The Impact of School Desegregation on White Individuals' Racial Attitudes and Politics in Adulthood Free

Black and White youth in the United States largely attend segregated schools (Orfield, Kucsera, and Siegel-Hawley 2012), and this racial isolation can contribute to inequality, as some scholars find that having more Black peers leads to worse educational outcomes (e.g., Billings, Deming, and Rockoff 2014). Integration may additionally benefit all students—and society more broadly—by encouraging the development of skills necessary for healthy civic engagement in multiethnic communities (for a review, see Ayscue, Frankenberg, and Siegel-Hawley 2017). The contact hypothesis (Allport 1954) specifically predicts that, in certain instances, increased White–Black contact in more racially diverse schools will improve students’ outgroup attitudes and decrease their negative outgroup bias. Notably, these measures also relate to White–Black inequalities in educational and socioeconomic outcomes (e.g., Bertrand and Mullainathan 2004; Charles and Guryan 2008; Chetty et al. 2020; Chin et al. 2020; Riddle and Sinclair 2019).

Most evaluations of intergroup contact, however, cannot make causal claims on whether and how racial attitudes shift immediately and over time (Paluck, Green, and Green 2018), though related K–12 education research does provide some exceptions. For example, Billings, Chyn, and Haggag (2021) find that after the Charlotte-Mecklenburg School District ended race-based busing in the early 2000s, White students that enrolled in schools with more racially minoritized peers were substantially less likely to be registered as a Republican in adulthood. Merlino, Stenhardt, and Wren-Lewis (2019) document that White youth with more same-gender Black peers in schools during the mid-1990s had more racially diverse relationships as adults and scored higher on proxies for positive racial attitudes. Shen (2018) shows that historical school desegregation outside the U.S. South increased biracial births among Black mothers, another potential proxy for improved racial attitudes (cf. Gordon and Reber 2018). Finally, Kaplan, Spenkuch, and Tuttle (2021) provide novel evidence on the long-run effects of school integration in Jefferson County, Kentucky: White male individuals quasi-randomly exposed to racially integrated schools because of a court-ordered desegregation busing plan were more (less) likely to be registered as a Democrat (Republican) and less likely to support conservative causes with donations. In contrast, similar studies of the school desegregation era of the 1960s through 1980s were methodologically flawed and/or largely observational (Schofield 1991).

All together, the investigations that support contact theory's predictions in racially diverse schools are limited. The existing studies in education primarily rely on outcomes that proxy for or correlate with racial attitudes, such as individuals’ political ideology (e.g., Kuziemko and Washington 2018; Valentino and Sears 2005) and the diversity of relationships. Furthermore, we lack convincing, nationwide evidence from the time following the Brown v. Board of Education Supreme Court decision, when the educational experiences of youth across the country were substantially altered as schools witnessed the largest decreases in racial isolation in U.S. history. In this study, I thus set out to address this gap in the literature by answering the following question: What is the causal impact of historical court-mandated school desegregation on White individuals’ racial attitudes and politics as adults?

To answer this question, I use nationwide data from the General Social Survey (GSS) geocoded to White adult respondents’ county of residence as teenagers. I focus on responses to questions related to racial attitudes and politics in counties where districts racially integrated schools following court mandates during the 1960s, 1970s, and 1980s.¹ Using information on respondents’ age relative to when major desegregation plans were implemented, I identify whether White adults in my sample were exposed as youth to desegregated schools (i.e., they were not yet 18 at the time of integration) or were not exposed (i.e., they were 18 and/or lived where districts were not mandated by courts to integrate). I then use a difference-in-differences approach to recover the effect of school desegregation on outcomes. Specifically, I compare the racial attitudes and politics of those exposed and not exposed to integration, after controlling for county (to account for time-invariant differences in outcomes across contexts) and cohort fixed effects (to account for contemporaneous trends across cohorts in attitudes and politics). Intuitively, if exposed and unexposed cohorts’ outcomes diverge in integrating counties even after subtracting the analogous cohort-level differences in comparison contexts, I would conclude that court orders to desegregate had a causal impact—assuming that racial attitudes and politics would have progressed similarly over birth cohorts between the two groups of counties.

I find that integration significantly reduced White individuals’ political conservatism as adults in the U.S. South but not elsewhere. I observe similar effect heterogeneity for attitudes toward Black individuals and policies promoting racial equity, but (positive) impacts and geographic variation are smaller in magnitude relative to those observed for conservatism. Investigations into mechanisms suggest that this heterogeneity may depend on the effectiveness of integration policies. In the South, White–Black exposure was greater following desegregation, and White disenrollment was lower.

I demonstrate that results are robust to concerns of bias resulting from potential nonrandom in- and out-mobility of individuals into integrating contexts. Though the richness of the GSS data in terms of outcomes and geocodes available uniquely allows me to identify the impact of school desegregation on White individuals’ racial attitudes and politics in adulthood, accounting for mobility is necessary because the survey is cross-sectional, that is, I do not have longitudinal geocodes for individuals since school age. My primary analytic models thus only focus on data from adults who report their current city of residence to be the same as their city of residence as a school-aged teenager—this helps address systematic differences in in-migration. Because even those who currently live in desegregated contexts who also report moving cities within state since childhood may still have attended the integrated school district in their locale (as city and district boundaries are not necessarily coterminous), I then test models that include these specific individuals in the analytic sample. Finally, I incorporate White adults who have moved cities within state since childhood, and who currently do not live in a desegregating county but who do live in a labor market area where other counties had integrated schools. Sensitivity analyses that use this latter sample in particular help to account for the plausible alternative explanation that the main findings stem from the out-mobility of more conservative White individuals with less positive racial attitudes from contexts that faced court-mandated integration (see the related phenomenon of White flight into neighboring locales after desegregation; Baum-Snow and Lutz 2011; Reber 2005; Welch and Light 1987).

