J15 | Macro Paper Warehouse

Civil War–Induced Displacement and Human Capital

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

This paper examines the impact of conflict-driven forced displacement on human capital accumulation using the Mozambican civil war (1977–1992) as the empirical setting. During this war, over four million civilians — roughly a third of the population — fled to rural areas, cities, neighboring countries, or UN-managed refugee camps. The study advances on prior work in three dimensions: it uses the full post-war population census (12 million individuals) rather than a small survey; it studies multiple displacement trajectories in a single framework; and it separately identifies place-based exposure effects from a general uprootedness effect.

The primary data source is the 1997 Mozambican census, which records each individual’s place of birth, residence in 1992 (the war’s end), and residence in 1997. Key outcomes are educational attainment and sectoral employment (agricultural versus services). The authors supplement the census with digitized colonial road and school maps, georeferenced conflict events, and landmine contamination data.

The main identification strategy compares approximately 135,000 siblings (from 45,000 families) separated during the war, using the sibling who stayed behind as a within-family counterfactual. This design controls for household-level characteristics including religious and ethnic background, aspirations, and exposure to violence.

The key findings are as follows. First, rural-born IDPs displaced to cities have a 7.3 percentage point higher likelihood of attending primary school and 0.53 more years of schooling compared to their siblings who stayed behind — roughly one-third of the non-displaced mean. Rural-born IDPs displaced to other rural areas also show gains, with a 3 percentage point higher likelihood of attending school and 0.24 additional years, supporting the uprootedness hypothesis even for displacements that did not reach urban centers. Urban-born IDPs forcibly relocated to the countryside — primarily through FRELIMO’s villagization scheme — experienced 9 percentage point lower primary school attendance and approximately 0.5 fewer years of schooling relative to siblings who remained in cities.

External displacement (to camps in Malawi or Zimbabwe) generated no significant schooling gains relative to staying siblings, despite UN-built schools in camps, likely because scarce employment opportunities reduced perceived returns to education.

Second, the paper jointly estimates place-based and uprootedness effects in a single within-family framework. Place effects are statistically significant: displacement to a district one standard deviation more developed than one’s birthplace raises schooling likelihood by approximately 3 percentage points (OLS) to 5 percentage points (2SLS reduced form). Crucially, a residual uprootedness effect of approximately 2–4 percentage points persists even after controlling fully for destination-origin differences in development and conflict intensity. This uprootedness effect is quantitatively comparable to being displaced to a district one standard deviation more developed than one’s birthplace.

Third, a primary survey of 208 Nampula residents conducted in early 2020 — three decades after the war — confirms lasting educational gains. IDPs displaced to Nampula have a 10 percentage point higher likelihood of completing primary school relative to their siblings who stayed in the countryside, and their educational attainment converged to levels of urban-born, never-displaced residents despite large urban-rural education gaps. However, IDPs report significantly lower social capital, civic participation, and community trust than urban-born respondents, and score significantly worse on mental health indicators, including depression, loneliness, and pessimism. These psychosocial costs persist three decades after the war’s end.

The findings apply to a low-income, post-colonial African setting characterized by widespread illiteracy (over 60%) and subsistence agriculture (over 85% of employment) at the war’s close. The results are robust to alternative age restrictions, extended family comparisons, dropping the oldest sibling, same-sex sibling pairs, and narrowing the age gap between sibling pairs to as few as two years.

Q: What is the core identification strategy and why is it preferred over cross-sectional estimates? A: The authors compare siblings within the same household who experienced different displacement trajectories during the war. Because siblings share household-level characteristics — parental preferences for education, ethnic and religious background, wealth, and local conflict exposure — the within-family design controls for confounders that would bias cross-sectional estimates. The within-family estimates are systematically smaller than cross-sectional ones (e.g., 7.3 pps vs. 24–30 pps for rural-to-urban displacement in primary school attendance), confirming that sorting was present even in the unpredictable civil war setting.

Q: What do the results show for rural-born IDPs displaced to urban centers? A: Within the sibling-pair framework, rural-born IDPs displaced to cities and towns have a 7.3 percentage point higher likelihood of attending primary school and 0.53 more years of schooling compared to their siblings who stayed in rural birthplaces, against a non-displaced sibling mean of approximately 20% primary school access and one year of formal schooling. These IDPs also show a 4 percentage point higher likelihood of non-agricultural employment five years after the war’s end.

Q: What do the results show for rural-born IDPs displaced to other rural areas? A: Even displacement to a different rural district — not a city — generates modest but statistically significant gains: a 3 percentage point higher likelihood of attending school and 0.24 additional years of schooling relative to siblings staying in their birthplace rural district. The authors interpret this as evidence for the uprootedness hypothesis, since rural Mozambique at the time was among the most impoverished and insecure environments in the world, meaning destination quality alone cannot explain the gain.

Q: What do the results show for externally displaced refugees? A: Refugees displaced to camps and settlements in Malawi, Zimbabwe, Tanzania, Zambia, and Swaziland show schooling levels statistically similar to their siblings who remained in their rural birthplaces, despite UN-built primary schools in camps. The authors attribute the absence of gains to low perceived returns to education stemming from scarce employment opportunities at displacement destinations. Externally displaced individuals do show a 5 percentage point lower likelihood of agricultural employment relative to staying siblings.

Q: What are the consequences of urban-to-rural forced displacement? A: Urban-born individuals forcibly relocated to the countryside — primarily through FRELIMO’s villagization and food production programs — have approximately 9 percentage point lower likelihood of attending primary school and 0.5 fewer years of schooling compared to siblings who remained in urban areas. These results indicate that FRELIMO’s coercive relocation policies imposed material human capital costs on the displaced.

Q: How are place-based and uprootedness effects separated empirically? A: The authors construct principal component indices for destination-origin differences in regional development (aggregating population density, Portuguese-speaking share, offspring mortality, road density, colonial market density, and school density) and conflict intensity (conflict events per capita and landmine contamination per capita). They then include these continuous exposure measures alongside a binary displacement indicator in within-family regressions. The coefficient on the binary displacement indicator — conditional on destination-origin development and conflict differences — isolates the uprootedness effect for individuals displaced to districts with identical characteristics to their birthplace.

Q: What are the magnitudes of the place-based and uprootedness effects? A: Under OLS, displacement to a district one standard deviation more developed than one’s birthplace raises schooling likelihood by approximately 3 percentage points. The residual uprootedness effect — displacement per se, controlling for destination quality — raises schooling likelihood by approximately 2 percentage points. Under 2SLS (instrumenting destination-origin development differences with the development of districts within 100 km of birthplace), the place-based effect rises to approximately 5 percentage points in the reduced form, and the uprootedness effect remains significant at approximately 4 percentage points. Both the uprootedness and place-based effects are of comparable magnitude.

Q: What instrument is used in the 2SLS specifications and what is its first-stage strength? A: The instrument exploits the fact that Mozambique’s heavily mined and rudimentary transportation network constrained civilian movement — the median displaced sibling ended up roughly 97 kilometers from birthplace. The authors instrument actual destination-origin development and conflict differences with the predicted differences based on the characteristics of districts within 100 km of the birthplace. The first-stage elasticity between actual and proximity-predicted differences in development is 0.86, and for conflict is 0.88, both precisely estimated.

Q: What do the long-run survey results from Nampula show about educational persistence? A: In a 2020 survey of 208 Nampula residents aged over 35, IDPs who fled to Nampula during the war have a 10 percentage point higher likelihood of completing primary school relative to their siblings who stayed in the countryside. Their educational attainment converges to the level of urban-born, never-displaced Nampula residents, despite large historical and contemporary urban-rural education gaps in northern Mozambique. The majority of IDPs (73%) report that extended relatives or friends advised them to attend school upon arriving in the city, and most believed education was necessary for urban employment.

Q: What are the long-run psychosocial costs documented in the Nampula survey? A: Even three decades after the war’s end, IDPs in Nampula report significantly lower social capital, civic participation, and community trust compared to urban-born never-displaced residents. IDPs also score significantly worse on mental health indicators including depression, loneliness, and pessimism. These findings suggest that forced displacement imposes persistent psychosocial costs that are not remediated by economic or educational convergence.

Q: What drives displacement in the data, and does selection threaten identification? A: Linear probability and multinomial logit models show that conflict intensity and geographic proximity (distance to the border for external displacement; distance to cities for urban displacement) are the primary correlates of displacement type, while differences in destination development are uncorrelated with displacement. Nevertheless, the overall explanatory power of these models is low, confirming many idiosyncratic and unpredictable features of the war. The within-family design addresses residual selection on household characteristics, and the 2SLS design addresses selection on destination-specific characteristics.

Q: How do educational gains translate into sectoral employment outcomes? A: Across specifications, gains in schooling move in tandem with a shift out of agriculture into services. Rural-to-urban IDPs have a 4 percentage point higher likelihood of non-agricultural employment five years after the war, while externally displaced show a 5 percentage point lower likelihood of agricultural employment. Urban-born IDPs displaced to the countryside are more likely to work in agriculture after the war. The authors interpret this co-movement as suggesting that conflict-driven human capital accumulation may contribute to structural transformation away from subsistence agriculture.

Q: How robust are the within-family estimates? A: The authors conduct six sensitivity checks: adding family fixed effects to cross-sectional regressions, restricting to individuals aged 12–18 in 1997 to address co-habitation concerns, extending comparisons to cousins and other relatives, dropping the oldest male sibling to minimize favoritism concerns, restricting to same-sex sibling pairs, and narrowing the age gap to two years. Across all permutations, the qualitative ordering is preserved: refugees show no significant schooling gains, rural-to-urban IDPs show gains of 5–6 percentage points in primary attendance and 0.35–0.5 extra years, rural-to-rural IDPs show small positive gains, and urban-to-rural IDPs show losses.

Uprootedness hypothesis: The idea, traced in the paper to Stigler and Becker (1977) and earlier scholars, that forced displacement incentivizes human capital investment precisely because education is a mobile asset that cannot be expropriated — distinct from place-based effects of destination quality.

Place-based (exposure) effects: The impact on human capital outcomes attributable to differences between the development level and conflict intensity of the displacement destination and the individual’s birthplace, measured as destination-origin differences in a principal component index of regional development.

Separated siblings design: An identification strategy that compares siblings from the same household who experienced different displacement trajectories during the war, holding constant all household-level characteristics including parental preferences, ethnicity, religion, wealth, and local conflict exposure.

Internal displacement (IDP): Conflict-driven movement within national borders to either rural areas or urban centers, constituting approximately 60% of global forced displacement and the majority of displacement in the Mozambican civil war context.

Source text origin: A categorization of the working paper text used for summarization — distinguishing full PDF or HTML text from abstract-only text. Abstract-only text is a hard block for summary generation in the pipeline.

Structural transformation: In this paper’s usage, the shift of workers out of subsistence agriculture into services associated with human capital accumulation triggered by conflict-driven displacement, treated as a potential mechanism of post-conflict recovery.

Psychosocial costs of displacement: Long-run deficits in social capital, civic engagement, community trust, and mental health (depression, loneliness, pessimism) reported by IDPs three decades after displacement, persisting despite convergence in educational attainment and employment.

Community Engagement and Public Safety: Evidence from Crime Enforcement Targeting Immigrants

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

This paper studies how immigration enforcement affects public safety, asking two questions: (1) what is the effect of increased enforcement on criminal victimization, and (2) how does increased enforcement affect victims’ willingness to report crimes to police? The authors exploit the staggered rollout of the U.S. Secure Communities (SC) program — the largest expansion of interior immigration enforcement in U.S. history — across counties between 2008 and 2013. SC expanded information sharing between local police and federal immigration authorities, causing ICE honored detainer requests to increase by over 50% following program activation.

The primary data source is the restricted-access National Crime Victimization Survey (NCVS), which measures victimizations independently of whether they were reported to police and includes respondent ethnicity. This allows the authors to separately estimate effects on underlying crime incidence and on reporting behavior for Hispanic and non-Hispanic individuals. The empirical strategy uses a staggered difference-in-differences design following Sun and Abraham (2021), comparing earlier-treated counties to the last 25% of counties to activate SC, with estimates run separately by ethnicity.

The main findings run contrary to the stated policy goal of improving public safety. Among Hispanic individuals, SC caused a statistically significant 0.15 percentage point increase in monthly victimization — a 16% increase relative to the pre-period baseline of 0.9 percentage points — implying approximately 1.3 million additional crimes against Hispanics in the two years following program activation. The increase is concentrated primarily in property crimes (a statistically significant 15% increase), with a similarly sized but imprecisely estimated 15% increase in violent crime victimizations. The victimization increase is larger for Hispanic females (0.23 percentage points, or 25%) and in counties with higher shares of non-citizen Hispanic residents.

Simultaneously, SC caused a 9.5 percentage point decline in the likelihood that Hispanic victims report incidents to police — a 30% decline relative to the pre-period mean reporting rate of 33 percentage points. This reporting decline is primarily driven by a 34% decline in the reporting of property offenses. No changes in victimization or reporting are found for non-Hispanic individuals in the aggregate, though non-Hispanic individuals in neighborhoods with high Hispanic population shares do experience higher victimization rates after SC.

Critically, reported crime rates (the product of victimization and reporting) are unchanged for both Hispanic and non-Hispanic individuals, explaining why prior studies using administrative reported-crime data found null effects of SC. The null effect on reported crime masks two large, opposing causal forces.

The authors provide evidence that the decline in crime reporting is the primary driver of the increase in victimization. Cohorts with larger reporting declines experienced larger victimization increases, and a decomposition exercise shows the reporting decline is substantially more important than concurrent SC-induced changes in unemployment, wages, female-headed household shares, and the male immigrant share. Supporting data from 75 police departments confirm no change in 911 call volumes or total arrest volumes, while showing a decline in the Hispanic share of arrestees in both Hispanic and non-Hispanic neighborhoods — consistent with reduced reporting leading to reduced apprehension of offenders, with offending shifting toward non-Hispanic individuals.

