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NBER WORKING PAPER SERIES LONG-RUN IMPACTS OF SCHOOL DESEGREGATION & SCHOOL QUALITY ON ADULT ATTAINMENTS Rucker C. Johnson Working Paper 16664 NATIONAL BUREAU OF ECONOMIC RESEARCH 1050 Massachusetts Avenue Cambridge, MA 02138 January 2011 Revised August 2015 I wish to thank John Logan (Brown University, American Communities Project) for sharing data on school desegregation court cases, Sarah Reber for sharing the Office of Civil Rights school data, and the PSID staff for access to the confidential restricted-use PSID geocode data.
I am grateful for detailed comments received from David Card, Sheldon Danziger, several anonymous referees, and seminar participants at the NBER labor studies meetings, IRP Summer Workshop (University of Wisconsin-Madison), UC-Berkeley, University of Chicago, University of Michigan, Stanford University, Northwestern, NYU, Yale, Duke, University of North Carolina, University of Minnesota, Wellesley College, Chicago Federal Reserve Bank, Russell Sage Foundation, ASSA/AEA annual conference, Midwest Economics Association meetings, and APPAM annual conference.
The views expressed herein are those of the author and do not necessarily reflect the views of the National Bureau of Economic Research.

© 2011 by Rucker C. Johnson.

All rights reserved.

Short sections of text, not to exceed two paragraphs, may be quoted without explicit permission provided that full credit, including © notice, is given to the source.

Long-run Impacts of School Desegregation & School Quality on Adult Attainments Rucker C. Johnson NBER Working Paper No.
16664 January 2011, Revised August 2015 JEL No.

I00,I21,I28,J15 ABSTRACT This paper investigates the long-run impacts of court-ordered school desegregation on an array of adult socioeconomic and health outcomes.

The study analyzes the life trajectories of children born between 1945 and 1968, and followed through 2013, using the Panel Study of Income Dynamics (PSID).
The PSID data are linked with multiple data sources that describe the neighborhood attributes, school quality resources, and coincident policies that prevailed at the time these children were growing up.

I exploit quasi-random variation in the timing of initial court orders, which generated differences in the timing and scope of the implementation of desegregation plans during the 1960s, 70s, and 80s.
Event study analyses as well as 2SLS and sibling-difference estimates indicate that school desegregation and the accompanied increases in school quality resulted in significant improvements in adult attainments for blacks.
I find that, for blacks, school desegregation significantly increased both educational and occupational attainments, college quality and adult earnings, reduced the probability of incarceration, and improved adult health status; desegregation had no effects on whites across each of these outcomes.
The results suggest that the mechanisms through which school desegregation led to beneficial adult attainment outcomes for blacks include improvement in access to school resources reflected in reductions in class size and increases in per-pupil spending.

Rucker C. Johnson Goldman School of Public Policy University of California, Berkeley 2607 Hearst Avenue Berkeley, CA 94720-7320 and NBER ruckerj@berkeley.edu I.
INTRODUCTION Racial segregation that results in race differences in access to school quality has often been cited as perpetuating inequality in attainment outcomes.

Since the landmark 1954 Supreme Court Brown v. Board of Education decision and subsequent court-ordered implementation of school desegregation plans during the 1960s, 70s and 80s, scholars have investigated the consequences of school desegregation on socioeconomic attainment outcomes of black children (Clotfelter, 2004; Rivkin & Welch, 2006).
However, few large-scale data collection efforts were undertaken to investigate school desegregation program effects, particularly on longer-run outcomes.

A recent, but growing body of evidence indicates that school desegregation improved black students’ educational attainment (Guryan, 2004; Reber, 2010; Hanushek et al., 2009), increased blacks’ subsequent adult incomes (Ashenfelter et al., 2005), and decreased rates of criminal offending by black youth (Weiner, Lutz, Ludwig, 2009).
This paper contributes to the literature a unified evaluation of the long-run impacts of school desegregation on adult outcomes across several domains using a more compelling research design and more comprehensive data.

I investigate the extent and mechanisms by which school desegregation and resultant changes in school inputs causally influence subsequent adult socioeconomic and health outcomes.
The primary difficulty in disentangling the relative importance of childhood family, neighborhood, and school quality factors is isolating variation in school quality characteristics that are unrelated to family and neighborhood factors.

This study analyzes the life trajectories of children who were born between 1945 and 1968 and have been followed through 2013, using the longest-running US nationally-representative longitudinal data spanning more than four decades.
To this data, I link information from multiple data sources that contain detailed neighborhood attributes, school quality resources, and coincident policies that prevailed at the time these children were growing up.
I also obtained and linked a comprehensive desegregation case inventory for the years between 1954 and 1990 that contains detailed information for every US school district that implemented a court-ordered desegregation plan, the year of the initial court order, and 1 the type of desegregation court order.1 The implementation of court-ordered school desegregation during the childhoods of these birth cohorts provides a unique opportunity to evaluate their long-run impacts.
The analysis is presented in two stages.

First, I present new evidence of how court-ordered school desegregation influenced the quantity and quality of educational inputs received by minority children.

Utilizing an event-study research design with both district-level and school-level data, the primary empirical strategy exploits quasi-random variation in the timing of initial court orders to identify effects.
I find that desegregation plans were effective in narrowing black-white gaps in per-pupil school spending and class size and decreasing school segregation.

Second, I investigate the long-run impacts of court- ordered desegregation on subsequent attainment outcomes, including whether graduated from high school, years of completed education, college quality, adult earnings and occupational attainment, income and poverty status, probability of incarceration, and adult health status.
I estimate fully non-parametric event study models and use the wide variation in the timing of initial court orders and scope of desegregation to identify their effects.

School desegregation and the accompanied increases in school quality resulted in significant improvements in adult attainments for blacks.
I find that, for blacks, school desegregation significantly increased both educational and occupational attainments, college quality and adult earnings, reduced the probability of incarceration, and improved adult health status; desegregation had no effects on whites across each of these outcomes.
In order to attempt to identify the potential mechanisms, I analyze the role of desegregation-induced changes in per-pupil spending and racial school integration, respectively, independent of district-specific trends and other coincident policies.

Changes in per-pupil spending and racial integration resultant from court-ordered desegregation are interpreted as markers for the intensity of treatment.
I find that blacks’ adult attainments increased significantly with both the amount of induced increase in school spending and the duration of desegregation exposure, with no apparent dose-response in the amount of racial integration resultant from court orders.

Desegregation had no effects on whites’ adult outcomes, in neither the duration of exposure nor the intensity of treatment.
The results suggest that the mechanisms through which school desegregation led to beneficial adult attainment outcomes for 2 blacks include improvement in access to school resources reflected in reductions in class size and increases in per-pupil spending.

As an alternative empirical strategy, I use sibling comparisons to identify the effects of school desegregation on adult socioeconomic and health outcomes.
This identification strategy compares the adult outcomes of individuals who were exposed to integrated schools during childhood with the corresponding adult outcomes of their siblings (evaluated at the same age) who grew up in the same communities but had already reached age 18 prior to desegregation or were exposed to integrated schools for only a limited period of their childhood, conditional on year of birth effects.
The pattern of results is similar across all of the empirical approaches (event study models, 2SLS and sibling fixed effect models), and reveals significant long-run impacts of school desegregation and school quality on a broad range of adult outcomes.

The results are robust to a battery of specification tests, which provides supportive evidence that the estimates reflect the causal impacts of school desegregation and school quality.
As evidenced herein, the black-white adult socioeconomic and health disparities gap narrowed for the cohorts exposed to integrated schools during childhood.
The empirical analysis builds on and extends the literature by investigating (1) non-racial integration aspects of court-ordered desegregation through its impacts on per-pupil spending; (2) the effects of court-ordered school desegregation on adult SES and health outcomes while simultaneously accounting for other important coincident policy changes; and (3) the role of childhood school quality in contributing to socioeconomic and racial health disparities in adulthood.
By examining life-course effects of school desegregation across a broad range of subsequent outcomes, I attempt to shed light on the mechanisms through which differences in school quality translate into differences in adult outcomes.

The remainder of the paper is organized as follows.

Section II briefly describes the timing of court-ordered school desegregation.

Section III presents the data used.

Section IV outlines the empirical strategy.


Section Va presents results of the effects of school desegregation on school quality inputs (per- pupil spending; class size; school segregation).

This informs what the typical “treatment” represented for the average black child.

Section Vb presents results of the long-run impacts on adult outcomes.Section VI 3 presents conclusions and summary discussion to put the magnitudes in perspective in relation to previous studies.
All appendix material is in the online appendix.

II.
USING THE TIMING OF COURT-ORDERED DESEGREGATION AS A QUASI-EXPERIMENT It is hypothesized that school desegregation may have long-run impacts on the adult economic and health status of African Americans through several potential mechanisms: (1) school quality resource effects (e.g., the distribution and level of per-pupil spending, class size, teacher quality); (2) peer exposure effects (e.g., children in classrooms with highly motivated and high-achieving students are likely to perform better due to positive spillover effects on other students in the classroom); and (3) effects on parental, teacher, and community-level expectations of child achievement.
The long-run effects of each hypothesized mechanism operate via their influence on the quality and quantity of educational attainment.

I examine the hypothesized primary mechanism: changes in school quality resulting from abrupt shifts in racial school segregation.2 An understanding of the causes of the timing of desegregation is critical to the identification strategy.
Accordingly, Appendix B provides a brief history of school desegregation litigation and implementation with an eye towards identification issues and demonstrating the validity of the research design—namely, the quasi-random timing of initial court orders.
To document the substantial variation in the timing and intensity of school desegregation efforts, I use a comprehensive desegregation case inventory compiled by legal scholars for the years between 1954 and 1990 that contains detailed information for every US school district that implemented a court-ordered desegregation plan, in conjunction with additional data from Welch and Light (1987) on the dates of major desegregation plan implementation for large urban districts.
Figure A1 presents the dates of initial court orders across the country among the 868 school districts ever subject to court-mandated desegregation between 1954 and 1980.

Districts exhibit a great deal of variation in the year in which the initial court order was issued and the subsequent timing when major desegregation plan implementation actually took place; this variation is evidenced both within and across regions of the country (see Appendix Figures A0-A2).
4 Most school districts did not adopt major school desegregation plans until forced to do so by court order (or threat of litigation) due to individual cases filed in local Federal court.