In terms of magnitude, my preferred specifications predicting composite outcome scores document that, in the south, exposure to desegregated schools decreased conservatism by 0.35 standard deviation (SD) and increased positive racial attitudes by 0.081 SD. Replacing these composites with more intelligible measures, I find that integration increased the likelihood of voting for the Democratic candidate in the most recent U.S. presidential election by approximately 18.34 percentage points and of dismissing problematic cultural explanations for Black–White inequality by 16.47 percentage points. But even for more conservative models, estimates of the effect of reducing racial isolation across schools on White individuals’ racial attitudes and politics in the U.S. South are substantial. For analyses that treat as exposed to desegregation those who move to potentially avoid contexts facing court mandates, that is, due to holding more conservative politics and/or negative attitudes, I observe impacts of approximately −0.16 and 0.043 SD for the conservatism and positive racial attitudes composite scores, respectively. Estimates from specifications using these expanded samples in particular can serve as useful lower bounds for treatment effects, as they may more accurately assign “treatment” status to some White individuals but not others (i.e., those presently in non-integrated counties who migrated from desegregated districts versus those who were, in reality, never exposed), inducing greater measurement error.

This study thus provides additional support to policy makers attempting to reduce racial isolation across schools but who are weighing potential benefits against costs. For example, historical school integration often met intense opposition (see the Boston busing crisis) which, according to the necessary conditions outlined in Allport's contact theory (1954), meant that desegregation could actually exacerbate existing negative attitudes and bias. Present day efforts face additional institutional barriers. The Milliken v. Bradley Supreme Court ruling in 1974 established that school systems were not responsible to address one of the largest contributors to racial segregation—segregation across district lines (Fiel 2013)—unless the evidence proved that this segregation was established with racist intent; a more recent Supreme Court decision similarly limited districts’ options for how to voluntarily integrate their own schools (Parents Involved in Community Schools v. Seattle School District No. 1).

Other research finds negative effects of integration on Black students and their communities, though these impacts appear to have been outweighed by substantial gains for Black youth in terms of educational attainment and labor market success (e.g., Anstreicher, Fletcher, and Thompson 2022; Guryan 2004; Johnson 2011). In the short term, historical efforts to address racial isolation across schools led to Black teachers losing jobs, schools serving predominantly Black students being closed, and increases in disciplinary inequality by race (Chin 2021; Schofield 1991; Thompson 2022). More contemporarily, Bergman (2018) finds that racially minoritized students participating in an interdistrict integration program in California were more likely to be arrested; in Florida, the racial composition of schools affects whether Black and Hispanic students are identified as having a disability (Elder et al. 2021). Finally, Black youth may be more at risk to exposure to discrimination, racial microaggressions, and stereotype threat in contexts with more White students and teachers (e.g., Fries-Britt and Turner 2002; Steele 1997). Negative consequences may be particularly salient if attending schools serving a relatively Whiter population is not accompanied with increased access to key school resources (Diette et al. 2021). Relatedly, the extent to which Black students benefit academically from policies that can theoretically desegregate schools may depend on the tradeoffs incurred when participating in these programs (e.g., increased systemwide costs and longer travel times to non-neighborhood schools in contexts with significant school choice; Angrist et al. 2022).

The current study adds rigorous evidence confirming the theoretical positive impacts of school integration on individuals’ racial attitudes and politics. Notably, alternative reforms in education that might help address racial inequality (e.g., equalization of school resources) cannot directly offer this benefit, as they do not explicitly expand White–Black contact. Educational leaders might thus seek to implement policies that desegregate schools even if other beneficial reforms face fewer barriers or lead to fewer unintended negative consequences.

After discussing the prior research relevant to this study, I overview the data and method that allow me to answer my research question. I then describe results from analyses before discussing their implications for future research and policy efforts to integrate schools by race.

Many scholars have tested how desegregation affects the educational and socioeconomic outcomes of youth. Nearly all these studies show that integration policies improved Black students’ educational attainment and adulthood outcomes without negative consequences for White youth (Angrist and Lang 2004; Anstreicher, Fletcher, and Thompson 2022; Bergman 2018; Guryan 2004; Jackson 2009; Johnson 2011; Weiner, Lutz, and Ludwig 2009). Several factors can explain positive effects (Reardon and Owens 2014), including changes to Black students’ peer groups (Billings, Deming, and Rockoff 2014), and increases in the quantity (Johnson 2011) and quality (Jackson 2009) of their schools’ resources. But increasing Black students’ academic achievement was just one argument used by the Supreme Court to support their decision in Brown v. Board (Stephan 1978).² Another key motivating factor for addressing racial isolation was reducing the outgroup racial prejudice of both White and Black individuals.³

Allport's seminal piece on contact theory (1954) explains why many believed in the potential for desegregation to cause attitudinal changes in individuals. According to the theory, expanding White–Black contact can reduce prejudice, and such contact would substantially increase in integrated school settings—especially in a society where deeply entrenched residential segregation may have limited it otherwise. However, in his hypothesis, Allport (1954) also stressed that improved intergroup relations would most likely follow in contexts meeting certain conditions: equal status between Black and White individuals, shared goals and cooperation, and societal, legal, and cultural support for White–Black contact. Whether or not the formally segregated schools met these conditions after Brown v. Board is debatable (Gerard 1983), especially given variation in the capacity (or desire) of school leaders, teachers, and other stakeholders to establish classrooms conducive to successful intergroup racial interaction. And though Pettigrew and Tropp's (2006) influential meta-analysis of studies of contact theory suggests that White–Black interactions can lead to prejudice reduction even when Allport's conditions (1954) are not met, recent research highlight the need for more systematic, rigorous evaluation (Paluck, Green, and Green 2018).