Scope conditions: results are estimated for the population residing in counties exceeding 100,000 residents (representing 61% of total U.S. population and 69% of the Hispanic population), excluding southern border counties and states that actively resisted SC implementation (Illinois, Massachusetts, New York). Effects apply to all Hispanic respondents — citizens and non-citizens — consistent with prior evidence that citizen Hispanics respond to immigration enforcement out of concern for non-citizen contacts.

Q: What was the Secure Communities program and how was it implemented? A: SC was a federal program launched in 2008 that required fingerprints of individuals booked into local jails to be forwarded not only to the FBI but also to the Department of Homeland Security, enabling automatic screening for immigration violations. Local authorities could not prevent federal officials from learning of an arrestee’s immigration status. The program rolled out county-by-county between October 2008 and January 2013 due to technological constraints and resource bottlenecks, generating the staggered variation used for identification.

Q: How large was the first-stage effect on actual immigration enforcement? A: County-level honored ICE detainer requests increased by over 50% following SC activation, with a similar 40% increase in all detainer requests. The number of honored detainers nationwide doubled between 2008 and 2012. Over 90% of detainers and removals in any given month were for individuals of Hispanic ethnicity.

Q: What is the main finding on Hispanic victimization? A: SC caused a 0.15 percentage point increase in monthly Hispanic victimization rates, a 16% increase relative to the pre-period baseline of 0.9 percentage points. This translates to approximately 1.3 million additional crimes against Hispanics over two years following program activation, calculated by multiplying the monthly effect by 24 months and the 35.3 million Hispanics in the sample counties.

Q: What is the main finding on Hispanic crime reporting? A: SC caused a 9.5 percentage point decline in the likelihood that Hispanic victims report incidents to police, a 30% decline relative to the pre-period mean reporting rate of 33 percentage points. This decline occurred relatively quickly after activation and was concentrated in property offenses, where reporting fell by 34%.

Q: Why do reported crime rates show no change despite large shifts in victimization and reporting? A: Reported crime rates — the probability of being victimized and reporting the crime — are unchanged because the 16% increase in victimization and the 30% decline in reporting are approximately offsetting in magnitude. This explains why prior work using administrative police data (Miles and Cox 2014; Treyger et al. 2014; Hines and Peri 2019) found null effects of SC on reported crime: those data sources cannot separately identify the two underlying changes.

Q: Does SC affect non-Hispanic individuals? A: In the aggregate, SC has no statistically significant effect on non-Hispanic victimization or reporting. However, non-Hispanic individuals living in neighborhoods with high Hispanic population shares do experience victimization increases, and in those neighborhoods their reporting rates also decline slightly. Re-weighting non-Hispanic respondents to match the county composition of Hispanic respondents yields an 8% increase in non-Hispanic victimization, suggesting spillover effects in Hispanic-dense areas.

Q: What mechanism links the reporting decline to the victimization increase? A: The authors argue that reduced victim reporting lowers the probability that offenders are apprehended, thereby reducing the cost of committing crimes. They demonstrate this through two analyses: first, cohorts of counties with larger reporting declines experienced larger victimization increases; second, a decomposition shows the reporting channel is substantially more important than concurrent SC-induced changes in unemployment, wages, female-headed household shares, and the male immigrant share of the population.

Q: What do the police administrative data show about offender composition? A: Data from 75 police departments show no change in 911 call volumes or total arrest volumes following SC — consistent with the NCVS finding of unchanged reported crime rates. However, the Hispanic share of arrestees declined after SC, with a 1.5 percentage point drop in Hispanic neighborhoods (off a base of 54%), suggesting the rise in offending was more concentrated among non-Hispanic offenders as reduced reporting lowered expected punishment probabilities.

Q: How does the victimization effect vary by gender? A: The victimization point estimate for Hispanic males is 0.085 percentage points and imprecisely estimated (SE = 0.088). For Hispanic females, the effect is over 2.5 times larger at 0.23 percentage points, a 25% increase. The decline in reporting is comparable in magnitude across male and female Hispanic victims, suggesting fear of enforcement is similar by gender but that females disproportionately bear the crime burden.

Q: How does the victimization effect vary by neighborhood non-citizen Hispanic share? A: Victimization effects for Hispanics are relatively constant across neighborhood types but are higher — around 25% — in neighborhoods with the highest shares of non-citizen Hispanics. Counties with higher non-citizen Hispanic shares also exhibit higher ICE removal rates, indicating greater total enforcement, and these counties have higher victimization effects. Reporting declines among Hispanics appear relatively uniform across neighborhood types.

Q: Could survey attrition or compositional changes explain the results? A: The authors rule this out through several tests. First, SC has no statistically significant effect on household survey response rates, even in Census tracts above the 90th percentile of Hispanic share. A worst-case bias calculation implies attrition could account for at most 26% of the victimization effect. Second, re-estimating using predicted victimization (based on pre-SC demographics) yields precise null effects, indicating the increase is not driven by compositional change. Third, results are stable when restricting to respondents present at all survey waves or using individual fixed effects.

Q: Could the reporting decline be mechanical — reflecting a change in the types of crimes committed rather than behavioral change? A: The authors test this by constructing predicted reporting rates using pre-SC incident characteristics. The largest alternative estimate is -1.45 percentage points, over six times smaller than the estimated main reporting effect of 9.5 percentage points, ruling out crime composition change as the primary explanation. Results also hold when focusing on always-respondents and using individual fixed effects, ruling out entry of low-reporting individuals into the survey.

Q: How robust are the results to alternative empirical strategies? A: Results are robust to including states that resisted SC (with somewhat smaller magnitudes as expected), alternative population cutoffs, TWFE specifications, the Borusyak et al. (2021) and Callaway and Sant’Anna (2021) estimators (which yield larger point estimates), a triple-differences specification using non-Hispanics as an additional control group, and the inclusion of time-varying unemployment rates. The dynamic event-study plots show parallel pre-trends across all specifications.

Q: What are the policy implications of the null effect on aggregate victimization? A: The authors estimate that the policy ruled out declines in aggregate victimization larger than 3.3%, indicating SC did not generate meaningful improvements in aggregate public safety. This contradicts the stated mission of immigration enforcement agencies. The findings imply that policies targeting immigrant communities can generate public safety costs through trust erosion that outweigh any deterrence or incapacitation benefits.

Secure Communities (SC): A federal program launched in 2008 requiring automatic sharing of fingerprints from local jail bookings with the Department of Homeland Security, enabling identification of unauthorized immigrants among local arrestees and triggering ICE detainer requests; the largest expansion of interior immigration enforcement in U.S. history.

Chilling effect: The mechanism by which immigration enforcement raises the perceived cost of contacting law enforcement for immigrant victims and witnesses — through fear that they, a family member, or neighbor will be detained or deported — thereby reducing willingness to report crimes independently of any change in underlying criminality.

Victimization rate: The likelihood that an individual is the victim of a crime in a given period, measured via the NCVS independently of whether the crime was reported to police; the paper’s primary measure of public safety.

Reporting rate: The likelihood that a criminal victimization is reported by the victim to the police, measured as a share of all crime incidents; distinct from victimization rate and central to the paper’s decomposition of reported crime into its two components.

Reported crime rate: The joint probability of being victimized and reporting the crime, analogous to measures available in administrative police data such as the FBI UCR; this outcome masks the opposing effects of SC on victimization and reporting.

Honored detainer: An ICE detainer request that results in a transfer of the arrested individual to ICE custody; the paper’s preferred measure of immigration enforcement intensity because it is available both before and after SC activation and is more directly linked to deportation actions than all detainer requests.

Decomposition of victimization increase: The paper’s procedure for quantifying the relative importance of the reporting-channel (reduced probability of apprehension) versus other SC-induced social and economic changes (unemployment, wages, female-headed households, male immigrant share) in explaining the rise in Hispanic victimization.

Leveraging Virtual Contact and Social Networks to Foster Interethnic Harmony

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

This paper investigates whether virtual contact — exposure to an outgroup through a documentary film — can promote interethnic harmony, and whether targeting network-central individuals amplifies effects on untreated community members. The study addresses a context of deep, historically rooted discrimination: the Santal ethnic minority in northwestern Bangladesh have faced colonial-era land dispossession, ongoing violence, labor market discrimination, and structural exclusion by the Bengali ethnic majority. The Santals are the second-largest ethnic-minority group in Bangladesh; in the study villages, their share ranges from 13% to 83% of the population.

The authors conducted a cluster-randomized field experiment across 121 multiethnic villages in the Rajshahi and Naogaon districts of Bangladesh, involving over 3,300 households. Villages were randomly assigned to three arms: a random treatment arm (RR, 40 villages, N=562 Bengalis) in which approximately 14 randomly selected ethnic-majority households per village watched a 45-minute documentary film (“Ami Santal” / “I Am Santal”) portraying Santal culture, economic hardships, and aspirations; a central treatment arm (41 villages) in which approximately 7 randomly selected Bengalis (RC) and 7 network-central Bengalis identified via a diffusion-centrality nomination exercise (CC) watched the same film; and a control arm (40 villages) in which households watched a placebo documentary on flower farming. The documentary, costing approximately $13 per participant, was screened individually at participants’ homes on tablets. Data were collected at baseline (September–October 2022), first end line approximately 3 months post-screening (February–March 2023), and a casual-work field experiment second end line approximately 4.5–5 months post-screening (April–May 2023). Outcomes were measured via lab-in-the-field experiments (dictator game, solidarity game), an experimentally validated interethnic trust survey item (Falk et al. 2018), self-reported behaviors, administrative police complaint data, and facial emotion detection during screening.

The main findings are as follows. First, treated Bengalis in the central arm (RC) gave 14.7% more in the dictator game (p < .01) and exhibited 21.7% greater trust toward Santals (p < .01) compared to controls; RR participants showed a 7.1% increase in solidarity game giving (p < .10) and 11.8% greater trust (p < .01). Effects on reducing negative stereotypes and discriminatory opinions were not statistically significant, suggesting that affective components of prejudice are more responsive to the intervention than cognitive components. About 82% of treated Bengalis reported acquiring new information about Santals, primarily regarding occupational struggles, educational aspirations, and economic potential. Facial expression analysis using emotion-detection software found sadness to be significantly more prevalent among viewers (p < .05), particularly among network-central participants, consistent with an empathetic response.

Second, untreated Bengalis in the central arm — who never watched the documentary — showed 20.9% higher altruism (p < .10), 27.3% higher solidarity (p < .05), and 8.1% higher trust (p < .05) toward Santals relative to controls. No significant effects on untreated Bengalis were found in the random arm. Untreated Santals in both arms exhibited greater trust toward Bengalis (11% increase in random arm, p < .05; 21.7% increase in central arm, p < .01) and higher subjective well-being (p < .01 in both arms). Village-level administrative data show a significant reduction in Bengali police complaints against Santals post-intervention (p < .05), but only in the central arm.

Third, in the casual-work field experiment, multiethnic pairs jointly produced paper bags under piece-rate compensation. Overall productivity increased approximately 5% (p < .05) in the central arm only. Both Bengali and Santal workers increased productivity specifically in the finisher role — the most critical role for determining earnings — in the central arm. The authors interpret Bengali productivity gains as reflecting increased prosociality toward Santal co-workers, and Santal productivity gains as reflecting conformism or peer pressure in response to Bengali effort. The scope of all effects is limited to multiethnic villages in northwestern Bangladesh, a context of historically severe and ongoing majority-minority inequality; the intervention deliberately did not challenge the socioeconomic hierarchy of the villages.

Q: What was the documentary film’s content and design rationale? A: The 45-minute film “Ami Santal” featured three narrative layers: Santal culture (rituals, cuisine, the Baha festival), economic hardships (housing, water access, low incomes, labor market struggles, educational barriers), and aspirational stories of Santals who achieved success. All stories were narrated by non-actor local Santals, filmed outside the study region, and deliberately avoided attributing blame to Bengalis. The film was designed under the supervision of anthropologists at the University of Rajshahi to maintain ethnographic authenticity and a non-moralistic, observational tone (moral judgment language was much lower than in comparison Bangladeshi documentaries and general films, per LIWC-22 analysis).

Q: How were network-central individuals identified and why might targeting them matter? A: In central-arm villages, enumerators surveyed approximately 18–20 randomly selected passers-by at village markets and asked them to nominate the 15 people most effective at disseminating information. The seven most consistently and highly ranked individuals per village were selected as network-central (CC). These individuals were expected to have high diffusion centrality — meaning information they receive spreads widely — so targeting them with the documentary could shift attitudes and behavior among untreated community members through persuasion, visibility, credibility, or diffusion (the paper cannot separately identify which mechanism operates).

Q: What were the primary behavioral effects on treated Bengalis (the ethnic majority who watched the film)? A: Randomly selected participants in the central arm (RC) gave 14.7% more in the dictator game (p < .01) and 8% more in the solidarity game (not statistically significant), and exhibited 21.7% greater trust toward Santals (p < .01), all relative to controls. In the random arm (RR), participants showed a 6.4% increase in dictator game giving (not statistically significant), a 7.1% increase in solidarity game giving (p < .10), and 11.8% greater trust toward Santals (p < .01). Effects on self-reported behaviors — interethnic friendships, social interactions, amount charged to minorities for water — were not statistically significant.

Q: Did the intervention change Bengali stereotypes or discriminatory opinions toward Santals? A: No. Despite treated Bengalis acquiring substantial new information (approximately 82% reported learning new things, primarily about Santal occupational struggles and educational aspirations), the authors find no significant effects on the stereotypes index or the discriminatory-opinions index among treated Bengalis. They propose two explanations: cognitive components of prejudice (stereotypes) are harder to change through indirect contact than affective components (emotions, prosocial behavior), consistent with Tropp and Pettigrew (2005) and Turner, Crisp, and Lambert (2007); and a single documentary may be insufficient to counter deeply ingrained generational biases due to resistance to change.