The importance of legal precedent caused the NAACP to strategically bring suits first, and foremost, when and where there was the greatest likelihood of winning, not where the largest potential gains from desegregation could be achieved for a particular local community at a point in time.
Enforcement of desegregation did not begin in earnest until the mid-1960s.

State and federal dollars proved to be the most effective incentives to desegregate the schools.
A critical turning point was the enactment of Title VI of the 1964 Civil Rights Act (CRA) and Title I funds of the 1965 Elementary & Secondary Education Act (ESEA), which prohibited federal aid to segregated schools and allowed the Justice Department to join suits against school districts that were in violation of the Brown vs. Board order to integrate.
This Act dramatically raised the amount of federal aid to education from a few million to more than one billion dollars a year; and, for the first time, the threat of withholding federal funds became a powerful inducement to comply with federal desegregation orders (Cascio et al., 2010; Holland, 2004).

This resulted in a significant drop in the extent of racial school segregation thereafter reinforced by local Federal courts.

Thus, there is a sharp post-1965 discontinuity in school desegregation.
This pattern and discontinuity after 1965 is also evident in the time lag between initial court order and major desegregation plan implementation, which occurs in the South and non-South (Appendix Figure B6).

For initial court orders meted out after 1965, there is immediate implementation (on average, major plan implemented within 1-2 years of initial court order).
On the other hand, for initial court orders meted out before 1965, there is more than a 10-year delay in implementation of a major plan (i.e., there is a systematic long delay that decreases in years leading up to 1965).

Litigation and desegregation plan implementation accelerated substantially between 1964 and 1972.
For example, only 6 percent of the districts that would eventually undergo court-ordered desegregation had implemented major plans by 1968 (when the PSID began); by 1972 this rose to over 56 percent.

It is this period of substantial growth in litigation activity, spurred by landmark court cases like the 1968 Green decision (which required immediate actions to effectively implement desegregation 5 plans), that forms the basis of the research design.
The process became highly decentralized with a diverse set of agents that initiated court litigation following the Brown decision, which contributed to the idiosyncratic nature of the timing and location where legal challenges arose that resulted in initial court orders.
Differences across districts in when desegregation court cases were first filed and the length of time it took these cases to proceed through the judicial system represents a plausibly exogenous source of identifying variation in the timing of school desegregation.

III.
III.

DATA I compiled data on school spending and school segregation, linked them to a comprehensive database of the timing of court-ordered school desegregation, and linked these data to a nationally- representative longitudinal dataset that follows individuals from childhood into adulthood.
Education funding data come from several sources that are combined to form a panel of per-pupil spending for US school districts in 1967 and annually from 1970 through 2000.3 School segregation data come from the Office of Civil Rights (OCR), and are combined to form a panel used to construct school segregation indices that span the period 1968 through 1988.

The school segregation and spending data are then linked to a database of desegregation litigation between 1954 and 2000.
The data on longer-run outcomes come from the Panel Study of Income Dynamics (PSID) that links individuals to their census blocks during childhood.4 The sample consists of PSID sample members born between 1945 and 1968 who have been followed into adulthood through 2013; these individuals were between the ages of 45 and 67 in 2013.

I include all information on them for each wave, 1968 to 2013.5 Due to the oversampling of black and low-income families, 45 percent of the sample is black.
I match the earliest available childhood residential address to the school district boundaries that prevailed in 1969 to avoid complications arising from endogenously changing district boundaries over time.

The algorithm is outlined in Appendix A.

Each record is merged with data on the timing of court- ordered desegregation, data on racial school segregation, student-to-teacher ratios, school spending at the school district level that correspond with the prevailing levels during their school-age years.
Finally, I 6 merge in county characteristics and information on other key policy changes during childhood (e.g., the timing of hospital desegregation, rollout of “War on Poverty” initiatives and expansion of safety net programs—described in Section IV) from multiple data sources.6 This allows for a rich set of controls.
The comprehensive desegregation court case data I use contains an entire case inventory of every school district ever subject to court desegregation orders over the 1955-1990 period (American Communities Project), and major plan implementation dates in large districts (compiled by Welch/Light).

Every court case is coded according to whether it involved segregation of students across schools, whether the court required a desegregation remedy, and the main component of the desegregation plan.
The combined data from the American Communities Project (Brown University) and Welch/Light provide the best available data that have ever been utilized to study this topic for several reasons.
First, the year of the initial court order (available for all districts) is plausibly more exogenous than the exact year in which a major desegregation plan was implemented because opposition groups to integration can delay major desegregation plan implementation by lengthening the court proceedings or by implementing inadequate desegregation plans (supportive evidence on this point is presented in Appendix B).
And, court-ordered desegregation by legal mandate is plausibly more exogenous than other more voluntary forms of desegregation.

Second, the date of the initial court order is precisely measured for all districts.
Sixty-nine percent of the PSID individuals born between 1945-1968 followed into adulthood grew up in a school district that was subject to a desegregation court order sometime between 1954 and 1990 (i.e., 9,156 out of 13,246 individuals), with the timing of the court order not necessarily occurring during their school-age years.
Eighty-eight percent of the PSID black individuals born between 1945- 1968 followed into adulthood grew up in a school district that was subject to a desegregation court order sometime between 1954 and 1990 (i.e., 4,618 out of 5,245 black individuals).

The share of individuals exposed to school desegregation orders during childhood increases significantly with birth year over the 1945-1970 birth cohorts analyzed in the PSID sample (Appendix Figure B5).
After combining information from the aforementioned 5 data sources, the main sample used to analyze adult attainment outcomes consists of PSID individuals born between 1945-1968 originally from 7 school districts that were subject to desegregation court orders sometime between 1954 and 1990; this includes 9,156 individuals from 3,702 childhood families, 645 school districts, 448 counties, representing 39 different states.
I restrict the estimation sample to individuals who grew up in school districts that were ever subject to court-ordered desegregation, since school districts of upbringing that were never under court order are arguably too different to provide a credible comparison group.

Appendix A lists the sources and years of all data elements.

Appendix Table C0 contains sample descriptive statistics for various childhood measures by race.

Outcomes of interest.


The set of school inputs examined include per-pupil spending, student-to- teacher ratios, and racial school segregation among students and teachers.

The measure of school spending during childhood is the average school spending (in real 2000 dollars) during expected school- age years (ages 5 through 17) in an individual’s childhood school district.7 Similarly, I measure the average student-to-teacher ratio during ages 5 through 17.
The measures of racial school segregation include the average school-age black-white dissimilarity index and black-white exposure index among both students and teachers, respectively.
The set of adult attainments examined chronologically over the life cycle include 1) educational outcomes—whether graduated from high school, years of completed education, college quality (proxied by 25th and 75th percentiles of SAT scores of the freshman class of college attended); 2) labor market and economic status outcomes (all expressed in real 2000 dollars)— occupational attainment (Duncan occupational prestige index), log wages, annual work hours, family income, annual incidence of poverty in adulthood (ages 20-50); 3) criminal involvement and incarceration outcomes—whether ever incarcerated (jail or prison) and the annual incidence of incarceration in adulthood; and 4) health outcomes—self-assessed general health status and the annual incidence of problematic health (ages 20-50).
All analyses include men and women with controls for gender, given well-known gender differences in labor market, incarceration, and health outcomes.

This data is combined to provide new evidence on the long-run impacts of school desegregation.

8 IV.

EMPIRICAL APPROACH The primary empirical strategy uses quasi-random variation in the timing of initial court orders to identify the effects of desegregation.
Systematic variation in the timing of desegregation court orders could lead to spurious estimates of desegregation impacts if those same school district characteristics are associated with differential trends in the outcomes of interest.

As shown below, the main way I test for this possibility is to use an event study model, which reveals no significant pre-existing time trends in the outcomes of interest.
The exogeneity of this timing is supported theoretically by the documented legal history of school desegregation and by my own empirical examination of the issue.

Table B1 also shows that collectively the bulk of pre-treatment school quality, SES, demographic, and labor market related characteristics does not significantly (jointly) predict the year of the initial court order (Appendix B).
On the other hand, I find that districts with a larger minority population, greater per-capita school spending, and smaller proportion of residents with low income are each strongly associated with longer delays in major desegregation implementation following the initial court order.

These results suggest that the timing of initial court litigation is more plausibly exogenous than the timing of major desegregation plan implementation.
These findings inform the empirical approach used to identify school desegregation impacts.

Point-in-time comparisons of integrated and segregated school systems confound the effect of desegregation plans with the effect of factors that influenced their implementation.

I match changes in school inputs and adult attainment outcomes of blacks and whites to the exact timing of court-ordered school desegregation.
Average outcome trends in the years leading up to desegregation are compared to rule out competing explanations.

As will be shown, the evidence is consistent with the identifying assumption that the timing of the initial court order is otherwise unrelated to trends in subsequent outcomes.
Evidence of endogenous delays in implementation of major desegregation plans following (exogenous) initial court orders supports the research design’s reliance on the timing of initial court 9 orders for identification, instead of directly using the timing of major desegregation plan implementation as prior studies have (discussed below).
The first stage of the analysis investigates how court-ordered school desegregation influenced the quantity and quality of educational inputs received by minority children.

Following Card and Krueger (1992), I measure school quality as the purchased inputs to a school—per-pupil spending and the student- teacher ratio.

Newly compiled school district-level and school-level panel datasets allow this analysis to use the staggered timing of court-ordered school desegregation within an event study analysis (cf.
Jacobson, LaLonde and Sullivan, 1993; McCrary, 2007) to quantify desegregation effects on school resources.

The event study framework compares school district per-pupil spending, student-to-teacher ratios, and school segregation levels among both students and teachers in the years immediately after court-ordered desegregation to the levels that prevailed in the years immediately before court orders for all districts that were ever subject to court orders.
The second part of the analysis uses the same fully non- parametric event study models to quantify desegregation effects on educational attainment, incarceration, and adult economic and health status outcomes, separately by race.
The analysis sample is restricted to districts that were ever subject to desegregation court orders, since districts that were never subject to court orders differ (e.g., on average, have a small number of minority students) and do not provide a valid counterfactual for the time-path of what would have occurred in the absence of desegregation.

To motivate the empirical strategy, I describe the policy experiment below.
Individuals who turned 17 years old during the initial year of the desegregation court order in their school district should have completed secondary school by the time reforms were enacted.