Other explanations exist besides those put forth by contact theory for why and how the racial attitudes of White individuals may change—or remain stable—over time. White flight from integrated school districts or increases in private school enrollment could have limited actual contact between Black and White youth and hindered changes in attitudes (Baum-Snow and Lutz 2011; Reber 2005; Welch and Light 1987). Within-school segregation—due to tracking or the racial homophily of friendships—similarly impedes contact (Moody 2001; Oakes 1985). When measuring the racial attitudes of White adults who attended integrated schools, mobility may bias estimates from a surveyed sample (e.g., Gordon and Reber 2018; Shen 2018). Finally, experiences in adulthood may counteract attitudinal shifts resulting from reduced racial isolation. With prior research showing positive effects of desegregation for the educational and socioeconomic outcomes of Black youth (Anstreicher, Fletcher, and Thompson 2022; Guryan 2004; Johnson 2011), White adults who attended desegregated schools may have developed negative outgroup attitudes as labor market competition increased.

Schofield (1991) describes that much of the empirical research in the decades following Brown v. Board exploring the impact that integration had on racial attitudes could not establish causality, covered a constrained geographic scale, and suffered from weak measurement instruments. These limitations contribute to the early literature's overall inconclusiveness on desegregation's impact on attitudes and their proxies. As noted above, more rigorous investigations of both earlier and recent K–12 educational contexts provide stronger support for the importance of the racial composition of students’ peers (i.e., Billings, Chyn, and Haggag 2021; Kaplan, Spenkuch, and Tuttle 2021; Merlino, Steinhardt, and Wren-Lewis 2019; Shen 2018), those these studies do not necessarily measure individuals’ racial attitudes directly.

In summary, many explanations can account for the inconclusiveness of historical school desegregation's impact on racial attitudes, and early empirical studies were particularly limited methodologically. Rigorously testing each potential mechanism is beyond the scope of this paper, but I have described here the set of extant theories and studies of more recent contexts to stress that positive, negative, and null effects are possible. I next document the data, sample, and empirical strategy that help me to address the methodological concerns of prior work.

To investigate the impact of school desegregation on White individuals’ racial attitudes and politics in adulthood, I use responses to the GSS, a nationwide survey of adults first administered in 1972 by the National Opinion Research Center.⁴ Since 1994, the survey has been conducted in every even-numbered year. I focus on surveys conducted between the years 1993 and 2018, when restricted-use data contain geographic information on respondents’ county of residence. The items I use from these surveys fall into three primary categories, measures of: respondents’ background, socioeconomic outcomes, and racial attitudes and politics.

Respondents’ background data include their age, their race, their current county of residence, whether they were living in the same city at the age of 16, and the year they responded to the GSS. With this information, I identify whether White individuals lived in a county that underwent school desegregation and, if so, I use survey year and age to determine if the respondent was of plausible school age (i.e., 17 years old or younger) when the county's earliest major desegregation plan was implemented.

I use measures of respondents’ socioeconomic outcomes to test potential mechanisms for any observed effects of integration. Specifically, I explore whether desegregation impacts White individuals’ educational attainment, earnings, or perceptions of class as adults. I conduct this “placebo” test because White individuals’ racial attitudes and politics may shift negatively as a response to the labor market they face, and not just because of exposure to less racially isolated schools. As noted above, prior research shows that integration improved the educational and socioeconomic outcomes for Black youth (Anstreicher, Fletcher, and Thompson 2022; Guryan 2004; Johnson 2011), which would have led to more competitive labor markets. For educational attainment I focus on respondents’ number of years of schools completed and for earnings I use reported family income (in 1986 dollars). To assess perceptions of class, I create a composite score using responses to three GSS items querying respondents’ self-reported social class, satisfaction with his or her financial situations, and opinion of family income relative to “American families in general.” In online appendix C I describe in more detail how I estimate composite scores; online appendix table C1 provides summary statistics for these three GSS items.

Finally, the primary outcomes in my analyses are respondents’ answers to questions regarding their racial attitudes and politics. I consider both sets of items because prior work tied to school integration and racial attitudes explore political outcomes and cite the association between the two. For the period following Brown v. Board in particular, the link between racial attitudes and partisan identity may be even more salient, as racially conservative White adults in the South who historically voted for Democratic political candidates realigned with the Republican party (Kuziemko and Washington 2018).

I identify nineteen items on GSS surveys that both plausibly relate to these topics and are also administered to a substantial number of survey respondents. However, the number of items and the relatively small size of my sample (described below) suggests that multiple inference may be an issue in analyses. As such, I use factor analyses to reduce the GSS data on White adults’ attitudes and politics into a set of three composite scores. These scores capture the conservatism of respondents’ politics (e.g., identifies as a Republican), their attitudes toward Black individuals and policies promoting racial equity (e.g., feels close to Black individuals relative to White individuals; favors affirmative action in hiring and promotions), and their support for protecting racist speech (e.g., believes individuals with racist points of view should be allowed to teach in a college or university).

In online appendix C, I provide details on the exploratory and confirmatory factor analyses informing the creation of these three composite scales and my method for estimating composite scores for White GSS respondents.⁵ I also include in online appendix table A1 the item text for all survey questions I consider as well as summary statistics.