Q: What emotional responses did the documentary elicit, and how was this measured? A: Field assistants took candid photographs of participants’ faces at a random point during the screening; these were analyzed using Emotimeter software (machine learning-based emotion detection) that assigns scores across seven emotion categories summing to 100%. Sadness was significantly more prevalent among documentary viewers compared to placebo viewers (p < .05), particularly among network-central participants (CC). The authors interpret this as consistent with an empathetic response to the film’s content about Santal hardships, and connect it to increased prosocial behavior via emotion-regulation mechanisms (alleviating sadness through prosocial action).

Q: What were the spillover effects on untreated Bengalis in the central arm? A: Untreated Bengalis in central-arm villages — who never watched the documentary — showed 20.9% higher altruism (p < .10), 27.3% higher solidarity (p < .05), and 8.1% higher trust toward Santals (p < .05) relative to controls. By contrast, untreated Bengalis in random-arm villages showed no statistically significant effects on any of these outcomes. The authors attribute the central-arm spillovers to the presence of network-central individuals being treated in those villages, though whether these patterns reflect persuasion, visibility, credibility, or information diffusion cannot be separately identified.

Q: How did the intervention affect the Santal ethnic minority (who never watched the documentary)? A: Untreated Santals in both arms exhibited greater trust toward Bengalis: an 11% increase in the random arm (p < .05) and a 21.7% increase in the central arm (p < .01) compared to controls. Santals in both arms also reported higher subjective well-being (p < .01). A weakly significant increase in food security was observed among Santals in the central arm (p < .10), possibly reflecting increased material support from Bengalis. No statistically significant effects were found on Santal altruism or solidarity.

Q: What did the village-level administrative complaint data show? A: Using data collected from two police stations covering all 121 villages, the authors find a significant reduction in Bengali complaints against Santals post-intervention in the central arm (p < .05). No significant reduction was found in Santals’ complaints against Bengalis (p > .10) in any arm. Data from village counselors’ offices (shalish arbitration complaints) showed no significant change in any arm. The distinction matters because police complaints involve more serious, violent matters, while village-counselor complaints involve routine arbitration.

Q: How was the casual-work field experiment designed, and what did it find? A: Approximately 4.5 months after the documentary screenings, 720 participants (360 Bengalis, 360 Santals) drawn equally from the three study arms were paired into multiethnic dyads to jointly produce paper bags for a local supplier under piece-rate compensation, with earnings split equally. One worker was randomly assigned the preparer role and the other the finisher role; roles were switched halfway through the three-hour session. The paper finds an approximately 5% overall productivity increase (p < .05) in the central arm only, concentrated in the finisher role (the role most critical for final output). Bengalis and Santals both increased productivity specifically as finishers in the central arm.

Q: What mechanisms explain the productivity effects in the casual-work experiment? A: For Bengali finishers, the productivity gain is interpreted as prosocial behavior: treated Bengalis who showed greater altruism toward Santals worked harder to increase the earnings of their Santal co-workers. For Santal finishers, the productivity gain is interpreted as conformism or peer pressure: Santals increased effort more when they worked as finisher after swapping roles (i.e., after observing Bengalis’ higher effort as finisher first), suggesting responsiveness to the higher productivity of Bengalis rather than an independent prosocial motivation. The authors present a simple theoretical model to formalize these interpretations, citing Rotemberg (1994) on prosocial effort and Kandel and Lazear (1992) and Mas and Moretti (2009) on peer pressure mechanisms.

Q: Why was virtual rather than direct contact used in this intervention? A: The authors argue that encouraging direct contact between Bengalis and Santals in this setting carries specific risks: the unequal status of the groups may generate anxiety during interactions, potentially limiting engagement or provoking backlash. By contrast, the documentary provides an indirect, low-cost ($13 per participant) form of contact that presents Santal lives without disrupting the socioeconomic hierarchy of the villages and without attributing blame to Bengalis. The film’s entertaining veneer and emotional storytelling make it more scalable and logistically feasible in contexts where direct contact is socially difficult or impractical.

Q: What are the primary limitations acknowledged by the authors? A: The authors acknowledge that the study’s sampling protocol relied on a door-to-door skip procedure without systematic records of approached households, raising the possibility of convenience or snowball-type recruitment and potential deviations from random sampling — this is reflected in some imbalances in baseline characteristics across arms. CC-control comparisons are explicitly descriptive (not causal) because network-central individuals were selected on centrality. Differential attrition was found among untreated Santals (both treatment arms had significantly lower attrition than control, p < .05), which could bias estimates for that subgroup. The authors cannot separately identify the mechanisms (persuasion, visibility, credibility, diffusion) underlying spillover effects in central villages.

Q: What are the policy implications of this study? A: The findings suggest that media-based virtual contact interventions are a low-cost, scalable tool for improving interethnic prosociality even in contexts of deep-rooted discrimination where direct contact may be socially impractical. Targeting network-central individuals — identified via a simple nomination exercise requiring no pre-existing network data — amplifies village-wide effects, including among untreated community members and the minority group itself. The productivity gains in multiethnic work teams imply that improved interethnic relations can have tangible economic consequences beyond attitudinal change. However, the null effects on stereotypes and discriminatory opinions suggest that single documentary interventions may not be sufficient to alter deep-seated cognitive biases, and more intensive or repeated interventions may be needed to achieve durable attitude change.

Virtual contact: Indirect exposure to an ethnic outgroup through a documentary film, as distinct from direct intergroup contact; posited to influence majority-group attitudes and behavior by increasing empathy and identification with the outgroup without requiring face-to-face interaction.

Diffusion centrality: A network measure of how effectively an individual can spread information through a community, operationalized via a nomination exercise in which community members identify those best positioned to disseminate information; used to select the seven highest-ranked individuals per village for targeted treatment.

Prosociality (altruism and solidarity): Measured using incentivized lab-in-the-field games — the dictator game (unilateral allocation of an endowment to a passive outgroup recipient) and the solidarity game (precommitted transfers to an outgroup member who may incur a random loss) — capturing willingness to benefit non-coethnic others at personal cost.

Affective versus cognitive components of prejudice: A distinction between emotional aspects of prejudice (feelings, empathy) — which the authors find to be more responsive to the documentary intervention — and cognitive aspects (negative stereotypes, discriminatory opinions) — which show no significant change despite new information acquisition.

Spillover effects (untreated individuals): Changes in behavior or attitudes among community members who did not directly receive the intervention (did not watch the documentary), attributed to the influence of treated individuals in their village, particularly network-central individuals in the central arm.

Piece-rate casual-work field experiment: A second end line in which multiethnic pairs of Bengali and Santal workers jointly produced paper bags for a local supplier, with individual earnings determined by joint piece-rate output; designed to measure whether improved interethnic attitudes translated into higher workplace productivity in ethnically mixed teams.

Source text origin: The provenance classification of the text used to generate a paper summary (full PDF, open-access HTML, or abstract only); the paper’s pipeline rules impose a hard block on abstract-only summarization.

Marriage, Fertility, and Cultural Integration in Italy

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

Bisin and Tura study the cultural integration of immigrants in Italy by estimating a structural model of marital matching embedded with intra-household decisions — fertility, socialization of children, and divorce — along cultural-ethnic lines. The central research question is how to decompose the demand for integration (from immigrants) and the supply of cultural acceptance (from natives) in explaining the pace and heterogeneity of cultural convergence.

The empirical analysis exploits administrative individual-level data from ISTAT’s ADELE Laboratory covering the universe of marriages formed in Italy from 1995 to 2012 and the universe of births and separations over the same period. After matching marriage, birth, and separation records, the final sample comprises more than 4 million marriages, representing 92.6% of all marriages celebrated in Italy over the period. Seven cultural-ethnic groups are studied: Italian (majority), Europe-EU15, Other Europe, North Africa–Middle East, Sub-Saharan Africa, East Asia, and Latin America. The model is a transferable-utility (TU) frictionless marriage market in which the joint marital surplus depends on a systematic component — itself the outcome of a collective household decision problem — and an idiosyncratic component capturing unobserved individual heterogeneity (following Choo and Siow, 2006). Parameters are estimated via method of moments, with identification drawing on cross-sectional variation across ethnic-group pairings and across Italy’s 20 administrative regions. Cultural socialization is proxied by language transmission (whether Italian is spoken at home with children).

The data confirm strong positive assortative mating along cultural-ethnic lines, with particularly high homogamy rates for Sub-Saharan African and East Asian minorities. Homogamous minority households show notably lower rates of Italian-language use at home — for East Asian parents, 20% in a homogamous marriage versus 92% in a heterogamous marriage. Heterogamous marriages have higher separation rates (7.5% for mixed families with at least one Italian spouse versus 6.4% for homogamous Italian couples) and lower fertility.

The estimated cultural intolerance parameters — measuring the psychological value a parent places on socializing a child to his/her own ethnic identity relative to a child acquiring a different identity — are strictly positive, asymmetric across directions, and highly heterogeneous across groups. North Africa–Middle East immigrants exhibit the highest minority intolerance (estimated at 97.85), more than six times that of Europe-EU15 immigrants (6.69). Latin America (93.13), Sub-Saharan Africa (87.08), and East Asia (81.22) also show high intolerance. On the native side, Italian intolerance is highest toward Sub-Saharan African immigrants (78.23) and lowest toward Europe-EU15 immigrants.

Long-run simulations over successive generations show that all minorities eventually converge to the Italian majority along the language dimension, but at heterogeneous rates. Seventy-five percent of second-generation immigrants speak Italian at home with their children (one-generation integration rate). Europe-EU15 and Other Europe minorities converge almost completely within a single generation. Latin America shows the slowest path, with only 70% integration after four generations. East Asia and Sub-Saharan Africa also integrate more slowly, driven respectively by high fertility rates and strong selection into homogamous marriages.

A counterintuitive counterfactual result is central to the paper: if Italian cultural intolerance were reduced to zero (full acceptance), cultural integration of minorities would slow by 15 percentage points over a generation (from 93% to 78% by the third generation). The mechanism is that greater native acceptance enables immigrants to sustain their own language even within heterogamous (mixed) marriages, increasing demand for such marriages and raising minority fertility, thereby preserving cultural distinctiveness.

Finally, doubling immigration inflows while holding population shares constant reduces third-generation integration from 93% to 86% (a 7-percentage-point reduction). Effects are concentrated among Sub-Saharan African (20-percentage-point reduction) and East Asian (6-percentage-point reduction) minorities, with little impact on European and North African minorities. When inflows are reweighted toward Sub-Saharan African and East Asian groups, integration losses for those minorities range from 20 to 60 percentage points by the third generation.

Q: What is the paper’s core methodological contribution? A: The paper embeds a collective household decision problem — covering fertility, socialization, and divorce — within a transferable-utility frictionless marriage matching framework. This allows marital utility to emerge endogenously from intra-household decisions rather than being specified exogenously. The key innovation is that socialization incentives and technologies differ systematically between homogamous and heterogamous marriages, and these differences feed back into marital matching and long-run cultural dynamics.

Q: What does “cultural intolerance” mean in this model, and how is it identified? A: Cultural intolerance is the psychological value a parent obtains from socializing a child to his/her own ethnic identity, relative to having a child adopt a different cultural-ethnic identity. It is the main parameter driving socialization effort and resistance to cultural integration. Identification relies on two sources of cross-sectional variation: differences in matching patterns, fertility, separation, and socialization rates across cultural-ethnic group pairings, and exogenous variation in the ethnic composition of the regional population across Italy’s 20 administrative regions.

Q: How heterogeneous are the estimated cultural intolerance parameters across minority groups? A: The parameters are highly heterogeneous. North Africa–Middle East immigrants have the highest estimated minority intolerance (97.85), more than six times the EU15 estimate (6.69). Latin America (93.13), Sub-Saharan Africa (87.08), and East Asia (81.22) are also substantially higher than EU15. The matrix is asymmetric: Italian intolerance toward Sub-Saharan Africans (78.23) is higher than toward North Africans (67.88), even though those two groups show comparable minority intolerance levels.

Q: What are the three mechanisms beyond intolerance parameters that explain heterogeneous integration dynamics? A: First, selection into homogamous marriages: Sub-Saharan Africa’s particularly strong selection into homogamy gives those households access to superior coordinated socialization technology, sustaining cultural heterogeneity despite similar intolerance levels to other groups. Second, fertility rates: East Asian minorities have particularly high estimated fertility, which amplifies the transmission of their cultural identity across generations. Third, socialization effectiveness in heterogamous marriages: Latin American immigrants are uniquely able to socialize children to their own language even when married to native Italians, making their integration the slowest despite being in many mixed marriages.

Q: What is the counterintuitive result about Italian cultural intolerance and integration speed? A: Lowering Italian cultural intolerance to zero would reduce minority integration by 15 percentage points over one generation, with third-generation integration falling from 93% to 78%. The intuition is that higher native acceptance enables immigrants to maintain their own language more effectively within heterogamous marriages, which in turn increases immigrant demand for intermarriage with natives and raises minority fertility — both of which slow cultural convergence rather than accelerating it.

Q: How do divorce dynamics differ between homogamous and heterogamous households? A: Heterogamous households exhibit higher separation rates than culturally homogeneous unions: 7.5% for mixed families with at least one Italian spouse versus 6.4% for homogamous Italian couples. In the model, divorce by heterogamous households can be a strategic choice by mothers with high cultural intolerance, since custody grants single mothers greater unilateral control over socialization. Divorce probabilities are decreasing in the number of children for both family types. Interestingly, heterogamous households invest more in socialization when divorced than when married, because the high-intolerance parent can act without spousal opposition.

Q: How well does the model fit the data? A: The raw correlation between predicted and observed gains to marriage is 0.84. The correlation between predicted and observed foreign-language socialization rates is 0.83, for both homogamous and heterogamous families. The dataset covers 92.5% of all marriages in Italy from 1995 to 2012, representing over 4 million marriages matched with birth and separation records at a 98.5% one-to-one match rate.