Such cohorts should be unaffected by desegregation so I classify them as “unexposed”.

In contrast, individuals who turned 16 years old or younger during the year of the passage of a court-ordered desegregation would likely have been attending primary or secondary school when desegregation plans were implemented.
I refer to these cohorts as “exposed”.

One can estimate the exposure effect on school inputs and adult outcomes for blacks and whites from a particular district by comparing the change in outcomes between exposed and unexposed birth cohorts from that district, separately for blacks and whites.
To account for any underlying 10 differences across birth cohorts, one can use the (race-specific) difference in outcomes across the same birth cohorts in districts that had not desegregated during that time as a comparison.
The difference in outcomes between exposed and unexposed black cohorts in a treated district minus the difference in outcomes across the same black birth cohorts in comparison districts yields a Difference-in-Difference (DiD) estimate of the exposure effect on outcomes for blacks from that district.

Similarly, one can obtain a DiD estimate of desegregation exposure effects for whites based on differences between exposed and unexposed white cohorts.
The key identifying assumption is that the timing of initial court orders is otherwise unrelated to within-district changes in outcomes across birth cohorts.
Under this assumption, an additional test of whether there is a causal effect of school desegregation is whether we witness larger improvements in school inputs and adult outcomes for blacks that experienced desegregation exposure for more of their school-age years (i.e., a dose-response effect); and likewise, we can examine exposure- duration effects for whites.
Theoretically, it is hypothesized that for African Americans, attending integrated schools during one’s elementary school years may result in greater benefits than exposure to integrated schools only later in the school careers due to three factors: 1) elementary students may have fewer social adjustments than older students; 2) early learning begets later learning; and 3) secondary schools are more likely to track students by academic ability (and race), which could reduce benefits of desegregation for minorities.
For these reasons, we may expect a dose-response effect of school desegregation exposure (and accompanied improvements in school quality).
I estimate fully non-parametric event study models of the form: (1) Y idb   X idb 1   r  T T 20    Z  I T idb  T   I T idb  T   I T idb  T   ( W 1960 db T r )   g   r d r b r * b   idb 12 T  r  T 1   b d 20  r  T 13  where i indexes the individual, d the school district, b the year of birth, g the region of birth (defined by 9 census division categories), and r the racial group.
The variable Tidb is the year individual i from school district d turned age 17 minus the year of the initial desegregation court order in school district d. 11 Accordingly, the timing indicators, I idbT  , are equal 1 if the year individual i from school district d turned T age 17 minus the year of the initial desegregation court order in school district d equals T and zero otherwise.
I include indicators for values of T between -20 and 20, which is the full support of years individuals were age 17 relative to initial court order years in the sample.
Values of T between -20 and -1 represent unexposed cohorts who turned between the ages of 18 and 37 in the year of the initial court order; a value of 0 is our reference category and represents individuals who turned 17 in the year of the initial court order and were thus not exposed; values between 1 and 11 represent exposed cohorts who were “partially treated” because they were of school-going age (6 through 16) at the time of the initial court order but had less than 12 years of expected exposure; and values of 12 and greater represent fully treated exposed cohorts who turned 5 or younger during the year court-ordered desegregation was enacted and were therefore expected to attend desegregated schools for all 12 years of public schooling.
This DiD event study model compares the difference in outcomes between birth cohorts within the same district exposed to desegregation for different amounts of time (variation in exposure), separately by race.

To only rely on variation across birth cohorts within districts I include race-specific school district fixed effects, d .
To account for general underlying differences across birth cohorts r (irrespective of exposure), I include race-specific birth year fixed effects ( r b ) and race-by-region of birth cohort trends ( g * ).

With the birth-cohort fixed effects, the estimated changes across birth cohorts in br desegregated districts are all relative to the changes across the same birth cohorts in districts that did not implement desegregation plans during that time.
The coefficients on the full set of event study year indicators ( r T ; r T ; r T ) map out the dynamic treatment effects (across birth cohorts from the same school district) of court-ordered desegregation on school inputs and adult attainment outcomes, separately by race.8 I plot the estimated dynamic treatment effects for both blacks and whites to illustrate how school inputs and adult outcomes evolve for cohorts in school before, during, and after desegregation (relative to changes for the same birth cohorts in similar 12 districts that had not enacted desegregation plans at that time).
The estimates of r T illustrate the exact timing of changes in outcomes in relation to the number of school-age years of exposure to court-ordered desegregation, separately by race; while the estimates of r T provide a precise visual depiction of whether there are systematic time trends preceding enactment of court-ordered desegregation.
The former uses the specific timing of changes to test for causal impacts of desegregation by race; the latter provides a test of endogeneity of the timing of initial court orders.

As long as the timing of court-ordered desegregation is exogenous to changes in outcomes across birth cohorts within districts, the coefficients r T should uncover the causal effects of school desegregation on adult outcomes, separately by race.
It is important to note that, because the childhood school district prior to reforms may not always be the same school district an individual actually attends (due to residential mobility after reforms), r T are intent-to-treat estimates that quantify the policy effects of desegregation in an individual’s childhood school district.9 The model includes controls for an extensive set of child and childhood family characteristics ( icbX : parental education and occupational status, parental income, mother’s marital status at birth, birth weight, child health insurance coverage, gender).
The set of controls also involve interactions between 1960 characteristics of the county of birth and linear trends in the year of birth ( W d  1960 b : 1960 county poverty rate, percent black, average education level, percent urban, population size), which include the percent of the county that voted for Strom Thurmond in the 1948 Presidential election (as a proxy for white segregationist preferences) as further controls for trends in factors hypothesized to influence the timing of desegregation.
The period in which school desegregation occurred overlaps other important coincident policy changes, including hospital desegregation in the South (Chay et al, 2009), the roll out and significant expansion of the safety net via War on Poverty and Great Society programs and initiatives, and is against the backdrop of the broader Civil Rights era.
To account for these policy changes, I directly include county-by-cohort-level measures that capture the timing of hospital desegregation × race (exposure based 13 on place and year of birth), roll out of community health centers, state-funded initiatives for kindergarten introduction, Head Start per-capita expenditures at age 4, per-capita expenditures from Title-I school funding, and per-capita expenditures on food stamps, AFDC, Medicaid, unemployment insurance, each averaged over the individual’s childhood years ( dbZ ).
The data sources used to compile these measures are detailed in the Data Appendix.

While this work draws heavily from prior research that have examined these other policy impacts, few studies have attempted to simultaneously account for such a comprehensive set of policies, in this case to isolate the causal impact of school desegregation.
The models that analyze the economic and health status outcomes of interest use all available person-year observations in adulthood (for ages 20-50) with controls for age, age squared, and age cubed to avoid confounding life cycle and birth cohort effects.
idb is a random error term and the standard errors are clustered at the school district level.10 The identification strategy herein that exploits the quasi-random timing of initial court orders using an event study framework differs from influential design-based studies in the desegregation literature that have mostly relied upon the timing of major desegregation plan implementation using data from Welch/Light in 120 large districts (e.g., Guryan, 2004; Reber, 2005; Baum-Snow & Lutz, 2010).
The most important among these is that of Guryan (2004), who did not estimate an event study model.

Endogenous delays of major desegregation plan implementation following initial court orders threaten the validity of this previously used strategy.

The existence of systematic, pre-desegregation trends could indicate that the timing of major desegregation plan implementation was endogenous to factors affecting post-plan outcomes, as evidence herein suggests (see Appendix B & Table B1).
In contrast, as will be shown in Section V, I find no evidence of systematic pre-existing time trends in outcomes preceding initial court orders, which supports the validity of the research design.
I present graphical plots, separately by race, based on equation (1) estimates that form the response function of school desegregation effects to test for any dose-response with years of exposure.11 The delays in desegregation implementation following initial court orders and well-documented riots and 14 protests surrounding the initial years of desegregation implementation in many communities suggest that desegregation efforts may have become more effective with time, as racial animosity and tensions lessened.
Thus, this could generate a pattern in which there is a significant relationship between outcomes and event study years beyond 12 ( r T ) (since those who were pre-school ages at the time of initial court orders benefited from the experiences of the first cohort of black children who were pioneers of integration even if they each had the maximum 12 school-age years of exposure), which I explore.

Va.
Va.

EFFECTS ON SCHOOL INPUTS I present the effect of court-ordered desegregation on average school-age racial segregation, spending, and student-to-teacher ratio for the sample of court-ordered districts linked to individuals in the PSID.

Similar event study model results of desegregation effects on school inputs using all districts that were ever under desegregation court orders are presented in Appendix B.
The similarity of the results among all districts ever under court order and the subset of those districts that overlap the PSID affirm the representativeness and generalizability of the findings reported from the PSID.
The event study figures trace out the (equilibrium) adjustment path for school inputs from the pre-desegregation plan period to the implementation of plans—allowing for possibility that efficacy of desegregation plans may erode over the long-run due to “white flight” (private school attendance or movement out of the district).

Reduction of Segregation within School Districts.

The extent of segregation within districts diminished sharply during the period 1968-72.
The changes were greatest in the Southeast, which had a smaller proportion of highly segregated districts in 1972 than any region of the country.
As shown in Figure 1 (and Appendix Figure B1a), following court desegregation orders, there is a sharp decline in the school district racial dissimilarity index, which ranges from zero to one, and represents the proportion of black students who would need to be reassigned to a different school for perfect integration to be achieved given the district’s overall racial composition.

There is no evidence of pre-existing segregation trends in the school districts prior to the court orders.
Such a trend, had it existed, would have raised concern about the validity of the approach.

Within three years after court order, the dissimilarity index 15 dropped by roughly 0.2 which is a substantial and rapid decrease given the average black-white dissimilarity index in 1968 among school districts that had not yet implemented a desegregation plan was 0.83.
The change in the dissimilarity index 4 years after the court order is equal to 36 percent of the average index in 1970 and to a full standard deviation change in the level of school segregation (based on the 1970 cross-sectional standard deviation of the index).
Similarly, as shown in Figure B1b, we also witness a significant increase in the black-white exposure index among students (an alternative measure of school segregation).12 Desegregation involved not only reassignments of student to schools, but also a merging of teachers and staff in the district, so that there would no longer be identifiably all-black and all-white schools within the district.
As shown in Figure 2 and Appendix Figures B2a-B2b, we see a parallel pattern of sharp declines in racial school segregation among teachers (for both the dissimilarity index and the black student-to-white teacher exposure index) emerge after desegregation court orders were enacted (not documented in prior studies).