Most respondents lacking data on specific questions are missing this information completely at random (MCAR) due to the structure of the GSS. Specifically, though many items regarding individuals’ racial attitudes and politics are asked across survey administrations, not every item appears in all years or on all survey forms. As such, I also detail in online appendix table A1 the rates of MCAR and other missingness for items I analyze. To account for missingness without dropping observations, I use full information maximum likelihood to compute the covariance matrix used in factor analyses (Graham 2009) and to estimate composite scores for those in my sample. As a sensitivity check, I also use multiple imputation to account for missingness and estimate composite scores from imputed datasets. Internal reliability estimates for the three composites based on multiply imputed data were acceptable, ranging from 0.66 to 0.76. I also find that scores for individuals’ conservatism of politics, attitudes toward Black individuals and policies promoting racial equity, and support for protecting racist speech estimated using full information maximum likelihood predict scores from imputed data almost one-to-one.

I leverage data from several other sources collected prior to the 1954 Brown v. Board decision to characterize the counties and school districts in my analytic sample. Data from the 1950 Decennial Census provide county-level details on demographics and socioeconomic outcomes. I augment this data with county-level information on U.S. presidential voting in the 1952 election from Dave Leip's (2016) Atlas of U.S. Presidential Elections.

To further explore mechanisms behind any observed effects of integration on racial attitudes and politics, I use district-level data linked to U.S. counties from the Office of Civil Rights (OCR) surveys, which were administered to school districts across the country beginning in the 1960s.⁶ I specifically focus on measures of district-level school segregation and the proportion of districts’ students that are White. With these data I investigate whether major desegregation plans “worked” and, if so, the extent to which they worked (i.e., the magnitude of the decrease in racial isolation across schools and/or White disenrollment following integration). My preferred measure of school segregation is the White–Black exposure index, which captures the proportion of Black students in the average White student's school. Another commonly studied measure, the dissimilarity index, is less appropriate to test theories of intergroup contact because of its specific focus on how evenly groups are distributed across schools.

Finally, I leverage mobility information in the 1980 Decennial Census. As I describe in more detail below, I specifically explore with this data the sensitivity of results to individuals’ migration decisions (potentially) resulting from court mandates for school integration by race.

To identify the impact of desegregation on White individuals’ racial attitudes and politics in adulthood, I analyze these outcomes for respondents from 342 U.S. counties represented in the GSS. Seventy-four of these counties contain seventy-seven school districts of interest that implemented major school integration plans between 1960 and 1990 following a court mandate (Welch and Light 1987). Several prior studies have investigated the effects of integration in these contexts (e.g., Chin 2021; Guryan 2004; Reber 2005). Furthermore, these districts were sampled for targeted analyses in the past because they represented a substantial proportion of school enrollment—especially of youth from racially minoritized backgrounds—in the United States at the time of measurement (Welch and Light 1987). Finally, I focus on these districts because they are among the largest in the country, which helps to ensure that the geographic level at which integration efforts occur (at the district level and not the county level) is less of a concern for analyses. In online appendix table A2 and appendix figure A1, I identify these districts, their counties, and the years of their earliest major plans, which are compiled by Welch and Light (1987). When a county comprises multiple integrating districts, in analyses I focus on the earliest year of integration.

The other 268 counties I analyze are “comparison” counties where districts were never mandated by court orders to integrate. To identify these counties, I link districts to counties using the OCR survey data and cross-reference these data to the most comprehensive list of districts ever under court mandate, collated by ProPublica (2017) (see also Fiel and Zhang 2019).

Among the White GSS respondents in these sample counties, I restrict the sample further. First, I exclude the extremely small proportion of individuals missing data on age, which I use in combination with survey year to identify exposure to desegregated schools. Second, in main analyses I focus on respondents that currently live in the same city as they did at the age of 16. Investigations of the impacts of school integration on long-term outcomes often cannot fully address potential bias resulting from the mobility of individuals over time (i.e., movement into or away from counties with desegregating schools) due to reliance on cross-sectional data (e.g., Gordon and Reber 2018; Shen 2018). By including just those who report living in the same city at a school-going age, I thus hope to assuage serious concerns of in-migration biasing my results.

Finally, to distinguish samples of GSS respondents who were not exposed to school desegregation, I focus on those who turned 18 in the year of their county of residence's first major integration plan or during the 11 years leading up to implementation; exposed White adults are conversely those who turned 18 up to 12 years after these major efforts to reduce racial isolation occurred. For those living in comparison counties, I similarly consider only those who turned 18 “within $±$12” years of any sample county's earliest integration efforts (i.e., school desegregation occurring from 1961 through 1982, see online appendix table A2; in the empirical strategy section below, I describe how I further constrain this sample of comparison GSS respondents to those who specifically turned 18 within $±$12 years of a referent county's integration year). This restriction reflects my preference to compare the racial attitudes and politics of individuals who are relatively closer in age but differentially exposed to desegregated schools, as they may be more similar on unobservable characteristics. In tests of the robustness of results, I further restrict my sample's age range to strengthen this assumption.

Because the GSS is nationally representative, the respondent count within any given county may concern some. However, of the desegregating counties, twenty-six have 10 to 19 respondents, nine have 20 to 29, and seven have 30 plus across surveys. In the average desegregating county, 59 percent of respondents are exposed to racially integrated schools, ensuring sufficient variation in the “treatment” variable of interest. This translates to approximately 6.31 unexposed (median of 4) and 8.91 exposed (median of 7) White respondents on average per integrating county; for comparison counties these averages are 4.24 (median of 3) and 5.37 (median of 4), respectively (for a similar county-level study in education using nationally representative data with comparable sample sizes, see Thompson 2018).

In table 1, I provide baseline summary statistics for the counties and GSS respondents in my analytic sample, split by desegregation status.