Q: What happens to cultural integration when immigration inflows are doubled with an overweighting of North Africa–Middle East, Sub-Saharan Africa, and East Asian immigrants? A: North Africa–Middle East immigrants reduce third-generation convergence by only 4 percentage points. By contrast, East Asian and Sub-Saharan African minorities produce integration losses ranging from 20 to 60 percentage points by the third generation. This wide range reflects how the interaction between high fertility, strong homogamy selection, and effective socialization in heterogamous marriages amplifies cultural persistence when these groups constitute a larger share of inflows.

Q: What is the one-generation cultural integration rate, and which groups diverge most from it? A: Seventy-five percent of second-generation immigrants speak Italian at home with their children, constituting the one-generation baseline integration rate. Europe-EU15 and Other Europe minorities converge almost completely within one generation, as does North Africa–Middle East. Latin America diverges most sharply downward, with only 70% integration even after four generations, and shows a partial retreat from integration in the first generation. Sub-Saharan Africa and East Asia also fall below the 75% one-generation benchmark.

Q: How does the paper relate to the debate on native labor market effects of immigration? A: The paper notes that sizeable negative labor market effects of immigration on natives are far from well-documented in the empirical literature, with results ranging from negative wage effects (Borjas) to positive or heterogeneous effects (Card, Ottaviano-Peri, Dustmann et al.). The authors therefore focus on the cultural externalities channel, which they argue better explains voter opposition to immigration, and study cultural integration structurally rather than examining wage outcomes.

Cultural intolerance: The psychological value a parent obtains from socializing a child to his/her own ethnic identity, relative to having a child adopt a different cultural-ethnic identity. It is specific to the household type (homogamous vs. heterogamous) and is the primary parameter measuring the strength of a group’s resistance to cultural integration.

Cultural socialization / language transmission: The costly investments parents make to transmit their own cultural-ethnic traits to children. In the empirical model, socialization is proxied by whether a parent speaks his/her own non-Italian language at home with children. Socialization technologies are more efficient in homogamous (same-ethnicity) marriages than heterogamous ones.

Homogamous vs. heterogamous marriage: A homogamous marriage is one in which both spouses share the same cultural-ethnic identity; a heterogamous marriage is one in which spouses differ. The distinction is load-bearing throughout the model: homogamous households have coordinated socialization incentives and superior technology, higher fertility, and lower separation rates.

Transferable utility (TU) matching: A marriage market framework in which utility is transferable between spouses, so that the equilibrium allocation maximizes aggregate marital surplus and equilibrium transfers are determined by outside options. The model is frictionless, meaning matching is driven purely by preferences over the characteristics of potential spouses.

Cultural integration (language dimension): In the paper’s long-run simulations, cultural integration is defined as the share of second- (or later-) generation immigrants who speak Italian at home with their own children. It is the empirical outcome used to track convergence to the majoritarian culture across generations.

Assortative mating along cultural-ethnic lines: The tendency for individuals to match with spouses of the same cultural-ethnic group. The paper finds positive assortative mating for all groups, with particularly strong homogamy for Sub-Saharan African and East Asian minorities, and explains it as the equilibrium outcome of the TU matching model given cultural intolerance preferences.

Socialization technology asymmetry: The model’s assumption that homogamous married parents hold a more efficient socialization technology than heterogamous parents, but that divorced heterogamous households invest more in socialization than married heterogamous ones, because the high-intolerance parent can act unilaterally without spousal opposition.

Measuring and Mitigating Racial Disparities in Tax Audits

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

Overview

Research Question. Do Black taxpayers face higher IRS audit rates than non-Black taxpayers, despite race-blind audit selection? And if so, why — and what would mitigation look like?

Data and Methodology. The authors use comprehensive administrative microdata covering approximately 148 million individual income tax returns and 780,627 operational audits for tax year 2014, supplemented with 71,878 research audits from the IRS National Research Program (NRP) pooled over 2010-2014. Because neither the researchers nor the IRS observe taxpayer race, the authors employ Bayesian Improved First Name Surname Geocoding (BIFSG), which imputes the probability that a taxpayer is Black from first name, surname, and Census Block Group. They develop a novel partial identification strategy: two estimators (a probabilistic estimator and a linear estimator) that, under conditions verified using a matched North Carolina voter-registration dataset containing self-reported race, asymptotically bound the true racial audit disparity from below and above respectively. To address the selective labels problem — underreporting is observable only for audited returns — the authors combine operational audit data with NRP random-sample audits to simulate counterfactual audit selection algorithms.

Main Findings.

Magnitude of the disparity. The probabilistic estimator implies a racial audit disparity of 0.81 percentage points; the linear estimator implies 1.34 percentage points. Against a base audit rate of 0.54% for the overall U.S. population in 2014, these bounds imply that Black taxpayers are audited at between 2.9 and 4.7 times the rate of non-Black taxpayers.

Role of the EITC. The disparity is concentrated among EITC claimants. The estimated disparity within the EITC population is 1.96 to 2.90 percentage points, compared to only 0.10 to 0.18 percentage points among non-EITC claimants. In relative terms, Black EITC claimants are audited at 2.9 to 4.4 times the rate of non-Black EITC claimants. A formal decomposition attributes 70-73% of the overall disparity to higher audit rates among Black EITC claimants, 20-21% to racial differences in EITC claiming rates, and 7-8% to differential audit rates among non-EITC filers. Within EITC claimants, 78.5% of the observed audit disparity is attributable to the Dependent Database (DDb) program.

Source of the disparity — algorithmic objective. Using counterfactual audit selection algorithms estimated on NRP data, the authors find that allocating EITC audits to maximize detected total underreporting (from any source) would produce audit rates of 0.74% for Black EITC claimants versus 1.63% for non-Black EITC claimants — reversing the disparity. In contrast, the status quo, which prioritizes detecting overclaimed refundable credits, yields 3.00% for Black claimants versus 1.04% for non-Black claimants. The primary driver is a difference in the types of noncompliance that are more prevalent by race: dependent-claiming errors are more common among Black EITC claimants (dependent error rate of 26.6% vs. 16.3% for non-Black), while the highest underreporting via business income underreporting is disproportionately concentrated among non-Black EITC claimants. An algorithm focused on refundable credit overclaims implicitly targets dependent errors and therefore selects Black taxpayers at higher rates.

Prediction model bias. Even conditional on the refundable-credit objective, the status quo disparity (1.96 p.p.) exceeds the disparity that would arise under an oracle that uses actual rather than predicted refundable credit overclaims (1.08 p.p.), suggesting that prediction errors are unevenly distributed by race. The refundable credit prediction algorithm generates a disparity of 1.75 p.p., approximately 60% larger than the oracle. The authors find suggestive evidence of missingness in birth certificate data (paternal information is disproportionately missing for children claimed on Black taxpayers’ returns) and differential predictive accuracy in the DDb risk score across race.

Operational consequences. Switching the objective from refundable credit overclaims to total underreporting would shift the composition of audited returns from predominantly dependent-eligibility issues (80% of refundable credit oracle-selected returns contain a dependent error) toward business income (86% of total-underreporting oracle-selected returns have business income underreporting). EITC returns with substantial business income (gross receipts above $25,000) cost on average $369.70 to audit versus $23.09 for other EITC returns. Holding the audit rate fixed, the switch would raise average examination costs by nearly an order of magnitude, while also increasing detected underreporting (mean adjustment of $22,578 per return under the total underreporting oracle versus $9,595 under the refundable credit oracle).

Scope Conditions. Results pertain primarily to tax year 2014. The paper finds similar patterns for tax years 2010, 2012, 2016, and 2018. The analysis covers Black versus non-Black taxpayers; disparities for other racial and ethnic groups are not the focus. The selective labels identification strategy relies on the NRP random-audit sample and the bounding conditions verified in the North Carolina matched data.

In depth

Q1. Why can’t the disparity be attributed simply to Black taxpayers being more likely to claim the EITC, combined with EITC claimants facing higher audit rates generally?

The authors test this directly by estimating racial audit disparities separately within EITC claimants and non-claimants. If differential EITC claiming rates were the full explanation, the within-EITC disparity would be close to zero. Instead, the disparity among EITC claimants (1.96-2.90 p.p.) is larger in absolute terms than the overall disparity (0.81-1.34 p.p.), indicating that Black EITC claimants face substantially higher audit rates than non-Black EITC claimants even holding EITC claimant status fixed. The formal decomposition attributes 70-73% of the overall disparity to differential audit rates within the EITC claimant population, not to differential claiming rates across the population.

Q2. How does the partial identification strategy work, and what are its key identifying assumptions?

The authors derive two estimators of the racial audit disparity that use BIFSG-imputed race probabilities rather than observed race. The probabilistic estimator weights each taxpayer’s contribution by their estimated probability of being Black; it is downward-biased when there is a positive residual covariance between audits and true race after conditioning on imputed race (E[Cov(Y,B|b)] > 0). The linear estimator regresses audit status on imputed race probability; it is upward-biased when there is a positive residual covariance between audits and imputed race after conditioning on true race (E[Cov(Y,b|B)] > 0). When both covariance terms are positive, the probabilistic and linear estimates bound the true disparity from below and above. The authors verify both conditions are positive and statistically significant (p < 0.01) in the matched North Carolina dataset, for the full population and the EITC population specifically.

Q3. Does the racial audit disparity within EITC claimants disappear when comparing taxpayers with similar levels of underreporting?

No. The authors use NRP data to estimate audit rates by race within each underreporting decile among EITC claimants. Within every decile of the underreporting distribution, the estimated audit rate for Black taxpayers exceeds that for non-Black taxpayers. An oracle algorithm that selects returns in descending order of actual underreporting produces an audit rate of 0.74% for Black EITC claimants and 1.63% for non-Black EITC claimants — the opposite of the status quo pattern (3.00% for Black, 1.04% for non-Black). This rules out total-dollar underreporting as the primary driver of the observed disparity.

Q4. Why does focusing audit selection on refundable credit overclaims specifically lead to higher audit rates for Black taxpayers?

Two mechanisms operate simultaneously. First, EITC eligibility is linked to children, so detecting erroneously claimed dependents generates large refundable credit adjustments. The dependent error rate is higher among Black EITC claimants than non-Black EITC claimants (26.6% vs. 16.3% in the probabilistic estimate, or 30.8% vs. 15.4% in the linear estimate). Second, the highest-dollar noncompliance via underreported business income is disproportionately concentrated among non-Black EITC claimants: among EITC claimants in the top 1% of business income underreporting, the probabilistic estimate shows 0.05% are Black compared to 0.21% non-Black. An algorithm aimed at refundable credit overclaims implicitly targets dependent errors and therefore selects Black taxpayers at higher rates; one aimed at total underreporting would prioritize business income underreporting instead and therefore select non-Black taxpayers at higher rates.

Q5. How do the simulated algorithms compare to the actual IRS algorithms?

The authors cannot directly replicate the IRS’s confidential DDb algorithm, but they provide three pieces of evidence that their refundable credit prediction algorithm is a reasonable proxy. First, public governmental documents describe DDb’s stated goal as identifying taxpayers who do not meet refundable credit eligibility requirements. Second, when selecting audits based on predicted refundable credit overclaims using largely the same features available to IRS, the authors generate a disparity (1.75 p.p.) close to the status quo disparity (1.96 p.p.). Third, operational audits of EITC returns are strongly associated with their predicted refundable credit overclaims measure but show a much weaker association with predicted total underreporting.

Q6. What does the status quo disparity exceeding the refundable credit oracle disparity reveal about prediction model design?

The status quo disparity (1.96 p.p.) is approximately 80% larger than the disparity that would arise if the IRS were perfectly informed about actual refundable credit overclaims and selected accordingly (oracle disparity: 1.08 p.p.). The refundable credit prediction algorithm generates a disparity of 1.75 p.p., approximately 60% larger than the oracle. This gap between the oracle and prediction disparity is consistent with prediction errors being distributed unevenly by race. The authors find that birth certificates of children claimed on Black taxpayers’ returns are substantially more likely to be missing paternal identity information, which may reduce the predictive accuracy of the DDb model for this population. They provide suggestive evidence that modifying the predictive features used could reduce the disparity without substantially degrading credit overclaim detection.

Q7. What are the downstream operational consequences of switching the algorithmic objective?

Switching from refundable credit overclaims to total underreporting would shift audited issues from dependent eligibility (80% of refundable credit oracle-selected returns have a dependent error) toward business income (86% of total underreporting oracle-selected returns have business income underreporting). Auditing business income returns is substantially more resource-intensive: $369.70 per return on average for returns with gross receipts above $25,000, versus $23.09 for other EITC returns. Holding the current EITC audit rate fixed, the share of audited returns with substantial business income would rise from 3% to 93%, raising total examination costs by nearly an order of magnitude. However, because total detected underreporting per audited return would also rise substantially (mean of $22,578 vs. $9,595), the increase in detected noncompliance would exceed the increase in audit costs, and the qualitative pattern persists even when accounting for higher per-return costs.

Q8. Is the disparity consistent across years, and is it driven by a particular audit type?

The authors find comparable audit disparities for tax years 2010, 2012, 2016, and 2018, confirming the 2014 results are not year-specific. The disparity is concentrated in correspondence audits: the estimated disparity in correspondence audit rates is 0.804-1.328 p.p. for the full population, while the disparity in field/office audit rates is only 0.010-0.016 p.p. The disparity is present in both pre-refund and post-refund audits, though pre-refund audits show a larger disparity even among correspondence audits alone. Among EITC claimants, the correspondence audit channel is nearly entirely responsible for the group-level disparity.

Q9. What heterogeneity exists within EITC claimants?