Increased Per-Pupil Spending.


Figure 3 depicts how school-age per-pupil spending evolved for cohorts that were expected to graduate seven years prior to the initial desegregation court order through those that were expected to graduate 17 years post reform.

The series of event-study estimates is relative to the effect for event study year 0 (those that turned 17 years old in the initial year of court-ordered desegregation in their school district).
Because the outcome is in logs, the values represent percent changes in average school-age spending relative to the cohort from the same district that was 17 the initial year of court-ordered desegregation.

As one can see, unexposed cohorts -7 through -1 (turned ages 18 through 24 the year of the first court-order) experienced no apparent significant changes in school-age per-pupil spending in the years immediately leading up to the initial court.
The p-value for the joint hypothesis that all these pre-reform event-study years is equal to zero is above 0.1.

This lends credibility to the exogeneity of the timing of court orders.

Consistent with court-ordered desegregation reducing racial inequality in spending, exposed black cohorts, on average, see large spending increases that increase with years of exposure, while whites, on average, did not experience any significant spending 16 changes.
The results indicate that among blacks with 12 years of exposure (age 5 during the year of the initial court order), average school-age per-pupil spending was 22.5 percent greater (or about $1,300 more (in 2000 dollars)) than that experienced among unexposed black cohorts from those districts who were 17 or older when the court rulings went into effect.
Appendix Figures B3a-B3d show court-ordered desegregation effects on school district per-pupil spending, separately by revenue source (local; state; federal).

Importantly, the large increase in school district per-pupil spending is driven solely by the infusion of state funds following the timing of court-ordered school desegregation (Figure B3c).
I do not find a similar pattern in districts that were not under court order, nor do I find significant spending changes in districts with a small minority proportional enrollment following court orders (Figure B3d).

I find insignificant and negligible effects on per-pupil spending from local or federal sources.
Recall that before school desegregation plans were enacted, school district spending, particularly in the South, was directed disproportionately to the majority-white schools within districts, which will not be reflected in the district-level spending data.

A political economy explanation for these results is that state legislatures were under pressure to ensure that the level of school resources available to whites would not be negatively affected by integration.
The larger the proportion of the school district’s students who were non-white, the larger was the share of school resources that may need to be redistributed toward minority students following school desegregation in the absence of an increase in state funding.
As a result, states infused greater funds into districts undergoing desegregation to ensure the level that black students received could be leveled-up to what whites were previously receiving (i.e., without affecting prevailing resource levels for white students).

Reductions in Class Size.


Figure 4 and Figure B4 provide supportive evidence of reduced average class size for blacks following desegregation court orders.13 With the use of school-level data, the results for class size do not exhibit any pre-existing time trend but fall sharply following court orders, with reductions in class size for blacks of about 3 to 4 students two years later (Figure B4).
The results indicate no significant effects on the average class size among white students, while significant reductions were experienced in class size for the average black student (using district-level data, Figure 4 shows average 17 school-age student-to-teacher ratios decline by one for fully exposed black cohorts relative to unexposed cohorts).
The sharp trend break in school resource inputs (per-pupil spending, class size, school segregation) immediately following court orders strongly suggests the estimates reflect the causal impact of desegregation.

Vb.

EFFECTS ON ADULT OUTCOMES Educational Attainment.

Figure 5 presents non-parametric event study model results for blacks and whites on the same graph for the effects of court-ordered school desegregation on years of completed schooling.
Black cohorts with more school-age years of desegregation exposure have higher completed years of education than unexposed cohorts and cohorts with fewer years of exposure.

For black children, exposure to court-ordered desegregation in all 12 school-age years increases educational attainment by roughly one year (p-value<.01).
Even though each event-study year is estimated with noise, among black cohorts with more than 5 years of exposure (i.e., those age 12 or younger at the time of the initial court order) the 90 percent confidence interval for all individual event-study years lies above zero.

Note that testing the difference between individual years of exposure is low powered, and is not a test of the broader hypothesis that court-ordered desegregation has a causal impact on adult outcomes.
To test this broader hypothesis, I find for blacks the post-desegregation event-study years are jointly significant at less than the 1% level.

Furthermore, a test of equality of the post-desegregation event-study year indicators across the two racial groups yields a p-value below 0.01.

Each additional year of exposure to court-ordered desegregation leads to a 0.1 increase in years of education for blacks.
To put these estimates in perspective, the gap in completed years of education between black and white children is one full year.

Thus, the estimated effect of desegregation exposure throughout all 12 school-age years for black children is large enough to eliminate the black-white educational attainment gap.
To examine the margin of educational attainment affected, I find similar event study results on the probability of graduating from high school with large, statistically significant effects for blacks (Figure 6).

The average high school graduation rates for blacks and whites for these birth cohorts is 0.73 and 0.88, respectively.
The results indicate that, for blacks, there is an immediate jump in the likelihood 18 of graduating from high school with exposure to court-ordered desegregation, and each additional year of exposure leads to a 1.8 percentage-point increase in the likelihood of high school graduation with an additional jump for those exposed throughout their school-age years.
The mean and standard deviation change in exposure to court-ordered desegregation for the sample is roughly 5 years; thus, a 5-year increase in exposure translates into a 14.5 percentage point increase in the likelihood of graduating from high school and roughly a 0.6 increase in years of education for blacks.

The desegregation effect sizes for blacks are comparable to the influence of having college-educated parents.
The pre-desegregation coefficients permit a partial test of the identifying assumption that, in the absence of court-ordered desegregation, educational attainment would have trended similarly in districts which had initial desegregation court orders enacted at different times.
Credibility of the research design is supported by the fact that there is very little evidence of pre-existing trends in either high school graduation or completed education before desegregation orders are enacted (the p-value for the joint hypothesis that all the pre-desegregation event-study years is equal to zero is above 0.1 for both blacks and whites); but after enactment, we see a structural break in the trend for blacks.
As aforementioned, the significant effects observed for blacks beyond one’s school-age years may reflect that desegregation efforts may have become more effective with time and/or that black children who were pre-school ages at the time of initial court orders benefited from the experiences of the first cohort of black children who were pioneers of integration.
In stark contrast, for whites there are consistently no significant effects on either the likelihood of high school graduation nor years of completed education, and the point estimates are negligible.

The small, insignificant effects for whites provide further evidence to rule out the competing hypothesis that the black improvements in educational attainment were driven by secular trends in desegregated districts.14 College Quality.
Equally important impacts of court-ordered desegregation may extend beyond blacks’ improvements in the quantity of years of completed education to the quality of education received (in both absolute and relative terms).

Accordingly, I next examine desegregation effects on college 19 quality.

A growing body of evidence demonstrates significant labor market returns to college quality (Andrews et al., 2011; Hoekstra, 2009).
I use information collected on college name reported by respondents between 1975 and 2013 and match it with the Integrated Post-secondary Education Data System (IPEDS) in order to link respondents with college quality indicators for the college attended.

I use the 25th and 75th percentiles of the SAT math and verbal scores of the freshman class to which the individual attended college as markers of college quality.
Figure 7 presents the non-parametric event study model estimates for black and whites on the same graph for the effects of desegregation on these measures of college quality.

Across each of the SAT math/verbal 25th and 75th percentile score outcomes, we see parallel patterns that mirror the effects found for years of education and high school graduation.
Namely, I find large estimated effects for blacks that increase with school-age years of desegregation exposure, with no pre-existing time trend and negligible effects beyond school-age years.

Estimated effects for whites are consistently small with point estimates near zero.15 Labor Market Outcomes, Adult Family Income and Poverty Status.

The next series of results reveal large, significant effects of court-ordered desegregation on blacks’ adult economic status and labor market outcomes.
Figures 8-11 present desegregation effects by race on adult economic outcomes (ages 20-50), including wages, occupational attainment, annual family income, and the annual incidence of poverty.

In light of the parallel set of findings across all these long-run economic outcomes, the results are discussed in succession.

Adult outcomes for blacks generally improved monotonically with the number of school-age years of exposure to desegregation.
The results indicate that, for blacks, court-ordered desegregation significantly increased adult wages and annual earnings, as there is an immediate jump in wages and earnings with exposure to court-ordered desegregation, and each additional year of exposure leads to a 2 percent increase in wages with an additional jump for those exposed throughout their school-age years (Figures 8 & 9).
Among black cohorts with more than 5 years of exposure the 90 percent confidence interval for all individual event-study years lies above zero.

I find for blacks the post-desegregation event- 20 study years are jointly significant at less than the 1% level.

Furthermore, a test of equality of the post- desegregation event-study year indicators across the two racial groups yields a p-value below 0.01.
These effects for blacks represent substantial improvements in adult labor market outcomes, as the average effects of a 5-year exposure to court-ordered school desegregation lead to about a 15 percent increase in wages and an increase in annual work hours of roughly 165, which combined to result in a 30 percent increase in annual earnings.
Furthermore, among blacks, desegregation exposure led to significant improvements in occupational attainment, as reflected in the 5.2 point increase in the occupational prestige index associated with a 5-year increase in exposure (Figure 12).

The average occupational prestige index for blacks and whites prior to desegregation was 30 and 60, respectively.

I find this translated into substantial gains in adult family economic status among blacks.
The effects on family income reflect (a) increases in own income, (b) increases in other income due to increases in the likelihood of being married (i.e., there are more potential earners), and (c) increase in the income of one’s family members (which is likely if persons marry individuals who were also affected by desegregation).
As shown in Figures 10 and 11, for blacks a similar pattern emerges of an immediate jump in family income and corresponding decline in the likelihood of adult poverty with exposure to court-ordered desegregation; each additional year of exposure leads to a roughly $1,000 increase in family income with an additional jump for those exposed throughout their school-age years (Figure 10); and in similar fashion, each additional year of exposure leads to a 1.3 percentage-point reduction in the annual incidence of poverty with an additional decline in poverty risk for those exposed throughout their school-age years (Figure 11).
The average effects of a 5-year exposure to court-ordered school desegregation lead to an 11 percentage-point decline in the annual incidence of poverty in adulthood and about a 25 percent increase in annual family income.
The estimated magnitudes of desegregation impacts are on par with the coefficients on parental education.16 It is equally noteworthy that there is no evidence of pre-existing time trends for any of these outcomes leading up to the year in which court-orders are enacted (the p-value for the joint hypothesis that all the pre-desegregation event-study years is equal to zero is above 0.1 for both blacks and whites); 21 whereas the post-desegregation event-study years for blacks are jointly significant at less than the 1% level.
Furthermore, a test of equality of the post-desegregation event-study year indicators across the two racial groups yields a p-value below 0.01.