From the table, I conclude that desegregating and comparison observations vary significantly from one another at baseline. For example, comparison counties are less populated, Whiter, and less urban. They are also less Democratic and experience less unemployment despite lower levels of median household income. These patterns for socioeconomic outcomes are reflected in the individual-level comparisons as well. Baseline equivalence between desegregating and comparison counties is not necessary to draw causal conclusions because I use a difference-in-differences approach. However, to help address this imbalance, in all regression models I use inverse propensity score weighting (IPW) to account for observable differences that influence the likelihood that schools in a county were mandated by courts to racially integrate. To arrive at the weights, I use the county-level socioeconomic and demographic measures in table 1 to predict propensity scores and maintain a weight of 1 for desegregating contexts to estimate average treatment effects on the treated (see also Rosinger 2019). Notably, the table depicts that utilizing IPW substantially improves the balance between treatment and comparison observations and greatly attenuates the magnitude of even the significant differences.⁷

To identify the causal impact of school desegregation on White individuals’ racial attitudes and politics in adulthood, I use a difference-in-differences (DID) approach. For the first difference, I compare outcomes between those living in the same county but, based on age and time of major desegregation plan implementation, experience credibly exogenous differences in exposure to integration. Specifically, I identify those who turn 18 after the year of their county's earliest plan to be exposed and those who turn 18 the year of or earlier (i.e., no longer of traditional K–2 school age) to not be exposed. For the second difference, I compare the outcomes of GSS respondents living in desegregating counties to those living in comparison counties who turned 18 in the same year. The first difference thus accounts for persistent contextual differences in racial attitudes and politics among White adults, whereas the second difference accounts for contemporaneous shifts in outcomes over time across age cohorts. Notably, with my particular DID approach (i.e., a “stacked” difference-in-differences; see Baker, Larcker, and Wang 2022; Cengiz et al. 2019; Chin 2021; Deshpande and Li 2019), I never use counties that have already integrated as comparison observations for other integrating contexts. This restriction, also commonly used in synthetic control strategies (Abadie, Diamond, and Hainmueler 2010), ensures that estimates are robust to concerns of bias raised by recent advances in the literature on DID (Goodman-Bacon 2021).

The main coefficient of interest is $γ$⁠, which captures for counties with desegregating school districts the relationship between the outcome and a dichotomous variable that indicates whether the year that the White GSS respondent turned 18, $t$⁠, occurred after the implementation year, $Tj*$⁠, of the earliest integration plan for districts in the desegregating county in the dataset. The regression coefficient $β$ captures this same relationship for those in the same age 18 cohorts, $t$⁠, but who live in comparison counties in the dataset. As noted above, I restrict my analytic sample based on age, including only GSS respondents whose age 18 cohort year is specifically within $±$12 years of the year of the earliest integration effort for the referent desegregating county of the unique stacked dataset, namely, ${(t-Tj*)∈Z∣-11≤(t-Tj*)≤12}$⁠. Finally, I do not include a main effect for living in a desegregating county, $Desegj$⁠, as variation in this variable is subsumed by the county fixed effects, $δj$⁠.

In addition to the event study findings, I show in sensitivity tests below that my DID results are robust when I restrict my sample to GSS respondents whose age 18 cohort year is within $±$8 or $±$4 years (instead of within $±$12 years, my preferred analytic sample) of the earliest implementation year of major integration plans for the referent desegregating county in each stacked dataset. This increases the likelihood of similarity on unobservable characteristics for analyzed cohorts and reduces the chance that any observed DID impacts for integration capture pre-trends across cohorts. I then show that results are robust when I slightly weaken the parallel trends assumption. Specifically, I estimate the model represented by equation 1 above but additionally include a linear age 18 cohort variable interacted with county fixed effects. That findings remain remarkably similar across tests—in addition to extensive prior evidence of parallel trends for other outcomes in DID papers investigating the same integrating districts I consider (e.g., Chin 2021; Reber 2005; Shen 2018)—supports the credibility of my DID results.

For all my analyses investigating the impact of school desegregation on White individuals’ racial attitudes and politics in adulthood, I investigate whether results vary by geographic region. Specifically, I estimate the models represented by equations 1 and 2 but interact exposure to integration variables with a dichotomous variable indicating if the desegregating county in the stacked dataset is located in the U.S. South, based on Census designation.¹⁰ I investigate geographic heterogeneity because, as laid out clearly by Shen (2018), how Black and White students were educated prior to the era of racial school desegregation—and, consequently, how integration unfolded—varied substantially across regions. For example, the U.S. South exhibited higher levels of segregation at baseline and, unlike in other parts of the United States, Black and White students were separated by law. One recent study also found positive impacts of integration on Black students’ adulthood outcomes but only in the South (Anstreicher, Fletcher, and Thompson 2022), with the authors theorizing that differential resistance among White stakeholders to desegregation efforts may explain heterogeneity across regions.

All results discussed in this section, unless otherwise noted, come from regressions that use IPW. I first describe my main results for the impact of integration on White individuals’ racial attitudes and politics as adults. In table 2, I present coefficient estimates from estimation of the model represented by equation 1 with the three GSS composite scores—political conservatism, having a positive attitude toward Black individuals and policies that promote racial equity, and support for protecting racist speech—as outcomes of the model. I focus on impacts for GSS respondents who lived in desegregating counties and were still school-aged when the first major integration plan was implemented for their district.

I find that school integration by race only had an overall effect on White individuals’ politics in adulthood. Those exposed to desegregation on average were 0.12 SD less conservative and scored 0.03 SD higher on the composite capturing positive racial attitudes. Further, there was no difference in support for protecting racist speech between those exposed and not exposed. Only for the point estimate on the first composite can I reject the null hypothesis that average impacts of integration are zero.