The disparity is especially pronounced among unmarried male EITC claimants with dependents: among this subgroup, the audit rate for Black men exceeds the audit rate for non-Black men by more than 4 percentage points, and both are an order of magnitude above the overall U.S. population audit rate. Disparities are smaller among joint filers, unmarried women, and unmarried men without dependents, though the ratio of Black to non-Black audit rates remains substantial across all subgroups. The concentration of the disparity among unmarried men with dependents is consistent with the role of dependent-claiming errors, which are more likely to arise in family structures characterized by nonmarital cohabitation — a pattern more prevalent among Black Americans due to lower marriage rates.

Q10. Can the disparity be attributed to disparate treatment — i.e., race-conscious selection?

The authors rule out disparate treatment for the EITC population. The DDb audit selection process for EITC returns is automated (no manual review), and IRS does not use race or geography as an input into audit selection. The disparity is therefore the product of disparate impact: race-neutral selection criteria interact with racially correlated patterns of tax return characteristics to produce differential audit rates. For higher-income non-EITC taxpayers, where audit selection may involve human classifiers, the authors cannot rule out disparate treatment.

Key Concepts

Audit Disparity (D). Defined in the paper as D = E[Y|B=1] - E[Y|B=0], the difference in audit rates between Black taxpayers (B=1) and non-Black taxpayers (B=0). This is a group-level difference in selection rates, not conditional on any other characteristic, and is the primary estimand throughout.

Probabilistic Disparity Estimator. An estimator that calculates group-specific audit rates by weighting each taxpayer’s contribution by their BIFSG-imputed probability of being Black (or non-Black). It is shown to be downward-biased when E[Cov(Y,B|b)] > 0, i.e., when there is residual positive association between true race and audits after conditioning on imputed race.

Linear Disparity Estimator. An estimator based on regressing audit status (Y) on BIFSG-imputed race probability (b). It is shown to be upward-biased when E[Cov(Y,b|B)] > 0, i.e., when imputed race probability predicts audits even after conditioning on true race. Together, the probabilistic and linear estimators form bounds on the true disparity under conditions verified empirically.

BIFSG (Bayesian Improved First Name Surname Geocoding). A probabilistic race imputation method that uses Bayes rule under a conditional independence assumption (first name, surname, and geography are independent given race) to compute Pr[Black | first name, surname, Census Block Group]. Applied here to all 148 million tax returns; calibrated and validated against matched North Carolina voter registration data with self-reported race.

Selective Labels Problem. The problem that noncompliance (underreporting) is observed only for returns selected for audit, not for the full filing population. In this paper it means the IRS cannot directly observe the underreporting distribution for unaudited returns. The authors address this using NRP random-audit data, which allows estimation of the unaudited underreporting distribution and construction of counterfactual selection algorithms.

Algorithmic Objective. The paper distinguishes between (1) the prediction component of audit selection — which model to use to forecast noncompliance — and (2) the objective component — what type of noncompliance to predict and pursue (overclaimed refundable credits versus total underreporting from any source). The paper finds that the objective, not just prediction error, is an independent driver of the racial audit disparity.

Dependent Database (DDb) Program. The IRS’s primary EITC audit selection program, responsible for approximately 75% of audited EITC returns in 2014. DDb flags returns based on rules, heuristics, and proprietary risk scores, with the stated goal of identifying taxpayers who do not meet refundable credit eligibility requirements. Selection through DDb is fully automated, without human classifier review.

National Research Program (NRP). A stratified random sample audit program through which the IRS conducts near-line-by-line examinations of a small fraction of the filing population each year (approximately 2% of audited returns in 2014). The paper pools 71,878 NRP audits from 2010-2014 to identify the distribution of underreporting in the full EITC filing population and to estimate counterfactual selection algorithms.

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.

Racial Disparities in Housing Returns

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

Layer 1 — Overview

Research Question

This paper estimates the racial/ethnic gap in realized housing returns using administrative data on individual housing transactions, and investigates the mechanisms that generate those gaps. The central question is: why do Black and Hispanic homeowners accumulate less housing wealth than White homeowners, even as minority homeownership rates have risen substantially over the last century?

Data and Methodology

The authors merge three primary data sources. First, a nationwide panel of residential property records from ATTOM covering 146.8 million arm’s-length home purchases from 1990 to 2020, which records transaction prices, mortgage characteristics, and property-level identifiers. Second, Home Mortgage Disclosure Act (HMDA) records, which contain self-reported race and ethnicity for mortgage applicants. Third, supplementary administrative sources including McDash mortgage servicing records, Equifax credit bureau data, Fannie Mae/Freddie Mac/ABSNet modification records, and the Survey of Income and Program Participation (SIPP). After applying sample restrictions — including requiring an observed purchase price, a linked HMDA record, an arm’s-length repeat sale, a combined loan-to-value ratio of at most 102.5%, and an ownership spell of at least 12 months — the baseline analysis sample comprises 13.6 million ownership spells for Black, Hispanic, and White homeowners who purchased homes with a mortgage between 1990 and 2016 in 40 states. Ownership spells unsold by March 2020 have their value imputed using the FHFA county-level house price index, a procedure that is conservative in that it understates racial gaps.

The authors construct two complementary return measures. The unlevered return compares the annualized ratio of sale price to purchase price. The levered return (internal rate of return) sets the net present value of all homeowner cash flows — down payment, monthly mortgage payments, implicit rent, maintenance, taxes, insurance, transaction costs, and limited liability in foreclosure — equal to zero.

Main Findings

Among mortgaged home purchases, mean annual unlevered returns are 0.5% for Black homeowners, 0.6% for Hispanic homeowners, and 2.8% for White homeowners, implying Black-White and Hispanic-White gaps of approximately 2.3 percentage points per year. Mean annual levered returns are 1.6%, −3.0%, and 6.6% for Black, Hispanic, and White homeowners respectively, yielding gaps of 5.0 and 9.6 percentage points. After adjusting for the approximately one-fourth of purchases made in cash (for which no racial gap is found), preferred estimates of the unlevered gap are 1.9 (Black-White) and 1.4 (Hispanic-White) percentage points.

Distressed sales — foreclosures and short sales — statistically account for the entire gap in returns. Within non-distressed sales, the Black-White gap in annual unlevered returns falls to less than 40 basis points, and the Hispanic-White gap reverses sign. Two distinct factors drive the role of distressed sales: (1) Black and Hispanic homeowners are approximately twice as likely as White homeowners to experience a distressed sale, and (2) minority homeowners live in neighborhoods where distressed sale price discounts are larger — estimated at 39%–40% for Black and Hispanic homeowners versus 28% for White homeowners. A Blinder-Oaxaca decomposition indicates that equalizing distressed sale rates (holding the distressed sale penalty fixed) would eliminate 84.6% of the Black-White unlevered returns gap and 133.6% of the Hispanic-White gap, confirming that the frequency margin dominates the severity margin.

A counterfactual wealth-accumulation exercise using PSID data shows that equalizing housing returns reduces the Black-White gap in housing wealth at retirement by 37%. Equalizing first-time purchase rates reduces the gap by only 1%, illustrating that promoting homeownership without addressing the returns gap is largely ineffective. Equalizing both returns and purchase rates reduces the gap by 49%.

Mechanisms

Approximately one-third of the gap in unlevered returns can be explained by purchase year and county fixed effects, with much of this timing effect attributable to the Great Recession. Controlling additionally for income, family structure, gender, and leverage reduces the gap by a further ~0.3 percentage points, leaving a substantial residual. About half of the racial gap in mortgage default can be attributed to observable credit risk (family structure, income, leverage, credit score). The remainder is associated with unobservable liquidity shortfalls and income instability: median liquid wealth among Black and Hispanic homeowners is $2,400 and $5,400 respectively, and minority homeowners are 2–4 percentage points more likely to transition to unemployment conditional on pre-unemployment income. Using quasi-experimental variation from adjustable-rate mortgage resets, the paper shows that in response to a 10% increase in monthly payments, White homeowners increase 90-day mortgage default by 3.0 percentage points after 12 months, while Black and Hispanic homeowners show increases of 4.5 and 7.1 percentage points respectively — excess sensitivity that is not captured by credit scores. The early-2000s credit supply expansion through private securitization and portfolio lending channels (as distinct from GSE/FHA) contributed to 61.5% of the 6.2-percentage-point increase in the Black-White distressed-sale gap between the 2002 and 2006 purchase cohorts, and 52.0% of the 12.2-percentage-point increase in the Hispanic-White gap. Evidence from the National Survey of Mortgage Originations suggests that Black homeowners hold overoptimistic expectations about future house price growth and income growth relative to their realized outcomes, which may explain why high-risk minority households do not self-select out of homeownership.

Scope Conditions

Results pertain to mortgaged home purchases (approximately three-fourths of all purchases) by Black, Hispanic, and White homeowners in 40 states (non-disclosure states excluded), with primary coverage from 2000 to 2016. No racial gap in returns is found for cash purchases. The racial gap in non-distressed returns is small and not economically meaningful, so the findings specifically pertain to the realized-return distribution that includes the distressed-sale tail.

In depth

Q1. How large is the racial gap in housing returns, and how does it compare to previously documented racial disparities in housing costs?

A: Among mortgaged purchases, Black and Hispanic homeowners each realize annual unlevered returns approximately 2.3 percentage points lower than White homeowners; levered return gaps are 5.0 percentage points (Black-White) and 9.6 percentage points (Hispanic-White). In dollar terms, this translates to a difference of roughly $5,920 per year for the average Black homeowner and $6,762 per year for the average Hispanic homeowner on a ten-year holding horizon. These gaps are an order of magnitude larger than previously documented racial disparities in housing costs, such as post-origination interest rate disparities of about 40 basis points (~$500 annually for a $200,000 home) or inflated property tax assessments amounting to $300–$390 per year.

Q2. What is the role of distressed sales in explaining racial gaps in returns, and how do frequency versus severity contribute?

A: Distressed sales statistically account for nearly the entire racial gap in realized housing returns. Within non-distressed sales, the Black-White unlevered gap falls to less than 40 basis points and the Hispanic-White gap inverts. Two channels operate: (1) Black and Hispanic homeowners are approximately twice as likely as White homeowners to experience a distressed sale; and (2) within distressed sales, minority homeowners realize lower returns because they tend to live in neighborhoods with larger distressed-sale price discounts (estimated at 39–40% below imputed market value for Black and Hispanic homeowners, vs. 28% for White homeowners). A Blinder-Oaxaca decomposition indicates that equalizing distressed sale frequency (holding severity fixed) would close 84.6% of the Black-White gap and 133.6% of the Hispanic-White gap, so the frequency margin is quantitatively dominant.

Q3. Are racial differences in house price appreciation responsible for the gap in non-distressed returns?

A: No. Among non-distressed sales, realized returns closely track county-level FHFA house price index growth for Black, Hispanic, and White homeowners alike, essentially one-for-one regardless of race. There is no economically meaningful racial gap in house price appreciation conditional on avoiding a distressed sale. This finding implies that the gap in average realized returns is not generated by differential neighborhood-level appreciation but rather by the incidence of distressed sales and the price penalties they entail.

Q4. How much of the racial gap in housing returns can be explained by observable homeowner characteristics such as income, family structure, and leverage?

A: Controlling for county and purchase year fixed effects reduces the raw Black-White and Hispanic-White unlevered returns gaps from 2.3 to 1.5 and 1.6 percentage points, respectively. Additionally controlling for income, family structure (gender and co-applicant status), and leverage reduces the gap by a further ~0.3 percentage points. Even among the ostensibly safest group — high-income couples with low leverage — the Black-White (Hispanic-White) gap in unlevered returns is 0.7 (0.5) percentage points. Among high-leverage, low-income, single-male homeowners the gap is 1.8 (1.7) percentage points. Gaps exist within every demographic subgroup, and neighborhoods (Census tract fixed effects) explain roughly half of the remaining gap for Black homeowners and one-third for Hispanic homeowners, but substantial residual gaps persist even within neighborhood.

Q5. What observable credit risk characteristics explain racial differences in mortgage default?

A: Raw racial gaps in 90-day mortgage delinquency are 2.6 percentage points (Black-White) and 1.8 percentage points (Hispanic-White). Controlling for purchase year and county reduces these to 2.2 and 1.6 percentage points respectively. Controlling for family structure, income, leverage, and credit score reduces the gaps to 0.98 and 0.94 percentage points — implying that observable characteristics explain approximately 55% and 41% of the Black-White and Hispanic-White default gaps respectively. Credit scores contribute the most explanatory power among these controls, while mortgage contract characteristics (a test of differential lender treatment) contribute negligibly.

Q6. What is the evidence that liquidity and income instability — factors not observable to lenders — explain the residual racial gap in default?

A: Survey data from SIPP reveal that median liquid wealth (bank accounts, stocks, bonds) for Black and Hispanic homeowners is only $2,400 and $5,400 respectively, while minority homeowners are 2–4 percentage points more likely to transition to unemployment conditional on pre-unemployment income. In SIPP mortgage delinquency regressions, controlling for liquidity, job loss in the prior year, and income reduces the Black-White coefficient by about 30% and the Hispanic-White coefficient by about 41% (and 29% and 70% respectively when also controlling for income level, current loan-to-value, and family composition). In administrative data using ARM payment resets as liquidity shocks, a 10% increase in monthly payments raises 90-day default by 3.0 percentage points for White homeowners, 4.5 percentage points for Black homeowners, and 7.1 percentage points for Hispanic homeowners after 12 months. This excess sensitivity is not substantially reduced by controlling for credit scores, income, or leverage — indicating that the liquidity risk of minority homeowners is largely unobservable to lenders at origination.

Q7. Is there evidence that strategic default explains higher minority distress rates?

A: No meaningful evidence supports strategic default as a driver of excess minority distress. Using quasi-experimental variation in ex-post leverage from diverging option ARM indices (following Gupta and Hansman 2022), the paper finds large causal impacts of leverage on default but no evidence that these impacts are larger for minority homeowners. Separate survey evidence from the NSMO shows a statistically insignificant Black-White difference of 0.05 percentage points (s.e. 0.65) in agreement that “it is okay to default if it is in the borrower’s financial interest” (relative to a White mean of 6.1%). The absence of larger leverage-driven default responses combined with the presence of larger payment-shock-driven responses points specifically to liquidity — not strategic behavior — as the relevant mechanism.