Equally striking as the substantial magnitudes of the effects on blacks, is the consistent absence of any significant impacts on whites across all of these outcomes.

These important specification tests affirm the credibility of the research design and rule out several competing explanations for the pattern of results.

Probability of Incarceration.


The substantial racial disparities in incarceration, most pronounced among high school dropouts, have been well-documented (see e.g., Raphael (2005); Western (2007)).

Increased investments in school quality may reduce the frequency of negative social outcomes such as crime (see, e.g., evidence from the Perry Pre-School Project (Schweinhart et al., 2005)).
The next series of results reveal large, significant effects of court-ordered desegregation on blacks’ annual incidence of incarceration and probability of ever being incarcerated in adulthood.

The proportion of blacks (whites) ever incarcerated is 0.08 (0.04) for this sample of birth cohorts.
Among blacks, Figures 13a and 13b reveal a substantial discontinuous drop in both the likelihood of ever being incarcerated and the annual incidence of incarceration with exposure to court-ordered desegregation, respectively.

The results also highlight the larger reduction in the likelihood of incarceration among blacks exposed to integrated schools throughout their childhood years (vs those with more limited exposure).
For blacks the results indicate that, relative to growing up in segregated schools throughout one’s school years, exposure to desegregation beginning in one’s elementary school years leads to a 3 percentage-point reduction in the annual incidence of incarceration (Figure 13b) and a 22 percentage-point decline in the probability of adult incarceration (Figure 13a).

The results do not indicate any pre-existing trends in these outcomes prior to court-ordered desegregation.
These differences are somewhat less dramatic when comparisons are made for smaller increments of desegregation exposure (e.g., about a 10 and 15 percentage-point reduction in the probability of adult incarceration if the court order first occurred during high school and middle school, respectively, relative to no exposure).

Furthermore, the incarceration effects explain a significant amount of the work hours’ effects of 22 desegregation for blacks.
Importantly, I find no desegregation effects on the probability of incarceration for whites, which follows the pattern of results for educational attainment by race.

Adult Health Status.

Education has been shown to be a very strong correlate of health status in cross-sectional work and across generations.
Scholars have long hypothesized that education has a causal effect on subsequent health, though the precise ways education influences adult health have not been well established (Cutler and Lleras-Muney, 2006).

Large gaps in morbidity and mortality between more- and less-educated individuals have been well documented.

Furthermore, gaps in health between blacks and whites are large and appear to widen over the life cycle, suggestive of an important role of childhood conditions.
The next series of results reveal large, significant improvements in blacks’ adult health status resulting from exposure to court-ordered school desegregation.

The main health outcome analyzed is self- assessed general health status (GHS).

To scale the GHS categories, I use the health utility-based scale that was developed in the construction of the Health and Activity Limitation index (HALex) (details in Appendix C).
The results are based on interval regression models using a 100-point scale where 100 equals perfect health—the interval health values associated with GHS used are: [95, 100] for excellent, [85, 95) for very good, [70,85) for good, [30,70) for fair, and [1,30) for poor health.

Alternatively, I define problematic health as an indicator of whether the individual self-reported not being in excellent or very good health (ages 20-50).
Linear probability models of the annual incidence of problematic health yielded similar patterns reflecting increases in the probability of excellent/very good health.17 The general health status (GHS) index in adulthood is 6.5 points lower for blacks, on average, but I find substantial birth cohort differences in the magnitude of black-white health disparities in adulthood (evaluated at the same ages) (Johnson, 2009).
In particular, while the age-adjusted average black-white difference in adult health status for cohorts born in the early 1950s is 9.3 points, this difference is reduced to 4.7 and 3.3 points, among cohorts born between 1955-1963 and 1964-1968, respectively.

These cohort differences are completely driven by health improvements experienced by African Americans over this period; I do not find any significant birth cohort differences for whites.
23 The non-parametric event study results (Figures 14a-14b), based on both the interval regression model and linear probability model of the annual incidence of problematic health, indicate that, for blacks, adult health status improves monotonically with duration of exposure to court-ordered desegregation.

The average effect of a 5-year exposure to court-ordered school desegregation yields a 11 percentage-point increase in the annual incidence of being in excellent/very good health.
There is no evidence of pre-existing time trends in adult health in the years leading up to the court order (the p-value for the joint hypothesis that all the pre-desegregation event-study years is equal to zero is above 0.1 for both blacks and whites); whereas the post-desegregation event-study years for blacks are jointly significant at the 0.05 level.
The magnitudes and precision of the event study estimates increase when focusing on ages 35-50 (Figure 14b), likely due to the fact that most health problems do not manifest in one’s 20s.
A useful way to interpret the estimate is in relationship to the size of the effect of age on health, with the impact of each additional year of desegregation exposure for blacks equivalent (on average) to blacks reaching a level of health deterioration about 1 year later than if that year were spent in segregated schools.
For example, GHS is roughly 3 points higher for black adults who experienced 5 years of exposure to court-ordered school desegregation (relative to blacks who did not), which is equal to roughly 7 years evaluated at an effect of age during one’s mid-30s and 40s of -0.41.

This magnitude is also comparable to the impacts of parental education.
Following the pattern of results for the education and adult socioeconomic attainment outcomes, the desegregation effects on the adult health status of whites are statistically insignificant.

Addressing Endogenous Residential Mobility: One potential parental response to the presence of city differences in the timing and scope of school desegregation is to move to a different city (Baum- Snow & Lutz, 2011).
Because I did not want to include endogenous residential moves, this analysis does not incorporate information of family moves across school districts during the child’s school-age years.

Instead, I identified the school district of upbringing based on the earliest childhood address (in most cases, 1968).18 One may still worry that the results are biased by endogenous residential mobility.
To 24 address potential bias, I re-estimated all models limiting the analysis sample to those who lived at their (earliest) childhood residence prior to the enactment of initial court orders in their respective district.

The results are presented in Appendix D. I find nearly identical results as those in the full sample.

This indicates that endogenous residential mobility is not an important source of bias in the analysis.

Using Sibling Differences to Estimate Desegregation Effects.
The sibling fixed effect approach enables one to control for time-invariant aspects of all family and neighborhood background shared by siblings.
The effect of school desegregation and school quality is identified by capitalizing on the fact that siblings of different ages may have matriculated through different school systems, as there were rapid changes during that time.19 Within sibling pairs that attended schools with different resources, the younger sibling experienced integrated schools for a longer period of childhood and typically had access to greater school resources as reflected in greater per-pupil spending and smaller class sizes during school-age years.
The sibling comparisons evaluate adult outcomes at the same age and control for birth order, year of birth, birth weight, and whether mother was married at birth.

The sibling difference approach complements the primary event study difference-in-difference strategy.

I restrict the sample to siblings who grew up in the same city to eliminate endogenous migration as a potential source of bias.
Table 1 presents sibling fixed effect models designed to assess the long-run effects of school desegregation on education, socioeconomic attainment, and adult health status.
I find that black children who were exposed to court-ordered school desegregation for the majority of their school-age years experienced significantly improved education, economic, and health outcomes in adulthood, compared with their older siblings who grew up in segregated school environments with weaker school resources (controlling for age and birth cohort effects).

Negligible effects are found for whites.


I find that education, economic and health outcomes among blacks were particularly affected by changes in access to school resources associated with desegregation, not simply changes in exposure to white students.20 I find little evidence that observable differences among siblings are related to differences in the quality of high schools they attend.
There is no evidence that the results are biased by a positive correlation between sibling differences in school inputs and sibling differences in other factors that are favorable to adult 25 attainments.

Robustness & Falsification Tests.

Table E1 probes the robustness of these estimates further.
As a falsification exercise, I re-estimated equation (1) replacing the timing of initial court ordered desegregation variables with litigation cases that were not successful and the corresponding year of their court ruling to identify effects; in essence estimating the effects of a series of “placebo” initiatives.
If my baseline estimates capture the effects of school desegregation – not an earlier or later unobserved shock or intervention – the largest estimates of desegregation effects should arise from estimation of the model as originally specified.

Indeed, this is the case (Table E1).

In particular, a placebo treatment variable is included in the model which captures the years of childhood exposure to unsuccessful court litigation.

The coefficient on the placebo variable should be small and insignificant.
Indeed, when I used the placebo and the corresponding year of their court ruling to identify effects, they are not associated with any measurable impact on any outcome of interest.

These results demonstrate that timing of unsuccessful court litigation is unrelated to adult attainment outcomes; only the timing of initial year of successful litigation that led to court-ordered school desegregation is significantly associated with blacks’ adult socioeconomic & health attainments.
This provides additional evidence that the main results are not spurious, and helps rule out confounding influences from changing local demographic characteristics or social policies.

If such omitted variables spuriously inflate the estimated effect of desegregation, the placebo coefficient should be significant.

It is not.

These falsification tests provide additional evidence that unobserved factors do not contaminate the estimates.
The results are robust to many other sensitivity tests including adding more fixed effects, examining subgroups of the sample, and placebo tests on groups not likely to be affected (e.g., contemporaneous black adult employment rates (in occupations outside of K-12 education), providing further evidence of the exogeneity of the treatment.
The results, as expected, show no significant impact of desegregation exposure for any of these groups—the point estimates are small, mostly statistically insignificant, and negative compared to the consistently positive and significant estimates for blacks.

26 The evidence collectively is not consistent with alternative omitted-variables counter- explanations of the results (i.e., other factors that happened to change at the same time these desegregation orders were enacted).
Based on the robustness of the results, such an alternative explanation must be a cause that meets the following very strict criteria: a) it closely follows the timing of initial court orders (given the evidence showing no pre-existing time trends); b) yet it be geographically confined to the specific school districts in which desegregation court orders were being enacted (given the robustness of the results to the inclusion of cohort-by-race-by-region of birth fixed effects); c) its impacts are constrained only to school-age years of exposure (given the evidence showing no effects for non- school age years beyond age 17); d) had the largest impacts on blacks in communities where desegregation resulted in the largest changes in school quality inputs (Tables F1-F2); and finally e) had no effects on whites.
The results support a causal interpretation of the effects of school desegregation by uncovering sharp differences in the estimated long-run effects on cohorts born within a fairly narrow window of each other that differ in whether and how long they attended desegregated schools.

