender-mismatched
R23	Women’s application response varied with schedule and shift conditions	Text p. 1045 (summary of online Appendix 17)	Long schedules intensified women’s exit from F jobs and attenuated entry into M jobs; multiple or irregular shifts also attenuated entry into M jobs
R24	The gender-share changes appeared quickly and persisted	Text p. 1015	Effects were visible in the first week and persisted for at least six months

Overall (paper’s conclusion). The ban integrated gender-previously-segregated applicant pools and callback pools without measurable harm to application quality or workers’ success rates per application. The integrating effects were broad-based across ads, firms, and job titles, but were concentrated in lower-wage positions and did not penetrate the most gender-stereotyped job titles (drivers, electricians, nurses, receptionists). The ban’s effects were considerably stronger for men than for women, which the paper attributes to gender differences in ambiguity aversion and the greater specificity of skills required for highly male-dominated occupations.

Theory / model

The paper has no formal theoretical model. Building on Kuhn and Shen (2013), the paper lays out the following testable hypotheses and identifies two channels through which a gendered-ad ban could affect labor markets.

Hypotheses. (i) Banning explicit gender requests will change the gender composition of applicant pools to formerly gendered jobs. (ii) The direction and magnitude of the change depend on how employers used gender requests before the ban: if requests reproduced the incumbent workforce gender mix (reinforcing segregation), the ban integrates; if requests were affirmative-action (“lean against the wind”), the ban impedes integration. (iii) The ban may generate additional frictions (harder to find good matches) or may be benign if workers self-select appropriately despite the absence of a gender signal.

Identification. The policy shock is a sharp RD in time. On the night of February 28, 2019, XMRC removed the preconfigured “desired gender” dropdown field from all job ads, effective March 1, 2019, without advance notice. The removal was sudden (employers had not pre-emptively reduced their use of gender requests between 2016 and the ban date), unexpected, and limited to the standardized field (text-embedded gender preferences in job descriptions were not removed). This allows a regression-discontinuity-in-time design: the outcome is compared in the same job ads before and after March 1, 2019. The parallel DiD robustness check uses equivalent weeks in 2018 as controls for 2019 (Delgado Helleseter, Kuhn, and Shen (2020) provides the baseline for the time-series context).

Evidence on the mechanism. Figure 3 (p. 1029) shows that, overwhelmingly, employers on XMRC used gender requests to reinforce the incumbent gender mix of the job title (not for affirmative-action purposes), confirming that the ban had an integrating effect in principle. The asymmetry between men and women (R4 vs R3, R2 vs R1) is consistent with two channels: (a) the female-dominated jobs on XMRC are less industry-specific (“administration and reception” titles appear across all sectors), so men could quickly qualify; (b) women are more deterred than men by ambiguous signals - removing an explicit female invitation reduced women’s own-gender applications (R7), while removing an explicit male invitation did not reduce men’s own-gender applications, consistent with Card, Colella, and Lalive (2021) and gender differences in ambiguity aversion documented in other settings.

Method

The paper applies two regression models, both adapted to the regression- discontinuity-in-time structure.

Equation (1): gender-share outcomes (weekly ad-week cells). The outcome $Y_{jt}$ is the female share of applications or callbacks to job $j$ in week $t$. The estimating equation is (p. 1025):

Y_{jt} = \beta^1 \text{Post}_t \cdot F_j + \beta^2 \text{Post}_t \cdot M_j + \beta^3 \text{Post}_t + \beta^4 F_j + \beta^5 M_j + \beta^6 \mathbf{X}_j + \varepsilon_{jt} \tag{1}

where $F_j$ and $M_j$ indicate that job $j$ had a female (male) gender request when first posted; $\text{Post}_t$ equals one for weeks on or after March 1, 2019; and $\mathbf{X}_j$ is a vector of controls including an intercept. Nongendered (N) jobs in the preban period are the reference category. The treatment effects are $\beta^1$ (ban’s effect on female share in F jobs relative to N jobs) and $\beta^2$ (ban’s effect in M jobs relative to N jobs). A quartic in calendar weeks and a quartic in job age (weeks since posting) control for secular trends and duration dependence within recruiting spells. The most saturated specification adds job-ad fixed effects (column 4 of Tables 1 and 2), absorbing all time-invariant job characteristics. Table 1 is weighted by the number of applications and Table 2 by the number of callbacks; both cluster standard errors by firm ID. The ad-week samples contain 1,428,768 application cells and 214,585 callback cells, respectively.

Equation (2): application arrival rates (daily ad-day cells, 30-day window). For outcomes with non-smooth seasonal trends around the Spring Festival, the paper fits local linear regressions to daily data within a 30-day window on either side of the ban (p. 1037):

Y_{jt} = \alpha + \beta \text{Post}_t + \delta^1 t + \delta^2 t \cdot \text{Post}_t + \theta \mathbf{X}_{jt} + \varepsilon_{jt} \tag{2}

where $t$ indexes days relative to the ban date (March 1, 2019 = day 0), $Y_{jt}$ is the number of applications received by job $j$ on day $t$, $\beta$ is the size of the discontinuity on the first treatment day, and $\delta^1, \delta^2$ allow different linear time trends on either side of the ban. Controls $\mathbf{X}_{jt}$ include day-of-week fixed effects, the number of vacancies specified in the ad, and dummies for the first three days of an ad’s life (to account for application-arrival spikes at posting). Job-ad fixed effects are added in column 2 of Table 4, giving the tightest within-ad estimate of the ban’s daily application effect. Regressions for match quality (Table 5) use the same specification as equation (2) with the normalized match quality as $Y_{jt}$. The callback-per-application regressions (Table 6) replace job-ad fixed effects with applicant fixed effects and define the outcome at the application level (application $i$ ever receives a callback).