Q8. What is the evidence for information frictions contributing to excess minority homeownership risk?

A: Black homeowners in the NSMO report future house price expectations that are 0.07 standard deviations more optimistic than White homeowners, conditional on past price experiences, yet realized house price growth in the subsequent two years is actually 1.1 percentage points lower for Black homeowners. Although Black homeowners are 2.8 percentage points more likely to report past personal financial crises, their stated expectations about future financial crises are similar to those of White homeowners — despite 90-day default rates that are 2.5 percentage points higher in the first two years post-origination. Black homeowners also report income growth expectations 0.3 standard deviations higher than White homeowners, while SIPP and CPS data show minorities are more likely to experience income losses. These patterns of overoptimistic expectations relative to realized outcomes are consistent with information frictions causing high-risk minority households to suboptimally select into homeownership.

Q9. How much of the racial gap in distress can be attributed to the early-2000s credit supply expansion?

A: The paper identifies the expansion as concentrated in portfolio loans and privately securitized mortgages, which are distinct from GSE/FHA mortgages that did not exhibit a comparable supply increase. Between the 2002 and 2006 purchase cohorts, the Black-White gap in distressed sales rose by 6.2 percentage points overall but only 2.4 percentage points among GSE/FHA loans. A decomposition using this contrast attributes 61.5% of the overall 6.2-percentage-point increase to the credit supply expansion. Analogously, 52.0% of the 12.2-percentage-point increase in the Hispanic-White gap between 2002 and 2006 is attributed to credit supply. Within-race decompositions find that credit supply accounts for 42%, 30%, and 35% of the increase in distress relative to 2002 for Black, Hispanic, and White homeowners respectively, for mortgages originated 2004–2006.

Q10. What is the implied contribution of the returns gap to the racial wealth gap?

A: Using a simple wealth accumulation model calibrated to PSID data on first-time homebuyer rates and home values (average first home for Black households: $142,587; for White households: $208,621), the paper finds an estimated Black-White gap in housing wealth at retirement of $169,389 versus an observed PSID gap of $182,771. Equalizing housing returns would reduce this gap by 37%. In contrast, equalizing first-time purchase rates alone reduces the gap by only about 1%, because low returns nullify the benefit of purchasing earlier. Equalizing both returns and purchase rates reduces the gap by 49%. Housing wealth in the primary home constitutes 43% of total net wealth for the average retirement-age Black household in PSID, implying the returns gap explains a quantitatively large share of the overall racial wealth gap.

Q11. What do the COVID-19 pandemic forbearance experience and mortgage modification evidence imply for policy?

A: Quasi-experimental estimates using servicer-level variation in modification propensity show that mortgage modifications cause economically large increases in housing returns for Black, Hispanic, and White homeowners alike, suggesting that since minority homeowners are more likely to become distressed, expanded modifications would disproportionately benefit them. The pandemic experience provides macroeconomic confirmation: after the onset of COVID-19 forbearance and foreclosure moratoria in March 2020, the Black-White gap in unlevered returns and distressed sales fell by approximately half, while the Hispanic-White gap (whose pre-pandemic distress convergence was already underway) remained comparatively stable. Administratively, Black homeowners who default are already 3–7 percentage points more likely than observationally similar White homeowners to receive a modification, even controlling for neighborhood and servicer, suggesting servicers partially internalize the larger distressed-sale discounts in minority neighborhoods.

Q12. Are neighborhood-level factors — specifically distressed-sale price discounts from illiquid real estate markets — important for explaining racial heterogeneity in returns conditional on distress?

A: Yes. Using MLS data on median days-on-market as a measure of real estate market thickness, the paper shows that distressed sale discounts are substantially larger in less-liquid markets, with discounts experienced by Black homeowners approximately 13 percentage points lower in the least-thick markets relative to the thickest. Black and Hispanic homeowners are disproportionately likely to realize distressed sales in thin markets. Regular sale returns are not affected by market thickness. This establishes that neighborhood market illiquidity is a second-order channel through which neighborhood-level factors contribute to the racial gap — primarily by amplifying the severity of distressed sale penalties rather than by affecting ordinary house price appreciation.

Key Concepts

Distressed sale: In this paper’s usage, an ownership spell that ends in either a foreclosure (where a lender seizes and sells the property after payment default) or a short sale (where the lender allows the homeowner to sell for less than the outstanding mortgage balance without holding the homeowner liable for the deficiency). Distressed sales are the central mediating factor between race and housing returns.

Unlevered return: The annualized ratio of sale price to purchase price, capturing property-level capital gains without reference to the financing structure. Computed as (P_sale / P_purchase)^(1/T) − 1. Does not capture leverage amplification or limited homeowner liability in foreclosure.

Levered return (internal rate of return): The discount rate that sets the net present value of all homeowner cash flows to zero, including down payment at purchase; monthly payments (principal, interest, taxes, insurance, maintenance); implicit rent; and the net proceeds at sale (property sale price minus outstanding principal balance, subject to a floor of $0.01 capturing limited liability). This measure accounts for both the amplifying effect of leverage on gains and the homeowner’s limited liability in underwater foreclosures.

Distressed sale frequency versus severity: The two distinct components through which distressed sales generate racial gaps. Frequency refers to the higher probability that a minority homeowner’s ownership spell terminates in a distressed sale. Severity refers to the larger price discount at distressed sale that minority homeowners experience, concentrated in neighborhoods with illiquid real estate markets. The paper’s decomposition finds frequency is the dominant margin.

Unobservable liquidity risk: Default risk arising from insufficient liquid wealth (cash, bank deposits, liquid securities) and income instability that is not captured by credit scores or other characteristics observable to lenders at mortgage origination. The paper’s ARM-reset event study shows this risk generates excess minority default responses even conditional on credit score and income.

Information friction (overoptimism): The tendency of minority homeowners, particularly Black homeowners, to hold expectations about future house prices, personal financial crises, and income growth that are more optimistic than their realized outcomes and than observationally similar White homeowners’ expectations. The paper uses this to explain why high-risk minority households do not self-select out of homeownership despite the high cost of distressed sales.

Credit supply channel: The mechanism by which the early-2000s expansion of private securitization and portfolio lending — channels that exhibited substantially greater growth among Black and Hispanic borrowers than among White borrowers — contributed to increased rates of minority distress during the Great Recession. Distinguished from GSE/FHA channels that did not exhibit comparable credit expansion and serve as the counterfactual.

Rationing by Race

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

Singh and Venkataramani ask whether resource scarcity causes discriminatory rationing of health care by patient race, with patient death as the starkest possible outcome of biased allocation decisions. They examine 107,221 inpatient admissions from 2015 to 2018 at two large urban academic teaching hospitals (each with over 500 beds) in a Southeastern U.S. city with a sizable Black population. Black patients accounted for 60% of admissions, were on average younger (52 vs. 59 years), more likely to be female (65% vs. 50%), and had similar comorbidity burdens and baseline in-hospital death rates (approximately 2% for both groups), but waited over two hours longer on average for an inpatient bed and were 27% less likely to be admitted to the ICU.

The authors exploit quasi-exogenous hour-to-hour variation in hospital capacity strain — measured as the share of inpatient beds occupied at the hour of a patient’s arrival — which clinical and qualitative literature establishes is difficult to predict even day-to-day. Capacity strain is coded in hospital-specific deciles (beds filled ranged from 69–78% in decile 1 to 91–95% in decile 10). The core regression interacts patient race with strain decile, controlling for hospital-specific hour-of-day, day-of-week, month-of-year, and year fixed effects; physician-of-record fixed effects; and a rich vector of patient characteristics including Elixhauser comorbidity indices, insurance status, and vital signs. Identification rests on the assumption that strain at the hour of arrival is conditionally independent of unobserved patient characteristics correlated with race — an assumption validated through balance tests on demographics, comorbidities, vital signs, machine-learning-derived admission themes, and selective discharge patterns.

The main finding is that in-hospital mortality rises for Black patients but not for White patients as hospitals approach capacity. At the tenth decile of strain, Black patients face a mortality rate 0.7 percentage points higher than White patients — a 47.6% relative increase over the 1.47% White mortality rate at the same decile. A pooled difference-in-differences estimate implies that approximately 15% of Black patient deaths at high strain (decile 10) would not have occurred had Black patients faced the same strain-mortality relationship as White patients (coefficient 0.0052, p = 0.025). This pattern is concentrated among patients with the greatest ex ante medical need as measured by above-median Elixhauser mortality index scores (a score with AUC of 0.92 for predicting in-hospital mortality) and, in qualitatively similar but less precisely estimated form, by abnormal vital signs at arrival.

The authors identify wait time for an inpatient bed as the primary mechanism. At all levels of capacity strain, high-need Black patients wait longer than low-need White patients — a pattern the authors characterize as a striking inversion of any need-based allocation principle. Racial disparities in wait times widen further at the highest decile of strain, exactly mirroring the mortality pattern. As an additional, more suggestive mechanism, the authors analyze free-text clinical documentation (the Reason for Admission field) using descriptive text features (time to completion, character count, average word length), sentiment analysis (subjectivity and polarity scores via TextBlob), and adjective counts. Documentation for Black patients exhibits features consistent with lower provider effort at all strain levels — shorter notes, less time deferred to completion — and subjectivity of notes and adjective counts diverge further by race at the highest strain decile, with White patients receiving increasingly detailed and descriptive notes as strain rises.

The findings are robust across sparse models (age, gender, hospital fixed effects only) through fully saturated specifications (DRG fixed effects, interactions of all controls with race and strain), and to replacing Elixhauser index composites with their 31 individual comorbidity components. The authors explicitly scope their findings to a pre-COVID-19 period (2015–2018), while noting that pandemic-era record capacity strain and racial disparities in health outcomes suggest de facto race-based rationing may have been far more severe during COVID-19.

Q: What is the central research question and why is the health care setting chosen? A: The paper asks whether increasing resource scarcity causes discriminatory rationing on the basis of race in consequential, high-stakes real-world decisions. Health care is chosen because it is high-stakes (patient death is the outcome), has a long documented history of racial discrimination at both provider and system levels, and offers uniquely detailed time-stamped electronic health record data that enables identification from hour-to-hour variation in capacity strain — a finer temporal resolution than most prior work.

Q: How is hospital capacity strain measured and what is the identifying variation? A: Strain is measured as the total number of patients occupying inpatient beds at the specific hour of a patient’s arrival, converted into hospital-specific deciles. The first decile corresponds to 69–78% of beds filled and the tenth decile to 91–95%. The identifying variation is residual hour-to-hour fluctuation in this measure after removing hospital-specific hour-of-day, day-of-week, month-of-year, and year fixed effects, which absorbs all predictable capacity patterns. Clinical and qualitative evidence establishes that even day-to-day strain is difficult to anticipate, making hour-to-hour residual variation plausibly as-if random.

Q: What are the main mortality findings, and how large are the racial disparities at peak strain? A: At the tenth decile of capacity strain, Black patients face a mortality rate 0.7 percentage points higher than White patients, representing a 47.6% relative increase over the 1.47% White mortality rate at that decile. The pooled difference-in-differences estimate (comparing decile 10 to deciles 1–9) implies that approximately 15% of Black patient deaths at high strain would not have occurred if Black patients had the same strain-mortality relationship as White patients (coefficient 0.0052, p = 0.025). White patient mortality does not increase at high strain; if anything, small (imprecisely estimated) decreases appear at deciles 7–9.

Q: Which patients drive the racial mortality disparity? A: The disparity is concentrated among patients with above-median Elixhauser mortality index scores — the ex ante sickest patients. The Elixhauser Mortality Index has a predictive AUC of 0.92 for in-hospital mortality. At decile 10, high-need Black patients experience a sharp increase in mortality not seen for high-need White patients or for low-need Black patients. Qualitatively similar but less precisely estimated results appear when acute need is measured by abnormal vital signs at arrival, with the difference that the triple interaction (race × strain × high-need vitals) is not statistically significant, consistent with vital signs being noisier proxies for severity than the Elixhauser indices.

Q: How do the authors validate the identifying assumption that strain is conditionally independent of patient composition by race? A: They document five types of supporting evidence: (i) the distribution of Black and White patients across hours of arrival and across strain deciles is nearly identical; (ii) regressions of patient demographics, all five Elixhauser comorbidity measures, and five vital signs abnormalities on race × strain interactions show no significant differential selection by race at different strain levels; (iii) machine-learning (Latent Dirichlet Allocation) topic themes from free-text admission notes change similarly by strain for Black and White patients; (iv) there is no evidence of selective discharge to hospice care by race and strain, with point estimates running counter to the hypothesis; and (v) strain is computed at time of arrival to the hospital rather than time of admission to an inpatient bed, preserving exogeneity.

Q: What is the primary identified mechanism for the mortality finding? A: Wait time for an inpatient bed is the primary mechanism. Black patients experience greater increases in wait times as strain rises compared to White patients, with the clearest divergence at decile 10 — exactly mirroring the mortality pattern. More strikingly, at every decile of strain (including decile 1, when beds are most abundant), high-need Black patients wait longer for a bed than low-need White patients, implying that the disparity is not solely a product of logistical constraints but reflects ingrained factors in clinical protocols, likely including implicit or explicit provider bias.

Q: What does the wait time evidence reveal about the role of medical need vs. race in allocation decisions? A: At lower strain levels, low-need patients appropriately wait longer than high-need patients. However, at higher strain levels (deciles 8–10) this need-based gap almost entirely disappears, while the racial gap in wait times persists. The gap between high-need Black and low-need White patients is larger than the gap between high-need and low-need patients of the same race, meaning race is a stronger predictor of wait times than medical need. This pattern is consistent with the paper’s conceptual framework in which increasing strain reduces providers’ ability to accurately assess medical need while increasing the weight assigned to racial identity.