Exploring the Potential Mechanisms.


The analysis cannot cleanly identify the precise mechanisms through which school desegregation influenced long-run adult outcomes, but two potential pathways that merit careful consideration is through impacts of peer effects and school quality improvements (i.e., greater school resources for blacks in integrated schools) on the socioeconomic mobility process.
In order to assess the relative roles of school resources and peer effects as potential mechanisms underlying the desegregation effects, I estimate 2SLS models in which the key explanatory variables of interest—log of average per-pupil spending experienced during one’s school-age years and the average level of racial school integration (i.e., the average black-white exposure index during ages 5- 17)—are predicted in a first-stage model using only the individual’s duration of desegregation exposure (fully non-parametric specification for school-age exposure years), with the same full set of controls as in equation (1).
Identification is based on the timing of court-ordered desegregation and the strong first-stage results of desegregation-induced changes in average school-age per-pupil spending and school segregation, respectively, were presented in Figures 1, 2b and B1b.21 The 2SLS models are presented in 27 Tables 2-4 for the main adult attainment outcomes, and include the same set of controls as the prior models, estimated separately by race.
These estimates are not intended to be interpreted as the causal impacts of school spending per se, but rather as markers of the treatment dosage that may capture the combined effects of improvements in school resources and teacher quality.
I present three sets of 2SLS estimates: (1) include only instrumented average black-white exposure index (without instrumented spending); (2) include only instrumented average school spending (without instrumented racial segregation); (3) include both instrumented average black-white exposure index and instrumented average school spending in the same model.22 The results highlight the importance of examining effects of both changes in access to school quality, as proxied by changes in per-pupil spending, and changes in peer exposure as measured by changes in racial school segregation.
The 2SLS estimates shown in Table 2 indicate significant positive effects of desegregation- induced increases in school spending on blacks’ educational attainment and adult wages, which are an order of magnitude larger than the corresponding naïve OLS estimates.

The beneficial effects of desegregation-induced increases in school spending for blacks are particularly pronounced when simultaneously accounting for changes in racial school segregation (columns (3), column (6)).
In contrast, these 2SLS models reveal small, insignificant effects for increases in racial integration for both blacks and whites (both in models without spending (column (1)) and in those holding spending changes constant (column (3)).
I also find desegregation-induced increases in school spending for blacks are associated with significant reductions in the annual incidences of poverty and problematic health in adulthood (Table 3), and reduced both the likelihood and incidence of adult incarceration (Table 4).
These significant spending effects for blacks persist after the inclusion of corresponding increases in the black-white exposure index that accompanied desegregation, and, if anything, appear stronger once changes in school segregation are accounted for.
The results for blacks indicate that a 10 percent increase in school spending experienced throughout one’s school-age years is associated with 0.49 additional years of completed education, a 21 percent increase in wages, a 7.1 percentage-point reduction in the annual incidence of 28 adult poverty, a 6.9 percentage-point reduction in the annual incidence of problematic health in adulthood, and an 11.9 percentage-point reduction in the likelihood of ever being incarcerated.
On the other hand, there is suggestive evidence that reductions in school segregation levels that were not accompanied by significant changes in school resources did not have equally large impacts on blacks’ adult attainments.

In general, the magnitudes of the desegregation impacts across the various adult outcomes for blacks were insensitive to how much reduction in racial school segregation resulted from court orders.
In particular, for blacks I find no significant effects of increases in racial integration on adult health and economic status.

Furthermore, for blacks the only significant effects of increased racial integration uncovered are for the likelihood of incarceration, but they run in the opposite direction once school spending changes are accounted for (i.e., increases in integration appear associated with increased likelihood of incarceration for blacks, holding spending changes constant).
For whites, there are no corresponding significant effects of either of these markers of treatment dosage on educational attainment and likelihood of incarceration.

There is some pattern of evidence that desegregation-induced increases in school spending were protective for whites in increasing wages and reducing the annual incidences of poverty and problematic health in adulthood, but these results are less consistent and contingent upon the inclusion of changes in racial school segregation.
The amount of desegregation achieved by the courts varied from district to district, as did the resultant change in access to school quality inputs received by minority children.

This was in part because desegregation was achieved in a variety of ways across school districts and was applied in many different initial school environments based on the form of racial segregation—de jure in the South and de facto in other regions of the country.
To further explore potential mechanisms, in additional analyses presented in Appendix F, I isolate for every district the desegregation-induced change in per-pupil spending and racial school integration, respectively, which are net of time-invariant school district characteristics, district- specific trends and a host of other coincident policy changes (see Figure F1).
I augment the primary model specifications for adult outcomes to investigate whether impacts appear to differ by the scope of desegregation (as proxied by the estimated desegregation-induced change in per-pupil spending (school 29 segregation)).

For each district, I compute the change in school district per-pupil spending (school segregation) induced by the court order from the year preceding enactment to the first several years following it.
I then exploit variation in the scope of desegregation court orders in addition to quasi- random variation in the timing to assess whether there is evidence of a dose-response effect of school quality improvements on subsequent education, economic, and health attainment outcomes among blacks.
This can be viewed as a triple-difference strategy that compares the difference in outcomes between treated and untreated cohorts within districts (variation in exposure) and across districts with larger or smaller changes in school spending due to desegregation (variation in intensity).
The full details of the estimation methods and results are presented in Appendix F. Importantly, I find no evidence that districts that underwent larger changes in school spending resultant from desegregation exhibited differential trends in outcomes preceding the enactment of court orders, which provides additional support for the identification strategy.
The results of these models once again suggest that changes in school quality resulting from integration played an important role in improving blacks’ educational, economic and health attainments.

The results indicate significant interactive effects of school desegregation exposure with the resultant change in access to school quality, as proxied by changes in per-pupil spending.
I find that court-ordered desegregation that led to larger improvements in school quality resulted in more beneficial educational, economic, and health outcomes in adulthood for blacks who grew up in those court-ordered desegregation districts.
Interestingly, in these additional models, I find no effects on whites in either the duration of desegregation exposure nor the resultant change in school resources, which is precisely the pattern one might expect if the state infusement of school funding that accompanied desegregation (as reported in Figure B3c for districts with significant black enrollment) was used to intentionally direct school resources to minority children and level up resources for them to the level whites were receiving prior to desegregation.
Moreover, the fact that I find no school spending effects for poor whites, coupled with the fact that Title I federal spending is already explicitly controlled for in these models, provides further support that the school spending effects are capturing desegregation-induced impacts, not Title I funding.
30 As an additional placebo falsification test using the 2SLS models, it is shown in Appendix Table F3 that school spending increases have no significant impacts on blacks’ adult outcomes when they occur during non-school ages after individuals should have left school (between the ages of 20 and 24), but rather all the estimated long-run effects of per-pupil spending are confined to school-age years of exposure, as we would expect.23 The preponderance of results indicates small, insignificant effects for increases in racial integration (holding spending changes constant).
The event study, difference-in-difference, 2SLS, and sibling-difference estimates indicate that school desegregation and accompanied increases in school quality resulted in significant improvements in adult socioeconomic and health outcomes for African-Americans.

The pattern of results is remarkably similar across all of the empirical approaches.
It is particularly noteworthy that that the estimated effects of desegregation court orders on adult attainments are similar for the subset of black children who grew up in the South and those who grew up in other regions (e.g., see Appendix Table G3).
Finally, it is noteworthy that other concurrent policy changes were explicitly controlled for (including hospital desegregation in the South, the roll-out and/or expansions of AFDC, Medicaid, Food Stamps, Community Health Centers, Title I funding, Head Start, and kindergarten introduction), and do not account for the pattern of results presented here.

Contextualizing the magnitudes with previous studies.
The study most directly related to the approach taken in this paper is Guryan (2004), who uses variation in the timing of major desegregation plan implementation in the 1970s and 1980s to identify the effects of school segregation on black high school dropout rates for 125 large school districts (Welch/Light data and 1970-80 censuses).

He applies a difference-in-difference (DiD) strategy and finds that desegregation led to 3 percentage-point decline in the black high school dropout rate during the 1970s.
Guryan (2004) reports IV estimates that are two to four times larger in magnitude than his main DiD estimates.

This pattern is consistent with the findings of this study.

In Appendix Table G1, I replicate the main results of Guryan (2004) using similar model specifications for the likelihood of high school graduation as he employed, but using my PSID data 31 among the subsample that grew up in the districts that overlap the Welch/Light data (representing 75 different counties; column 2).
Column (3) of Appendix Table G1 appends his basic specification with a parametric event study model, which reveal a pre-existing negative time trend in the likelihood of high school graduation for blacks in the years leading up to major desegregation plan implementation; this result puts into question the exogeneity of major plan implementation timing due to endogenous delays following initial court orders.

In most other respects, I am able to replicate the main results of Guryan using the PSID.
Namely, when one uses the arguably endogenous timing of major plan implementation for identification, 1) for blacks, it is shown that there does not appear to be a dose-response with duration of desegregation exposure (column 4); 2) the estimated effect of any desegregation exposure increases the likelihood of high school graduation by roughly 4 percentage points for blacks (not significantly different from Guryan’s estimate with his specification); 3) no significant effects for whites.
In stark contrast, when one uses the preferred parametric event study specification on this same PSID subsample that overlaps Welch/Light districts, but instead using the timing of initial court order for identification, I find large impacts for blacks similar in magnitude as those reported in the main results presented in this paper (columns 5-6).
One explanation for the larger estimated effects in this paper than ones based directly on models of the effects of desegregation plans is that the timing of initial court orders is more plausibly exogenous than the year of first implementation of major desegregation plans, due to endogenous delays in effective implementation.24 There were longer delays in implementation of major desegregation plans following initial court orders for districts that had significant minority proportion, larger per-capita school spending, teacher salary, smaller average student-to-teacher ratios, and/or greater income (Table B1).
These factors likely lead OLS estimates of the effects of desegregation plans to be understated.
I also find a similar pattern of results for the effects of court-ordered school desegregation on district-level high school dropout rates using the Office of Civil Rights (OCR) Data and Common Core Data (CCD)—Local Education Agency Universe Survey and Non-Fiscal Survey Database—for all school districts in the US for available years 1972-1999 with the preferred research design, as reported in 32 Appendix Table G2.
The similar pattern of the PSID and OCR-CCD results serves to further demonstrate that the findings are generalizable and representative for these birth cohorts, and allay concerns that the results are specific to the PSID.