Empirical specifications

Tables 1 and 2: gender composition of applicant and callback pools. Equation (1) is estimated on ad-week cells with at least one application (N = 1,428,768 for applications; 214,585 for callbacks). The preferred specification is column 4 (job-ad fixed effects), which implies:

• R3: ban raised female applicant share in M jobs by $\hat{\beta}^2 + \hat{\beta}^3 = 0.0348 + 0.0053 = 4.01$ pp, from a preban base of 5.59% (Table 1, p. 1026).
• R4: ban raised male applicant share in F jobs by $-({\hat{\beta}^1 + \hat{\beta}^3}) = -(-0.1393 + 0.0053) = 0.1340$ (13.40 pp), from 10.06% (Table 1, p. 1026).
• R1: ban raised female callback share in M jobs by $2.46 + 0.48 = 2.94$ pp (61%), from 4.79% (Table 2 col 4, p. 1027).
• R2: ban raised male callback share in F jobs by $10.39 - 0.48 = 9.91$ pp (146%), from 6.78% (Table 2 col 4, p. 1027).

All four estimates are robust across five specifications (columns 1-5 of Tables 1 and 2) including quartic time trends, calendar-week fixed effects, and job-ad fixed effects.

Tables 4-6: application flows, match quality, and callback yield. Equation (2) identifies the ban’s effect on application arrival rates using the 30-day daily window (N = 3,514,552 application-day cells for Table 4 panel A). The ban raised total applications by 3.2 percent in aggregate, concentrated in F and M jobs (R5, R6). All of the new applications to F and M jobs were gender-mismatched (columns 3-4, Table 4): women exclusively drove the increase to M jobs, and men drove the increase to F jobs, while women reduced applications to their own F jobs (R7, coefficient -0.0160/day, significant), consistent with greater female ambiguity aversion when an explicit gender invitation is removed. Match quality rose slightly (R8, Table 5), suggesting the new gender-mismatched applications were not low quality. The aggregate callback rate per application showed no detectable change (R9); across Table 6, only two of sixteen coefficients were statistically significant. These estimates provide no evidence of an overall increase in matching frictions for workers.

Application-level callback specification. Table 5 uses the printed equation (2) with mean match quality in ad-day cells as the dependent variable. Table 6 changes the unit to an application, replaces the left-hand side with the callback indicator, and replaces job-ad fixed effects with applicant fixed effects. Written out from Section V (text p. 1040; not separately numbered in the paper):

$\text{Callback}_{i} = \alpha + \beta \text{Post}_{i} + \delta^1 t_i + \delta^2 (t_i \cdot \text{Post}_{i}) + \theta \text{X}_{i} + \text{ApplicantFE}_{i} + \varepsilon_i$

Table 4 uses active ad-day cells in the 30-day window, with applications sent within 15 days of the ban (3,514,552 observations in the all-ad sample); standard errors cluster by firm. Table 5 uses 439,515 ad-day cells with at least one application and a valid match score, with job-ad fixed effects in columns 2-4 and firm-clustered standard errors. Table 6 uses 638,142 applications and the daily RD controls described above, adds the vacancy count and its missing indicator, and includes applicant fixed effects in columns 2-4; standard errors are clustered by firm. Table 4 has 3,514,552 ad-day observations in the all-ad sample. See Tables 4-6, pp. 1038, 1040-1041.

Datasets used

Dataset	Role in paper	Wiki page
XMRC.com internal job-board records	Primary: 3,133,603 applications by 204,407 workers to 117,390 ads by 15,902 firms over September 2018 to August 2019, including job gender labels, application timestamps, callback indicators, match scores, and worker resume data	no page yet

Sample scope: private-sector vacancies in the Xiamen metropolitan area (Fujian, China), skewed toward skilled workers (mean education 13.3 years, mean requested age 29.8). The mean posted wage was 5,793 RMB/month for M jobs and 4,433 RMB/month for F jobs, reflecting a raw gender wage gap of 23.5 percent in posted wages.

When to read the full paper

• Read if you study gender discrimination in labor markets, effects of equal-opportunity legislation, or job-ad content on application behavior.
• Read Section III (Tables 1 and 2, Figure 1) for the core integration result with gender-share regressions.
• Read Section IV (Table 3, Figures 3 and 4) to understand which job titles and workplaces integrated and which did not.
• Read Section V (Tables 4-6, Figure 5) for the mechanism evidence: application flows, match quality, and callback yield.
• Read the Discussion (Section VII, pp. 1045-1046) for the policy limits: asymmetry, low-wage concentration, and the untouched most-gendered titles.

Attribution and rights

Kuhn, Peter, and Kailing Shen. 2023. “What Happens When Employers Can No Longer Discriminate in Job Ads?” American Economic Review 113(4): 1013-1048. https://doi.org/10.1257/aer.20211127

Replication data: Kuhn and Shen (2023), openICPSR, https://doi.org/10.3886/E183021V1.

Paywalled; all rights reserved by the American Economic Association. Extract-only. This page is an LLM-distilled summary (paper-distiller, claude-sonnet-4-6, 2026-06-25); it is not human-verified and the results have not been reproduced.