Q: How is provider effort measured and what are the findings? A: Provider effort is inferred from features of free-text Reason for Admission documentation: time to completion, character count, average word length, TextBlob subjectivity and polarity scores, and adjective counts. Across all strain levels, Black patients’ documentation exhibits features consistent with lower effort — shorter completion times (providers less likely to defer documentation for clinical tasks), shorter notes with fewer characters and shorter words. At the highest strain decile, subjectivity scores for Black patients’ notes increase relative to White patients’ (driven by both rising Black and falling White subjectivity), and White patients receive more adjectives as strain rises while Black patients’ adjective counts do not increase. Polarity scores remain stable by race and strain.

Q: What do the documentation patterns suggest about compensatory behavior by providers? A: The authors speculate that providers may anticipate reduced care quality at high strain and compensate by becoming more conscientious with White patients — writing longer, more detailed, more descriptive notes as strain increases, and potentially exerting greater care effort correlated with these documentation improvements. This protective compensatory behavior appears substantially less pronounced or absent for Black patients, which the authors suggest may translate into the small imprecisely estimated decrease in White patient mortality at higher strain deciles. They explicitly characterize this interpretation as speculative and requiring further investigation.

Q: How robust are the main mortality findings to specification choices? A: The mortality findings hold across: (i) sparse models with only age, gender, and hospital/year fixed effects; (ii) linear probability and logistic models; (iii) models with DRG fixed effects to compare within-diagnosis; (iv) models interacting all control variables with patient race and strain; (v) models replacing the Elixhauser composite index with its 31 individual comorbidity components; and (vi) models additionally controlling for five individual abnormal vital sign indicators. Results are substantively unchanged across all these specifications.

Q: What additional care intensity measures are examined and what do they show? A: The authors also examine ICU admission, ICU length of stay, total inpatient length of stay, and inpatient charges. They find no strain-related racial disparities on these margins. However, they note that unconditionally (across all strain levels), Black patients receive fewer resources on average — they are 27% less likely to be admitted to the ICU. The authors treat these care intensity measures as harder to interpret because both over- and under-provision can harm patients, and thus view them as less informative for their research question.

Q: What conceptual framework guides the empirical predictions? A: The framework models providers as assessing perceived medical need Nij(t) = Ni × exp(−γ × S(t)), where the parameter γ captures the diminishing ability to accurately assess true need as strain S(t) rises. Simultaneously, the racial weight Rij(t) = Ri × φ(S(t)) increases with strain through the parameter φ(S(t)). When γ = 0 and φ = 0, allocation is race-neutral and need-based. When both parameters are positive, increasing strain simultaneously degrades need assessment and amplifies reliance on racial identity in allocation decisions — the paper’s core prediction, which is confirmed empirically.

Q: How do the findings relate to the COVID-19 pandemic? A: The data predate COVID-19 (2015–2018). The authors argue that pandemic conditions — record hospital capacity strain (especially in hospitals serving Black patients), extreme provider burnout, and documented racial disparities in health access — suggest race-based rationing may have been considerably more severe during COVID-19. The paper also contextualizes its findings within the pandemic-era debate over whether explicit race-based triage protocols were ethical or legal, arguing that de facto rationing by race appears to occur in ordinary care settings under typical stressors irrespective of that normative debate.

Q: What policy interventions do the authors suggest? A: The authors propose: increasing provider awareness of implicit biases; developing new algorithms to improve triage decisions for high-mortality-risk patients who might otherwise be overlooked; correcting existing care algorithms with documented racial bias; building provider peer networks to reduce biased treatment decisions; supporting patient self-advocacy; improving capacity prediction systems (as spurred by COVID-19); and creating load-shifting protocols and inter-hospital transfer networks to prevent resources from being stretched beyond capacity during high-strain periods.

Capacity strain: The state of a hospital when a high share of inpatient beds are occupied, measured here at the hour of patient arrival as hospital-specific deciles of bed occupancy (ranging from 69–78% full at decile 1 to 91–95% full at decile 10); the paper’s primary measure of resource scarcity.

Rationing by race: The paper’s term for the phenomenon whereby, as resource scarcity deepens, allocation decisions increasingly reflect patient racial identity rather than medical need — a form of discriminatory rationing that the authors distinguish from explicit (de jure) race-based triage and document as de facto practice.

Perceived need (N*): In the paper’s conceptual framework, the provider’s assessment of a patient’s medical need, which deviates from true need Ni by the factor exp(−γ × S(t)) as strain S(t) increases; captures the provider team’s diminishing ability or willingness to accurately assess true medical need under cognitive and resource constraints.

Racial weight (R*): The weight assigned to a patient’s racial identity in allocation decisions, modeled as Ri × φ(S(t)), where the function φ is increasing in capacity strain; represents the potential for discrimination — from implicit bias, algorithmic bias, reduced patient advocacy, or provider-patient social distance — to intensify as strain rises.

Wait time inversion: The condition, documented throughout the paper, where high-need Black patients wait longer for an inpatient bed than low-need White patients at every decile of capacity strain, including decile 1 when resources are most abundant — inverting the normative principle that greater medical need should yield faster access to care.

Elixhauser Mortality Index: A widely validated composite score of patient comorbid conditions used to predict in-hospital mortality (AUC = 0.92); used in this paper as the primary measure of chronic medical need, with patients split at the median into relatively sick (above median) and relatively healthy (below median) groups.

Provider effort (inferred): An unobserved construct inferred in this paper from features of free-text clinical documentation in the Reason for Admission field, including time to note completion, character count, average word length, TextBlob subjectivity and polarity scores, and adjective counts; features argued to reflect how much attention, detail, and care a provider invested in documenting — and by extension, in assessing — a patient’s condition.

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.

The Confederate Diaspora

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

This paper investigates how white migration out of the postbellum South diffused Confederate culture and entrenched racial norms across the United States during a critical juncture of westward expansion and post-Civil War reconciliation. The central question is whether the “Confederate diaspora” — Southern white migrants who left the former Confederacy from 1870 to 1900 — causally shaped the geography of Confederate memorialization, white supremacist organizations, racial violence, and long-run racial inequity outside the South.

Using complete-count U.S. Census records from 1870–1900 and linked Census records from the Census Linking Project, the authors track nearly one million white migrants from former Confederate states, including more than 61,000 former enslavers and 127,000 of their household kin, who settled outside the South by 1900. By 1900, migrants from the former Confederacy comprised on average 2.2% of the population in destination counties. Four outcomes measuring Confederate culture at the county level are constructed: Confederate memorialization (monuments, place names, schools), United Daughters of the Confederacy (UDC) chapters, Ku Klux Klan (KKK) chapters, and lynchings of Black people.

The primary identification strategy is a shift-share instrumental variable (SSIV) that combines the cross-sectional distribution of Southern white migrants across non-Southern counties in 1870 (shares) with predicted migration flows out of each Southern state between 1870 and 1900 (shifts). The predicted shifts are constructed from origin-county economic and ideological push factors estimated via LASSO, insulating the IV from endogenous location sorting. Conditional on the 1870 Southern white population share, the SSIV identifies the distinct causal influence of the postbellum Confederate diaspora.

Main findings are large relative to the diaspora’s modest population share. Moving from zero to the mean Confederate diaspora share implies an 8 percentage point (p.p.) increase in the likelihood of KKK activity relative to a mean prevalence of 35% in non-Southern counties. Effects on post-1900 lynching events are even larger proportionally: a 4 p.p. increase in likelihood relative to a mean of only 5%. IV estimates for Confederate memorialization show that a 1 p.p. increase in the Southern white share in 1900 raised the likelihood of memorialization by 3.4 p.p. (after controlling for the 1870 share), relative to a baseline prevalence of 25% outside the South. Effects on UDC chapters are similarly large given the organization’s limited non-Southern footprint (present in only 10% of counties). IV estimates consistently exceed OLS estimates, consistent with economic sorting biasing OLS downward.

Beyond Confederate symbolism, the diaspora also contributed to a novel form of racial exclusion: the “sundown town.” A 1 p.p. increase in the Confederate diaspora share in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation (defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900).

Former slaveholders, though only about 6% of Confederate migrants, played an outsized role. They disproportionately sorted into frontier counties and into positions of public authority — more than twice as likely to work as lawyers or judges and nearly three times as likely to work in public administration as the average non-slaveholding Southern white migrant. Their cultural influence was especially pronounced in frontier communities where institutions were weak and norms malleable. In Denver, first-generation Southern white migrants were 11% more likely to join the KKK than men with no Southern heritage, with a similar differential observed for second-generation migrants.

The diaspora’s effects persist into the 21st century: counties with larger Confederate diasporas in 1900 exhibit larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, higher rates of police-induced Black mortality, and more conservative racial attitudes among whites, as measured in modern survey data. These long-run findings are identified using the same county-level SSIV strategy. Scope conditions: effects are larger in frontier counties (weaker institutions, more malleable norms), in counties with fewer Union Army enlistees, and in newly incorporated areas with fewer than 2 residents per square mile in 1860.

Q: What is the central research question and why does it matter? A: The paper asks whether postbellum Southern white migration causally diffused Confederate culture — memorialization, organized white supremacy, and racial violence — beyond the South, and whether this early cultural transplantation has persistent effects on racial inequity today. It matters because Confederate monuments and persistent Black disadvantage in labor, housing, and policing are often attributed to the legacies of slavery within the South; this paper shows the mechanism by which those norms spread nationally through internal migration at a critical juncture of westward expansion and post-war reconciliation.

Q: How large was the Confederate diaspora, and who comprised it? A: Estimates from linked Census records suggest that nearly one million whites left the former Confederacy for the rest of the U.S. in the three decades after the war, including more than 61,000 former enslavers and 127,000 of their household kin. By 1900, migrants from the former Confederacy averaged 2.2% of the population in non-Southern destination counties. The diaspora hailed primarily from the upper South — Virginia, Tennessee, and North Carolina — and later from Texas, Arkansas, and Oklahoma.

Q: How do the authors construct the shift-share instrumental variable, and what identifying assumption does it require? A: The SSIV multiplies each Southern origin state’s 1870 settlement shares across non-Southern counties (the shares) by predicted total Southern white outflows from 1870 to 1900 (the shifts), where the predicted shifts are constructed by summing LASSO-selected origin-county push factors — economic conditions, cotton and tobacco potential, Civil War battle locations, Black population share — rather than actual flows. The exclusion restriction requires that these predicted push-factor-driven outflows affect destination county outcomes only through the Confederate diaspora they deliver, not through direct economic linkages with origin counties. Conditioning on the 1870 Southern white share absorbs time-invariant destination heterogeneity correlated with antebellum settlement.

Q: What are the IV estimates for Confederate memorialization and UDC chapters? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of Confederate memorialization by 3.4 p.p. after controlling for the 1870 share (relative to a baseline prevalence of 25% outside the South). For UDC chapters, which were present in only 10% of non-Southern counties, IV estimates show similar or larger proportional effect sizes. IV estimates are consistently more than twice the size of OLS estimates, consistent with downward bias from economic sorting of Southern whites toward productive, culturally-diverse destinations.

Q: What are the IV estimates for KKK activity and Black lynchings, and how are they interpreted? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of KKK chapter presence by 3.5 p.p. (controlling for 1870 shares), relative to a mean KKK prevalence of 37% in non-Southern counties, implying that moving from zero to the mean diaspora share is associated with an 8 p.p. increase in the probability of KKK activity. For Black lynchings, the corresponding IV estimate is 1.5 p.p. (column 5), with the effect rising when earlier migration is controlled, against a mean prevalence of only 5% — implying moving from zero to the mean raises lynching likelihood by 4 p.p. Critically, the authors find no diaspora effect on white lynchings, which distinguishes racially-targeted violence from a generalized Southern culture of violence.

Q: What is a “sundown town” and what does the paper find about the diaspora’s role in producing them? A: Sundown towns, described in historical research by Loewen (2005), are all-white towns where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960 and representing a novel form of racial exclusion distinct from de jure Jim Crow institutions. The authors find that a 1 p.p. increase in the size of the Confederate diaspora in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation — defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 — changing the geography of Black settlement throughout the 20th century.

Q: What role did former slaveholders specifically play, and how are their effects separately identified? A: Former slaveholders comprised just over 6% of the Confederate migrant sample but played an outsized role: they were about 50% more likely than the average Southern white migrant to work in any public-facing authority occupation, more than twice as likely to work as lawyers or judges, and nearly three times as likely to work in public administration. Their effects are identified using an analogous SSIV that, conditional on the instrumented overall diaspora, draws on distinct identifying variation in slaveholder-specific push factors. Former slaveholders gravitated toward Western, lower-density, cotton-suitable counties with higher Breckinridge vote shares and fewer Union Army soldiers, consistent with seeking to reconstruct antebellum hierarchies in malleable frontier spaces.

Q: Why were effects stronger in frontier counties? A: The paper finds that diaspora impacts on Confederate culture diffusion were significantly larger in counties along the frontier, where state institutions were weak and cultural norms not yet deeply ingrained. Restricting the sample to counties with fewer than 2 residents per square mile in the 1860 Census yields somewhat larger estimates than baseline, and the differential sorting of Southern whites (especially former slaveholders) into these nascent communities suggests that institutional malleability amplified the cultural entrepreneurs’ influence. Fewer Union Army enlistees in destination counties also amplified effects, as those families might otherwise have opposed resurgent Confederate ideology.

Q: How did the diaspora transmit its norms to subsequent generations and non-Southern neighbors? A: In the Denver metropolitan area, using newly digitized KKK membership records, first-generation Southern migrants were 11% more likely to join the KKK than men with no Southern heritage, and a similar differential holds for second-generation migrants (born in the diaspora), with patterns holding within Census enumeration blocks. White men without Southern heritage living next door to first- or second-generation Southern whites were significantly more likely to join the KKK, consistent with horizontal cultural spillovers. For naming patterns, non-Southern white parents who moved to counties with a larger Confederate diaspora gave their later-born children names more evocative of Confederate heroes than those given to earlier-born children — providing direct evidence of cultural spillovers beyond the diaspora.