A large body of literature examines the effects of school spending on academic performance and educational attainment (Hanushek, 1997; Hedges, Greenwald, and Laine, 1994).
While evidence is mixed on the extent to which school resources matter, the results of this paper are in line with Card and Krueger (1992) and other recent studies that use randomized and quasi-random variation in school inputs (e.g., Jackson, Johnson, Persico, 2015; Chetty et al, 2013; Fredrikkson et al, 2012).
Jackson, Johnson, Persico (2015), using evidence from court-ordered school finance reforms, find that, for children from low- income families, a 10 percent increase in per-pupil spending throughout one’s K-12 years leads to 0.46 additional years of completed education, 9.6 percent higher earnings, and a 6.1 percentage-point reduction in the annual incidence of adult poverty.
An important limitation of most recent studies that find insignificant results focusing on the effects of school quality on labor market outcomes using longitudinal individual-level data is that earnings are observed at young ages (averaging around 23 years old).
A strength of the analyses contained in this paper, in addition to its credible research design, is both the extensive set of controls for childhood family and neighborhood characteristics and the ability to follow adult attainment outcomes into one’s peak earnings years through age 50.

Experimental evidence from the Tennessee Project Star class size intervention demonstrates that black students benefited about twice as much as whites from being assigned to a small class.
Krueger and Whitmore (2002) find that this result is mostly driven by a larger treatment effect for all students regardless of race in predominantly black schools, suggesting that benefits from additional resources are higher in such schools; and may lead to better adult socioeconomic attainments (Chetty et al., 2011).
The findings of the present study show that labor market outcomes, and adult income and health status rose in line with blacks’ educational improvements (in quantity and quality in both absolute and relative terms), as did declines in the incidence of incarceration.

Table G4 presents a summary of the implied Wald estimates of the returns to education (reflecting a combination of both increased quantity 33 and quality) across the adult outcomes.
A Wald estimate of the returns to education on wages is the ratio of the estimates of the desegregation effects of 5 years of exposure on wages and completed years of education, yielding a return of 31 percent (0.15/0.48).

These estimates are notably larger than the 8 to 14 percent returns typically estimated using modern era schooling interventions and data sources from more recent (younger) birth cohorts (e.g., Card, 1999), but these do not typically account for improvements in the quality of education.
If a Wald estimate is constructed based on effects on the incidence of adult poverty, probability of incarceration, and adult health status, the implied returns to education are even larger.

The incarceration effects of desegregation are consistent with Lochner and Moretti (2004), who report that a 10 percentage-point increase in high school graduation rates would reduce overall violent crime arrest rates for blacks by 25 percent and reduce murder arrests by two-thirds.
There are several plausible explanations for the much larger estimates obtained in these analyses.

First, improved school environments could have facilitated a higher quality teacher workforce (Jackson, 2009) and thus boosted the return to a year of school.

A second possibility is that the returns to schooling for those who were most impacted by school desegregation were just extremely large.
Third, the marginal returns to education for the groups affected by school desegregation may be larger than the average return.

Card (1999) shows that heterogeneous rates of return to education may arise due to differing costs of education, preferences, or marginal returns to the production function relating schooling to earnings.
Card suggests that one possible explanation for the tendency for many IV estimates of the returns to schooling to exceed OLS estimates is that in the presence of heterogeneous returns, the marginal returns to education for the groups affected by the instrument may be larger than the average return.25 VI.
SUMMARY DISCUSSION AND CONCLUSION Differences across districts in when desegregation court cases were first filed and the length of time it took these cases to proceed through the judicial system are used as a plausibly exogenous source of identifying variation to analyze the long-run impacts of school desegregation.

The exogeneity of the timing of initial court orders is supported theoretically by the documented legal history of school 34 desegregation and by my own empirical examination of the issue.
The analysis capitalizes on this source of identifying variation.

I control for possible confounders in a number of ways.

First, I estimate event study models that support the validity of the research design.
Second, I examine the determinants of the timing of the occurrence of the initial court order and major desegregation plan adoption, and find that collectively the pre-treatment school quality, SES, demographic, and labor market related characteristics do not significantly predict the year of the initial court order.

Third, I perform a variety of robustness checks to test the validity of the identifying assumptions.

The findings of this study contribute to the literature in several important ways.
First, this study is the most comprehensive to date on the topic, especially in terms of the range of empirical approaches utilized, broad set of outcomes analyzed, and the long time horizon considered.

Second, this paper provides important, new estimates of the impact of court-ordered school desegregation.

I use an event- study framework and exploit the wide quasi-random variation in the timing and scope of court-ordered desegregation during the 1960s, 70s and 80s to identify these effects.
I find that school desegregation significantly increased educational attainment among blacks exposed to desegregation during their school-age years, with impacts found on the likelihood of graduating from high school, completed years of schooling, attending college, graduating with a 4-year college degree, and college quality.
Non- parametric event-study estimates and sibling-difference estimates indicate that school desegregation and the accompanied increases in school quality also resulted in significant improvements in adult labor market and health status outcomes, and reductions in both the annual incidence of adult poverty and incarceration for blacks.
The significant long-run impacts of school desegregation found for blacks with parallel findings across a broad set of socioeconomic outcomes and health status indicators of well-being, with no corresponding impacts found for whites, is striking.
The results suggest that the mechanisms through which school desegregation led to beneficial socioeconomic outcomes in adulthood for blacks include improvement in access to school resources, which is reflected in reductions in class size and increases in per-pupil spending.

Furthermore, the 35 evidence is consistent with a dose-response effect of school quality improvements and the duration of exposure to them on subsequent attainments in adulthood.
The magnitude of the estimated effects of dimensions of school quality are larger than estimates reported in previous research and, taken together, are larger than the impact of increasing parents’ income by a comparable amount.

Finally, the present data and methods improve upon prior research, which lacked access to panel data that follow children from birth to adulthood, relied on aggregate state-level analyses, and/or failed to address the endogeneity of residential location.
This paper is among the first to assess and provide evidence on the extent and ways in which childhood school quality factors causally influence later-life health outcomes.

The evidence collectively paints a consistent picture of significant later-life health returns of school quality.
The results highlight the significant impacts of educational attainment on future health status, and point to the importance of school quality in influencing socioeconomic mobility prospects, which in turn have far-reaching impacts on health.

The results demonstrate that racial convergence in school quality and educational attainment following court-ordered school desegregation played a significant role in accounting for the reduction in the black-white adult health gap.
While no single explanation likely accounts for this rapid convergence, this work shows that school desegregation was a primary contributor, explaining a sizable share of the narrowing of the racial education, and economic and health status gaps among the cohorts examined.

Small, statistically insignificant results across each of these adult outcomes for whites suggest that benefits for minority children do not come at the expense of white students.
A limitation of the court-ordered desegregation results is their reduced-form nature.

I cannot separately identify the pathways through which desegregation impacts subsequent adult attainments.

It may not be the school desegregation so much as the nature and type of school desegregation implementation (e.g., how much it changed access to school resources for minority children) that matter most for long-run economic well-being and thereby adult health.
Future research should further uncover the precise structure of the underlying causal linkages between school desegregation and subsequent 36 attainment.

Separately identifying and disentangling the mechanisms underlying the overall causal impact of desegregation is very difficult with available data and is left for future work.

This study illustrates the gains in human capital acquisition among blacks that occurred due to greater accessibility of dimensions of school quality.
The findings highlight the large productivity gains that can arise when substantial improvement to school inputs are introduced to equalize differences in access to school quality.

Brown offered the hope and promise of better educational opportunities for minority children in the US, and was intended not only to promote equitable access to school quality but also to alter the attitudes and socialization of children -- beginning at the youngest ages.
A motivation of this study was to attempt to quantify the extent to which progress was made in fulfillment of policy expectations and to evaluate the enduring impact of what is arguably the most important subcomponent of legal actions during the Civil Rights era.
This work contributes to a growing literature that evaluates the longer-run effects of the Civil Rights Act, Great Society, and War on Poverty policy initiatives.26 The present research is the first to contribute estimates of the effects of school desegregation (and school quality) on adult economic and health outcomes using a plausibly exogenous source of identifying variation.

This study highlights the importance of analyses on the returns to education policies beyond labor market outcomes.
The findings of this paper strongly suggest that estimates of the returns to education that focus on increases in wages substantially understate the total returns.

Given the scarcity of large-scale educational experiments that had such dramatic changes in access to school quality, it is important to learn as much as possible about the long-run consequences of one of the great social experiments of inclusion.

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1 This desegregation case data was compiled by legal scholars for The American Communities Project at Brown University, and I combine it with additional information from Welch and Light (1987) on the dates of major desegregation plan implementation for large urban districts.

See Appendix A for more details.

2 Integration may also influence long-term outcomes in ways that are unrelated to academic achievement and educational outcomes.
3 The Census of Governments has been conducted every five years since 1972 and records school spending for every school district in the US.

The Historical Database on Individual Government Finances (INDFIN) contains school district finance data annually for a sub-sample of districts from 1967, and 1970 through 1991.

After 1991, the CCD School District Finance Survey (F-33) includes data on school spending for every school district in the United States.
Additional details on how these databases were compiled and the coverage of districts in these data are in Appendix B.

4 The PSID began interviewing a national probability sample of families in 1968.

These families were re- interviewed each year through 1997, when interviewing became biennial.

All persons in PSID families in 1968 have the PSID “gene,” which means that they are followed in subsequent waves.
When children with the “gene” become adults and leave their parents’ homes, they become their own PSID “family unit” and are interviewed in each wave.

The original geographic cluster design of the PSID enables comparisons in adulthood of childhood neighbors who have been followed over the life course.

Moreover, the genealogical design implies that the PSID sample today includes numerous adult sibling groupings who have been members of PSID-interviewed families for more than four decades.
I include both the Survey Research Center component and the Survey of Economic Opportunity component, commonly known as the “poverty sample,” of the PSID sample.