However, the table also depicts substantial heterogeneity in the effects of historical desegregation on outcomes by geography. Specifically, I find that White adults in the U.S. South experienced significant decreases in conservatism when exposed to integration in contrast to small, insignificant shifts in conservatism for those in other geographic regions. Efforts to reduce racial isolation across schools lowered conservatism by 0.35 SD in the South and by 0.0032 SD in non-Southern counties. The difference in these point estimates is statistically significant $(p<.01)$⁠. I observe a similar statistical pattern when focusing on the composite score capturing White individuals’ positive attitudes toward Black individuals and policies that promote racial equity. Impacts on this measure are positive in the South and slightly negative elsewhere, though the U.S. South–specific estimates and geographic differences are smaller relative to those documented for conservatism. Finally, I observe no clear evidence of impact heterogeneity for integration on individuals’ support for protecting racist speech.^11,12,13

Because there is no obvious benchmark in the literature for the specific composites in my analyses, interpreting the magnitude of these impacts of integration is challenging. Thus, to facilitate understanding, I focus on the impact of desegregation on more transparent items of the composites. For example, when I estimate the model represented by equation 1 but include as my outcome whether the GSS respondent voted (or intended to vote) for the Democratic candidate in the most recent presidential election, I find that those who were exposed to schools desegregating by race in the south were 18.34 percentage points more likely to have voted for the Democratic candidate. Analogously, I find that integration increased White adults’ propensity to dismiss problematic cultural explanations for Black–White inequality by 16.47 percentage points in the U.S. South. In contrast, I estimate no meaningful shifts for these more intelligible outcomes for treated GSS respondents in non-Southern counties.

Prior research (Baum-Snow and Lutz 2011; Reber 2005; Welch and Light 1987) as well as results presented below (table 5) document shifting migration patterns for White individuals in districts affected by court-mandated school integration. These historical trends highlight the importance of this study's focus on the politics and racial attitudes of White GSS respondents who report living in the same city at age 16 and at the time when surveyed. Without this sample restriction, analysis of the cross-sectional survey data might result in, for example, the inclusion of those who moved into a desegregating context after a court order was passed down—and, subsequently, potential misattribution of the direct effect of efforts to reduce racial isolation across schools on outcomes. Importantly, if these respondents were included and in-mobility was nonrandom, for example, if more liberal White adults with positive racial attitudes self-selected into treated counties, impact estimates from the main specification could be spurious.

In table 3, I thus present findings from analyses that further explore potential issues with the primary DID specification related to mobility in counties where schools integrated by race.

In panel A, I investigate the inclusion of additional GSS respondents and their data in analyses. I specifically add to the sample those who indicate living in a desegregating county as adults but identify as living in the same state but not the same city at school age. I then reestimate the DID model represented by equation 1, but for these new respondents I replace the indicator variable in the equation, $Desegj$⁠, with the county-level proportion of White 21-year-olds reporting as living in either the same house or the same county as 16-year-olds,¹⁴ based on information from the 1980 Decennial Census. (For all details on the construction of county-level proportions using the 1980 Decennial Census, see online appendix D.) In other words, I do not alter how treatment is defined for the (immobile) individuals in the original sample, but for the supplemental sample of individuals reporting migration since 16, I assign treatment based on the population-wide likelihood that mobile individuals lived in the treated context at school age.

I perform this migration robustness check because of how GSS interviewers were instructed to query individuals about mobility and because city and district boundaries are not necessarily coterminous. When asking respondents on changes in residence since school age, interviewers are given more specific interview instructions based on the urbanicity of where the conversation is taking place. Specifically, though the data only denote if a respondent currently lives in the same city that they did at the age of 16, interviewers are told to ask about living in the same “town” or “county” when interviewing in a town or more rural area, respectively. Because I assign exposure to court mandates to desegregate schools by race at the county level, this does not impact correct assignment of treatment for those in the main analytic sample. However, this language does suggest that some individuals—especially those living in urban centers—may report being mobile from school age but still live in the same county and should still be considered as treated. I thus retain (and assign a treatment dosage to) in analyses here the individuals who may have moved across city lines in integrating contexts but who also remained in the same school district. The main conclusions do not change.¹⁵

In panel B, I conduct this same exercise (as panel A) by adding to the sample those who indicate living in a desegregating context as adults but identify as living in the same state but not the same city at school age. I then additionally consider White GSS respondents residing in the same labor market area (LMA) where a district was mandated by courts to integrate to be exposed to treatment. In LMAs with multiple desegregating agencies, I identify treatment based on the year of earliest implementation of a major plan to reduce racial isolation across schools. I do not change the status of individuals living in non-integrating contexts unless their county of residence falls into a newly treated LMA. I then reestimate the DID model represented by equation 1, but for the supplemental sample of respondents I replace the indicator variable in the equation, $Desegj$⁠: for those living in the same county as a desegregating district as adults but who moved cities, the county-level proportion of White 21 year olds reporting as living in either the same house or the same county as 16-year-olds; for those who moved cities and are living in the same LMA but not county of a desegregating district as an adult, the county-level proportion of White 21-one-year-olds reporting as living in a desegregating county in the LMA at 16 years old. Both values are based on information from the 1980 Decennial Census. Put differently, I again do not alter how treatment is defined for the (immobile) individuals in the original sample. But for the mobile sample, I assign treatment based on the likelihood of having lived in a treated context at school age. Despite this substantial shift in the analytic sample and DID model, results in panel B mirror the main findings qualitatively, as I observe that desegregation continues to significantly decrease the conservatism of White individuals in adulthood, but only in the U.S. South (albeit at a slightly attenuated magnitude).