Q: What long-run effects of the diaspora are documented through the 21st century? A: Using the county-level SSIV strategy, the paper finds that a larger Confederate diaspora in 1900 is associated with larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, and higher rates of police-induced Black mortality through the 21st century. These disparities are mirrored in more conservative racial attitudes among whites in these counties as measured in modern survey data. These persistent effects suggest that, despite racially progressive national policy reform since the 1960s, locally institutionalized mechanisms reinforced by a culture of racial animus continue to generate inequity.

Q: How robust are the main estimates to alternative specifications? A: The authors show robustness across: (i) alternative spatial standard errors using Conley (1999) distance-based clustering and Adao et al. (2019) shift-share inference corrections; (ii) Belloni et al. (2014) double LASSO control selection; (iii) replacing predicted shifts with actual shifts; (iv) a random-shifts placebo where fewer than 5% of coefficients are significant; (v) dropping individual origin or destination states one-by-one (all estimates remain significant with 97% positive Rotemberg weights); (vi) excluding border states with antebellum slavery (Delaware, Kentucky, Maryland, Missouri, West Virginia), which actually increases estimates; and (vii) restricting to newly incorporated counties with near-zero 1860 populations, which yields somewhat larger effects.

Q: What is the paper’s contribution to the culture-institutions literature? A: The paper uses granular data on migration, occupational choices, and local governance to shed light on the historical process by which Confederate “cultural entrepreneurs” captured early institutions across America, illustrating how culture and institutions reinforce each other during critical junctures of nation-building. The findings suggest that laws to reduce racial discrimination may have limited impact where a culture of racial animus is ingrained in local institutions — an institutionalized persistence mechanism that helps explain the gap between formal legal reforms and observed racial outcomes. The paper also identifies a prestige-biased cultural transmission channel, consistent with Henrich and Gil-White (2001), wherein non-elite masses emulate former slaveowners in positions of power.

Confederate diaspora: The approximately one million white migrants, including more than 61,000 former enslavers and 127,000 of their household kin, who left former Confederate states for the rest of the U.S. in the three decades after the Civil War, comprising on average 2.2% of destination county populations by 1900 and retaining strong cultural attachments to the Confederacy.

Confederate culture: A cluster of symbolic and material expressions that coalesced in the postbellum South, encompassing Lost Cause narratives (glorifying Confederate figures and reframing secession as a defense of states’ rights rather than slavery), public memorialization (monuments, place names, school names), United Daughters of the Confederacy chapters, Ku Klux Klan activity, and lynchings of Black people — together functioning as technologies to transmit white supremacist norms and maintain racial hierarchies.

Lost Cause: A revisionist narrative emerging after the Civil War that sought to redeem the image of the South by offering noble rationalizations for secession — emphasizing Northern aggression and states’ rights while downplaying slavery — and portraying enslaved people as content and slaveowners as generously paternalistic; central to the ideology propagated by the UDC and to Confederate memorialization.

Shift-share instrumental variable (SSIV): An identification strategy that combines the 1870 distribution of Southern white migrants across non-Southern counties (shares, reflecting historical migration networks) with predicted total Southern white outflows from 1870 to 1900 constructed from origin-county push factors via LASSO (shifts), to isolate exogenous county-level variation in Confederate diaspora exposure that is insulated from endogenous location sorting.

Sundown town: An all-white municipality where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960, operationalized in this paper as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 (Black depopulation), representing a novel form of racial exclusion distinct from de jure Jim Crow institutions associated with the Confederacy.

Prestige-biased cultural transmission: An evolutionary transmission mechanism, formalized in Henrich and Gil-White (2001), in which non-elite populations emulate culturally salient leaders; invoked in this paper to explain how former slaveholders in positions of authority could diffuse Confederate norms to non-Southern whites who had no direct connection to the Confederacy.

Cultural entrepreneur: A migrant (especially a former slaveholder) who, by sorting into positions of public-facing authority — judges, lawyers, law enforcement, clergy, public administrators — at early stages of community formation when institutions are most malleable, actively embeds cultural norms into nascent local institutions, amplifying influence beyond their small population share.

Vanguard: Black Veterans and Civil Rights After World War I

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

This paper provides the first causal evidence on how military service shaped Black civil rights activism in the aftermath of World War I. The research question is whether random induction into the segregated National Army caused Black men to join the nascent NAACP and become prominent community leaders during the New Negro era. The authors leverage the WWI draft lottery — in which each registrant’s unique serial number was drawn from a bowl to determine induction order — as an instrument for military service, a source of exogenous variation not previously exploited in the literature.

To support this analysis, Ang and Chinoy construct an unusually rich dataset by digitizing nearly one million Black draft registration cards from the first registration (June 17, 1917), linking them through the 1930 full-count census to 233,517 NAACP member observations across 227 branches from 1912 to 1940, and supplementing with Veterans Administration records, Army Transport Service passenger lists, and biographical dictionaries of prominent African Americans. The instrument — serial number percentile within draft board and race (SNP%) — is validated against all observed pre-draft registrant characteristics and yields a first-stage F-statistic of 1,051 in the preferred specification.

The main finding is that Black men randomly induced to serve in the military were nearly three times more likely to join the NAACP than observably similar registrants from the same draft board (TSLS coefficient 0.0219, se = 0.0049, against a sample mean NAACP participation rate of 0.8%). The authors estimate that the draft induced more than 10,000 Black men to join the NAACP in total. Military service also raised the probability of appearing in biographical dictionaries of historically prominent African Americans by a factor of roughly 1.6 (TSLS coefficient 0.0027, se = 0.0012, sample mean 0.17%). These results are robust to alternative instruments, flexible polynomial specifications of SNP%, state-year fixed effects, and alternative veteran-status measures from VAMI and ATS records. They are also not explained by differential residential mobility: adding controls for interstate and North-South migration leaves the main coefficient essentially unchanged (0.0217-0.0218).

In contrast, TSLS estimates for all socioeconomic outcomes — literacy, home ownership, employment, census-predicted income, actual 1940 income, and educational attainment — are small and insignificant, ruling out human capital acquisition as a mechanism. Club involvement measured in the census is likewise unaffected, indicating that NAACP membership reflects specifically civil rights activism rather than generically greater social participation.

The mechanism the paper identifies is experienced discrimination. Effects on NAACP participation increase monotonically with the racial gap in induction rates across draft boards (significant at p = 0.01). Effects are large and significant for men assigned to camps that restricted Black soldiers’ access to military training (coefficient 0.0351, se = 0.0104) and to officer promotion (coefficient 0.0360, se = 0.0111), and are large for men in both restriction types simultaneously (coefficient 0.0367, se = 0.0114). In contrast, men attending less discriminatory camps show small and insignificant effects. Among the two all-Black combat divisions, NAACP participation is highest for veterans of the 92nd Division — subjected to constant racial abuse under U.S. command — and lower for the 93rd Division, which served under more hospitable French command. Previously unstudied veteran surveys from Virginia and Connecticut corroborate this narrative: respondents from camps with training and promotion restrictions were more than twice as likely to mention racial injustice, and mentions of injustice were more predictive of postwar civic engagement than any other survey theme.

The scope of the paper is Black male registrants in the first WWI draft registration (men aged 21-30 as of June 17, 1917), linked to a sample of approximately 300,000 in the 1930 census. Effects are attenuated for men from counties with greater racial hostility — proxied by Confederate state status, Confederate monument density, and county lynching rates — consistent with the interpretation that activism was more feasible in less repressive environments.

Q: What is the core identification strategy and why was it not feasible to use it before this paper? A: The paper uses each Black registrant’s serial number percentile within his draft board and racial group (SNP%) as an instrument for WWI military service. Unlike the WWII and Vietnam drafts, which used birthday-based lotteries, the WWI lottery assigned induction order by drawing unique serial numbers from a bowl, making serial number rank the source of quasi-random variation. This source had never been exploited in the literature, partly because the serial numbers had to be hand-captured from digitized draft card images.

Q: How strong is the first stage, and was the lottery truly random? A: The first-stage F-statistic is 1,051, and a ten-percentile decrease in SNP% is associated with a 34.5 percentage point increase in the probability of serving. Bivariate serial numbers show some non-random patterns — nine of 13 pre-draft characteristics correlate with raw SN% — likely because some Southern boards inflated numbers for white registrants. Conditioning on board fixed effects and using SNP% within board-race cells eliminates these correlations; Panel B of Appendix Table A1 shows the largest standardized coefficient falls to 0.006.

Q: What is the magnitude of the effect on NAACP membership and how does the causal estimate compare to a naive OLS? A: The TSLS coefficient is 0.0219 (se = 0.0049) against a sample mean of 0.8%, implying roughly a threefold increase in NAACP membership. The OLS estimate of 0.0116 understates the causal effect, consistent with the marginal man induced by the lottery being observationally weaker than infra-marginal volunteers.

Q: Does the effect reflect simply that veterans moved to Northern cities where NAACP branches were more accessible? A: No. Adding indicators for interstate migration and North-South migration leaves the TSLS coefficient essentially unchanged at 0.0218 and 0.0217, respectively. The Great Migration channel is thus not the operative mechanism.

Q: Did military service improve Black veterans’ economic outcomes? A: TSLS estimates for literacy, home ownership, employment, census-predicted income, actual 1940 income, and educational attainment are all small and statistically insignificant. This contrasts sharply with evidence on Black veterans of WWII and Korea (Greenberg et al., 2022) and is consistent with the documented absence of meaningful postwar benefits or training for Black WWI soldiers.

Q: If it was not human capital or migration, what mechanism does the paper establish? A: The primary mechanism is exposure to institutional discrimination during military service. Three distinct empirical patterns converge: (1) effects increase monotonically with draft board racial disparities in induction rates; (2) effects are large and significant for men at camps that denied training and promotion, and near zero for men at less discriminatory camps; (3) veteran survey mentions of racial injustice are more common among men from discriminatory camps and are more predictive of postwar NAACP membership than any other survey theme.

Q: How do the two all-Black combat divisions differ in their postwar NAACP participation, and what does this reveal? A: Veterans of the 92nd Division, who fought under U.S. command amid constant racial abuse, show the highest NAACP participation rates. Veterans of the 93rd Division, who fought under French command and were received with relative hospitality, show lower (though not statistically significantly lower) participation. Since both divisions received similar formal training and neither group shows socioeconomic gains, the differential reflects discrimination exposure rather than skill acquisition.

Q: What is the quantitative scale of the effect for the most discriminatory camps? A: For men assigned to camps with restrictions on both training and promotion, the TSLS coefficient on NAACP membership is 0.0367 (se = 0.0114) — more than 1.5 times the average estimate of 0.0219. Men at camps without restrictions show coefficients that are small and statistically insignificant.

Q: How does county-level racial hostility moderate the effect? A: The effects of military service on NAACP membership are larger — more positive — for men from counties with fewer Confederate monuments, lower lynching rates, and non-Confederate state status. This is interpreted as evidence that activism in response to discriminatory military experiences was more feasible in less racially hostile local environments, rather than as evidence that discrimination exposure was lower.

Q: What is the paper’s aggregate policy implication regarding the scale of the draft’s effect on the civil rights movement? A: The authors estimate that the WWI draft induced more than 10,000 Black men to join the NAACP. Veterans accounted for nearly 15% of all male NAACP members, against roughly 8% of Black male adults in the population, and were significantly more likely to appear in biographical dictionaries of prominent African Americans. The draft thus constituted a sizable and measurable contribution to the organizational vanguard of the early civil rights movement.

Q: How does the paper contribute to the economics of discrimination beyond documenting discriminatory behavior by majority actors? A: Most economics research on discrimination studies the conduct of white decision-makers (e.g., racial bias in hiring, lending, or bail). This paper examines how experiences of discrimination reshape the political behavior and aspirations of the minority group itself. The results show that institutional betrayal — systematic exclusion, degradation, and denial of training — generated deep discontent that translated into aggressive political mobilization, a dynamic the authors trace through subsequent episodes including the WWII Double V campaign and responses to police killings.

Serial number percentile within draft board and race (SNP%): The instrument constructed by the authors. Each WWI registrant received a serial number from 1 to the size of his draft board; those numbers were drawn in random order to determine induction priority. SNP% measures where a registrant fell in that draw relative to others in his board and racial group, and serves as the source of quasi-random variation in veteran status.

New Negro era: The period of invigorated Black political and cultural assertiveness following WWI, characterized by renewed racial pride, economic independence, and progressive politics. The movement spanned the Harlem Renaissance, the Universal Negro Improvement Association, the American Negro Press, and the Brotherhood of Sleeping Car Porters, and represented a rejection of the “conservatism, parochialism, and political accommodationism” of older Black leaders.

Draft board racial gap: The authors’ measure of draft board discrimination, defined as the difference in induction rates between Black and white registrants within a given draft board. The interquartile range spans roughly 0 to 20 percentage points, with a notable fraction of boards exhibiting gaps exceeding 30 percentage points.

Camp discrimination: The denial of military training and officer promotion opportunities to Black soldiers, documented in War Department reports by military intelligence officers tasked with monitoring the treatment of Black soldiers. The paper classifies each camp as restricted or unrestricted on each dimension and uses this classification to estimate heterogeneous treatment effects.

Institutional betrayal: The paper’s characterization of the U.S. government’s treatment of Black WWI soldiers — drafting them at higher rates than whites, denying them training and promotion, and assigning them to menial labor — as generating a profound sense of injustice that motivated postwar political activism rather than loyalty or accommodation.

NAACP membership as civil rights activism proxy: The paper uses dues-paying membership in local NAACP branches as its primary quantitative measure of civil rights participation. Membership involved active financial cost (annual fees of $1 to $10 at a time when median Black family income was below $500), exposure to harassment and violence in the South, and participation in local protest and legal advocacy, distinguishing it from passive civic engagement.