This second migration robustness check solves the aforementioned issues tied to interviewer instructions and non-coterminous boundaries between cities and districts, and also retains (and assigns a treatment dosage to) respondents who may have been enrolled in integrating districts but who migrated to nearby locales as adults. By including these individuals, I hope to assuage concerns that my main findings result not from the impact of desegregation per se, but from the out-mobility of more conservative White individuals with less positive racial attitudes from contexts that faced court-mandated integration. Furthermore, by assigning treatment to adults living in nontreated counties but where other counties in the same LMA made efforts to reduce racial isolation across schools, the estimates presented in panel B of table 3 may be seen as lower bounds for treatment effects. Specifically, in addition to accounting for potential systematic out-migration in impact estimates, this sensitivity likely expands measurement error in treatment assignment, as some of those living in counties never exposed to court mandates as adults may never have been exposed in reality.¹⁶

I next provide additional evidence supporting the robustness of my DID findings for the impact of school desegregation on White individuals’ racial attitudes and politics as adults.

In table 4, I present the coefficient estimates resulting from variants of the model represented by equation 1, again with the three GSS composite scores as outcomes. In panels A and B, I test whether the results in table 2 hold after changing the sample of White GSS respondents included in my sample. Specifically, in my preferred specification, I focus on those who turned 18 within $±$12 years of the earliest implementation year of major integration plans for desegregating counties. When I restrict this age range further—to include only those who turned 18 within $±$8 of $±$4 years integration—and reestimate my models, results remain qualitatively the same. Those in the South exposed to school integration by race are significantly less conservative and more likely to hold positive attitudes toward Black individuals and policies that promote racial equity. These causal effects are more attenuated for those living elsewhere in the United States though still in the same direction. I also continue to observe no impact of efforts to reduce racial isolation on individuals’ support for the protection of racist speech. The findings in panels A and B in table 3 thus suggest that my results are consistent when I compare the racial attitudes and politics for a narrower range of birth cohorts, which increases the likelihood of similarity on unobservable characteristics for analyzed cohorts and reduces the chance that any observed DID impacts for integration are capturing pre-trends across cohorts.¹⁷

In panel C of table 4, I document further evidence of the robustness of my main findings. In this panel, I provide the coefficient estimates resulting from the model represented by equation 1, but additionally interact county fixed effects with a linear term for the age 18 cohort. The inclusion of these interactions results in a conservative specification that can disentangle potential impacts of integration from underlying cohort trends in racial attitudes and politics within county. But even with these controls I continue to find the same result. White individuals exposed to integrated schools are less conservative and hold more positive racial attitudes as adults, and these effects are stronger in magnitude for those living in the U.S. South.

In panel D of table 4, I report impacts after restricting analyses just to the counties with desegregating school districts. I conduct this sensitivity test because, as shown in table 1, there may be some concern over the systematic baseline differences for integrating districts even after using IPW (though baseline equivalence is not a necessary condition to recover causal estimates using DID). I specifically contrast GSS respondents in each county exposed to integration mandates only to those from other counties that eventually received mandates in the future. This empirical approach notably mirrors more closely those used in prior studies (Gordon and Reber 2018; Reber 2005; Shen 2018). I continue to find the same pattern as my main results when I focus on respondents who turned 18 within $±$8 years of the earliest implementation year of major integration plans for desegregating counties and difference out contemporaneous trends observed in counties that desegregate at least eight years later.¹⁸

In table 5, I present results from an exploratory investigation of potential mechanisms explaining why I observe greater effects of integration for White individuals in the U.S. South. I test two primary mechanisms. First, I identify the extent to which efforts to reduce racial isolation across schools worked. Second, I consider whether integration affected White individuals’ socioeconomic outcomes as adults. This latter investigation also serves as a placebo test for my DID approach—that is, if socioeconomic outcomes changed for White individuals exposed to integration, it might signal some other policy occurring concurrently with school desegregation leading to shifts in racial attitudes and politics as well.

I first find that school integration worked “better” in the U.S. South, which might explain the stronger effects on White individuals’ racial attitudes and politics. The White–Black Exposure index in desegregating districts in the South increased by 0.15; elsewhere it increased by 0.12 (table 5). In layman's terms, integration expanded as a result of court orders, as the average White student in the South attended a school that served a student population with 15 percentage points more Black students after the mandates. Overall, these results closely mirror those seen in prior studies (Reber 2005). However, the difference between the regression coefficient for the impact of desegregation in the South is not statistically significant from the same coefficient for non-Southern contexts (⁠$p≈.25$⁠). In contrast, geographic heterogeneity is statistically significant when considering the effect of integration on the district-level percent enrollment of White students. Districts in the U.S. South saw significantly less White disenrollment following integration, further suggesting that White individuals who were exposed to less racially isolated schools were more likely to experience White–Black contact as a result.

Conversely, I find weaker evidence that the greater decreases in political conservatism and increases in positive attitudes toward Black individuals and policies that promote racial equity could be driven by relatively more competitive labor market for White adults in the U.S. South as compared to other regions. In fact, I show that White adults exposed to integrating schools in the U.S. South on average attained approximately half a year more of education, though no significant difference emerged for achieving an educational attainment of high school or above (see Guryan 2004). Finally, I observe no commensurate impacts of education on GSS respondents’ income or perceptions of class, nor do I observe any significant geographic heterogeneity for impacts across measures of socioeconomic success.

Court-mandated desegregation of schools by race starting in the 1950s left an indelible impact on education in the United States. Research largely finds that these changes improved the life outcomes of Black youth across the country (Anstreicher, Fletcher, and Thompson 2022; Guryan 2004; Johnson 2011). But stubborn resistance to integration over the decades, primarily by White families, and judicial precedent eventually slowed and even reversed the rate of desegregation (Reardon and Owens 2014).

In recent years, school integration by race has yet again become a topic of conversation in education policy circles. Given its largely positive effects on the educational and socioeconomic outcomes of Black youth and its potential importance in the moral and character development of White youth, this interest is unsurprising. However, some research also finds negative unintended consequences resulting from desegregation. Because other educational interventions have helped advance equity, without additional evidence of integration's positive contributions, it may be more politically (and legally) feasible to pursue these other programs.

But integration advocates have long cited its unique potential to improve the racial attitudes of White youth, as contact theory broadly predicts (Allport 1954). These theoretical changes can have major implications for the long-term opportunities of Black individuals across the United States. However, limited causal evidence exists that supports advocates’ views, and the necessary conditions for successful White–Black interaction stipulated by the contact hypothesis suggest that negative attitudinal shifts appear just as applicable.

In this study, I address this limitation of existing research by leveraging a credibly causal design, in combination with nationwide data on White individuals’ racial attitudes and politics, to identify these theoretical benefits of integration. I find evidence that though historical court-mandated school integration by race did positively affect racial attitudes (and the political views that tend to correlate with these attitudes) on average across the country, significant heterogeneity exists. Specifically, White individuals exposed to desegregated schools in the U.S. South exhibit in adulthood weaker conservative politics, and more positive attitudes toward Black individuals and policies promoting racial equity. I find suggestive evidence that stronger positive effects of reduced racial isolation in the South may stem from more effective desegregation plans, namely, those that led to relatively larger increases in White–Black exposure in public schools and smaller decreases in White public school enrollment. Divergences in the effectiveness of these plans may themselves proxy for heterogeneity across contexts in terms of resistance to integrative efforts. My findings thus converge with the most relevant studies to my work, which are conducted by Billings and colleagues (2021) in Charlotte-Mecklenburg in North Carolina and Kaplan and colleagues (2021) in Jefferson County in Kentucky. These authors find that exposure to more racially diverse schools decreased the propensity for White youth to register as Republicans in adulthood.

Any investigation of how substantial school reforms affect individuals’ outcomes measured decades later is subject to limitations. Studies on the long-term impacts of historical efforts to reduce racial isolation across schools following Brown v. Board are no different. For example, one of the most pressing concerns is that the richest dataset available to explore racial attitudes and proxies for attitudes in the present day—the GSS—is not collected for the same individuals longitudinally. My study is generally able to address this issue by focusing in main analyses only on data from GSS respondents that report living in the same city in both adulthood and in their teenage years. Furthermore, results remain qualitatively similar when exploring migration potentially tied to efforts to reduce racial isolation across schools. Yet by restricting my analytic sample to nationwide data collected from a subset of GSS respondents, I cannot leverage (arguably) more rigorous methodological approaches to assess the impacts of desegregation on White individuals’ racial attitudes and politics in adulthood. Specifically, I cannot estimate precisely event study models that would allow me to predict the impact of reduced racial isolation on individual cohorts of White youth exposed to integrated schools.

Finally, the generalizability of study may be limited geographically and temporally. Though I investigate the impacts of efforts to reduce racial isolation across schools in the largest districts across the country, how these efforts translate to shifts in racial attitudes may vary in contexts that are dissimilar to the seventy-seven focal districts of my study. Furthermore, the educational landscape in the decades leading up to and following the Brown v. Board decision is substantially different from the present landscape. As such, whether my results will replicate in districts currently pursuing desegregation is uncertain. With increasingly racially homogenous school districts and schools, and with between-district school segregation accounting for more and more of the overall observed racial isolation, integrative efforts may be less effective at actually expanding outgroup contact by race.

Future research should thus investigate how contemporary school desegregation policies impact the long-term racial attitudes of White youth. Because the demographics of students attending U.S. public elementary and secondary schools are changing, this work should also test how White individuals’ attitudes toward other groups are changing. My study, for example, cannot test whether school desegregation might be able to remedy prejudice toward Hispanic or Asian individuals—the largest growing populations in the country. Furthermore, because the GSS sample is composed predominantly of White respondents, I cannot investigate how the politics and attitudes of Black youth (or youth from other racial/ethnic backgrounds) change in integrated settings—something that psychological theories would also predict.

With these important caveats in mind, how should policy makers currently interested in reducing racial isolation across schools leverage the findings of my study? It is clear that the context in which desegregation occurs matters for how the policy change can impact racial attitudes. I find strong positive effects of historical integration in the U.S. South but not elsewhere. I argue that my exploratory analyses on mechanisms suggest this heterogeneity because desegregation was more effective in the South. As such, if new policies are only marginally effective—or counteracted by other within-school sorting of students by race (e.g., tracking)—the positive attitudinal effects I observe may not be realized. Furthermore, I would encourage school and district leaders to heed Allport's (1954) original concerns that increasing White–Black contact in schools might actually exacerbate negative outgroup prejudices if not pursued intentionally and with stakeholder support.

School integration has worked to improve racial equity in the past and it can do so again. Given the social and legal barriers to reducing racial isolation, policy makers should of course continue to explore adopting educational programs that improve the outcomes of Black youth but are prima facie neutral on how they change the racial composition of schools. But desegregation's theoretical effects on improving intergroup relations did accrue in certain contexts following Brown v. Board. The potential benefits of integrated schools to support the development of youth's attitudinal outcomes and, subsequently, their ability to engage in a diverse, multiethnic society thus compels leaders to identify how best to foster integrated spaces in education.

I thank Nora Gordon and Sarah Reber for making the Office of Civil Rights survey data available, and to Desmond Ang, Peter Blair, Sarah Cohodes, David Deming, Li Feng, Dan Kreisman, Stephen Ross, Randall Reback, Eric Taylor, Martin West, several anonymous referees, and conference participants at AEFP, AERA, and APPAM for valuable feedback. The research reported here was supported in part by the Institute of Education Sciences, U.S. Department of Education, through grant R305B150010 for the Partnering in Education Research Fellowship in collaboration with the Center for Education Policy Research at Harvard University. The opinions expressed are those of the author and do not represent the views of the Institute or the U.S. Department of Education. All errors are my own.