5 The PSID maintains extremely high wave-to-wave response rates of 95-98%.

Studies have concluded that the PSID sample of heads and wives remains representative of the national sample of adults (Gottschalk et al, 1999; Becketti et al, 1997).
6 The data I use include measures from 1968-1988 Office of Civil Rights (OCR) data; 1960, 1970, 1980, and 1990 Census data; 1962-1999 Census of Governments (COG) data; Common Core data (CCD) compiled by the National Center for Education Statistics; Regional Economic Information System (REIS) data; the comprehensive case inventory of court litigation regarding school desegregation over the 1955-1990 period (American Communities Project), and major plan implementation dates in large districts (compiled by Welch/Light); and American Hospital Association’s Annual Survey of Hospitals (1946-1990) and the Centers for Medicare Provider of Service data files (dating back to 1960s) to identify the precise date in which a Medicare-certified hospital was established in each county of the US (an accurate marker for hospital desegregation compliance).
Many school districts were counties during this period, including more than one-half of Southern school districts.

7 The average level of district per-pupil spending across all school-age years provides a summary measure of the level of financial resources available in the individual’s childhood school district during all their school-going years (ages 5 through 17 corresponding to expected grades K-12).
I use the natural log of this average measure to capture the fact that school spending likely exhibits diminishing marginal product (all results are robust to using the level of average school-age spending).
8 For example, 5 is the effect of the passage of a court-ordered desegregation on outcomes of untreated cohorts 5 is the effect of court-ordered desegregation that turned age 17 five years prior to reforms for racial group r. Also, r r on the outcomes of treated cohorts that turned age 17 five years after the passage of desegregation court orders.
9 Because some individuals may have moved away from their pre-reform school district or may have dropped out of school before the age of 17, my measure of school-age desegregation exposure is a noisy measure of the amount of desegregation individuals were actually exposed to.

Using the actual desegregation an individual is exposed to would introduce selection bias, because school-age years of exposure would be determined in part by the decisions of individual parents.
By using the individual’s childhood residential location prior to the court order, one removes 39 any potential bias due to endogenous residential sorting.

As shown in Appendix D, the results are nearly identical when the analysis sample is restricted to those who lived at their (earliest) childhood residence prior to the enactment of initial court orders in their respective district.
10 The statistical significance of all the main results are very similar when I cluster the standard errors at the childhood county level (instead of district level).

The estimates are very similar for models that include age fixed effects (instead of age cubic) for adult economic and health status outcomes.
11 Wherever possible, I present event study figures showing the 10 years leading up to court order and 17 years following court orders; for some outcomes in which data during pre-treatment years is more limited, results are presented for the 5-8 years leading up to court orders (the estimated models are the same throughout).

12 Levels of racial integration in schools peaked around 1988.
13 With the use of school-level data, models are weighted by baseline black student enrollment in the school, so that results can be interpreted as the desegregation effect experienced by the average black child.

Similarly, the results presented on the same graph for whites is weighted by baseline white student enrollment, so that the results can be interpreted as the desegregation effect experienced by the average white child (N=33,952 schools from 33 different states).
14 In additional specifications not shown to conserve space, I find similar results using a parsimonious set of controls (results available upon request).

The inclusion of the extensive set of childhood family/neighborhood factors, coincident policies and government transfer programs largely do not influence the point estimates of desegregation impacts (but tend to improve their precision).
This further supports the exogeneity of the timing of initial court orders, as this array of childhood factors and coincident policies (while independently related to adult attainment outcomes) does not appear systematically related to the timing of initial court orders.

15 Because of the smaller sample size for the models on college quality, the point estimates are much less precise with such a saturated model.
The pattern that emerges is clear, however, and an F-test rejects the null hypothesis and affirms the joint significance of the coefficients on the exposure years for blacks.

16 The sum of coefficients of mother’s and father’s education on adult wages is roughly 0.04.
17 Linear probability models of the annual incidence of problematic health, where problematic health is defined as being in fair or poor health yielded similar patterns, but with less precision due to the relatively younger ages (under 50) to study the onset of major health problems and use of fully non-parametric event study models.

18 Among original sample children in the PSID, the average proportion of childhood spent growing up in the 1968 neighborhood was roughly two-thirds.
19 This use of sibling models follows the research design previously utilized by Altonji and Dunn (1996) to analyze the effects of school quality on wages.

The sibling approach assumes parents treat their children similarly and do not reallocate resources within the family as a result of school desegregation.

20 These additional results are suppressed to conserve space; available upon request.
21 Qualitatively similar patterns of results are found for the effects of desegregation-induced changes in racial school segregation among students whether segregation is measured by black-white dissimilarity index or exposure index.

22 I also use naïve OLS estimates of effects of school spending and school segregation as a baseline comparison with the 2SLS estimates.
23 The first-stage models include as predictors the years of desegregation exposure (for relevant ages 5-17; 20-24) interacted with the respective school district's desegregation-induced change in school spending.
24 In other specifications (not shown to conserve space), I compared IV and non-IV estimated effects of major school desegregation plans on educational attainment, separately by race; the IV estimates for blacks are 2.4 times greater for high school graduation and 1.6 times greater for completed years of schooling (relative to the corresponding non-IV estimates using the same sample and model specification).
25 This could arise if marginal returns are higher for those with low levels of schooling and the instrument (e.g., school reforms, school accessibility) mainly affects this segment of the population by lowering the costs of schooling.

It seems plausible that desegregation disproportionately benefited those students with high costs of schooling and with especially high marginal rates of return.
26 Recent examples include Chay, Guryan, and Mazumder (2009) (desegregation of hospitals and academic achievement), Almond, Chay and Greenstone (Civil rights and infant mortality), Finkelstein & McKnight (Medicare introduction), Cascio, Gordon, Lewis and Reber (Title I), Ludwig and Miller (Head Start), Almond, Hoynes and Schanzenbach (food stamps and birth outcomes), and McCrary (court-ordered police hiring quotas).
40 FIGURE 1 FIGURE 2 Effect of Court-Ordered School Desegregation on Avg School-Age Racial School Segregation Among Students e g a - - k c a B l i .1 0 -.1 -.2 -.3 -.4 -10 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Blacks e g a - Effect of Court-Ordered School Desegregation on Racial School Segregation among Teachers .08 .06 .04 .02 0 -.02 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 6 2 8 4 14 16 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.
n i e g n a h C i ) g n d n e p S l i p u P - r e P g v A ( n L e g a - l o o h c s FIGURE 3 Effect of Court-Ordered School Desegregation on Avg School-Age Per-Pupil Spending .4 .3 .2 .1 0 -.1 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 2 6 4 8 14 16 90% CI Blacks FIGURE 4 Effect of Court-Ordered School Desegregation on Avg School-age Student-to-Teacher Ratio .5 0 -.5 -1 -1.5 -2 e g a - l o o h c s g v a n i e g n a h C o i t a R r e h c a e T - o t - t n e d u t S -4 -2 0 12 6 Year Aged 17 - Year of Initial Court Order 10 8 2 4 14 16 90% CI Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.
FIGURE 5 Effect of Court-Ordered School Desegregation on Educational Attainment, By Race 2 1.5 1 .5 0 -.5 -1 -1.5 -2 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 4 6 2 8 0 12 14 16 90% CI Whites Blacks FIGURE 6 Effect of Court-Ordered School Desegregation on Likelihood of Graduating from High School, By Race .4 .3 .2 .1 0 -.1 -.2 -.3 -10 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order ) d a r G o o h c S h g H ( b o r P i 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

(N=8,548 individuals from 3,562 childhood families, 631 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0 (see Appendix Figures C1b-C2b).
The Effect of Court-Ordered Desegregation on College Quality by Race: 25th Pctile of College's SAT Math Score The Effect of Court-Ordered Desegregation on College Quality by Race: 75th Pctile of College's SAT Math Score FIGURE 7. n i e g n a h C h t a M T A S s e g e ' l l o C f o e l i t % h t 5 7 200 100 0 -2 0 2 10 Year Aged 17 - Year of Initial Court Order 8 6 4 12 14 -2 0 2 10 Year Aged 17 - Year of Initial Court Order 6 4 8 12 14 Blacks Whites Blacks Whites The Effect of Court-Ordered Desegregation on College Quality by Race: 25th Pctile of College's SAT Verbal Score The Effect of Court-Ordered Desegregation on College Quality by Race: 75th Pctile of College's SAT Verbal Score n i e g n a h C l a b r e V T A S s e g e ' l l o C f o e l i t % h t 5 7 200 100 0 300 200 100 0 200 100 0 n i e g n a h C n i e g n a h C h t a M T A S s e g e ' l l o C f o e l i t % h t 5 2 l a b r e V T A S s e g e ' l l o C f o e l i t % h t 5 2 -2 0 2 10 Year Aged 17 - Year of Initial Court Order 8 4 6 12 14 -2 0 2 10 Year Aged 17 - Year of Initial Court Order 8 4 6 12 14 Blacks Whites Blacks Whites Data: PSID geocode Data (1968-2013), matched with childhood school and College characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation for whom college information available.

(N=1,570 individuals from 1,116 childhood families, 360 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division- specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Statisitically significant results for blacks, none for whites.
FIGURE 8 Effect of Court-Ordered School Desegregation on Adult Wages, By Race n i e g n a h C 0 5 - 0 2 s e g a , ) s e g a W ( n L .75 .5 .25 0 -.25 -.5 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 4 8 6 2 0 12 14 16 90% CI Whites Blacks FIGURE 9 Effect of Court-Ordered School Desegregation on Adult Earnings, By Race n i e g n a h C , ) s g n n r a E i l a u n n a ( n L 0 5 - 0 2 s e g a 1.25 1 .75 .5 .25 0 -.25 -.5 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 2 4 0 6 8 12 14 16 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year positive earnings observations (ages 20-50) are included except those in which individual was in school (N=97,568 person-year wage observations, 8,597 individuals from 3,584 childhood families, 636 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0 (see Appendix Figures C3b-C4b).
FIGURE 10 Effect of Court-Ordered School Desegregation on Adult Family Income, By Race n i e g n a h C , ) e m o c n I y m a F l i l a u n n a ( n L 0 5 - 0 2 s e g a 1.5 1.25 1 .75 .5 .25 0 -.25 -.5 -10 -8 -6 -4 Year Aged 17 - Year of Initial Court Order 10 -2 2 8 4 6 0 12 14 16 90% CI Whites Blacks FIGURE 11 FIGURE 12 Effect of Court-Ordered School Desegregation on Annual Incidence of Poverty in Adulthood, By Race Effect of Court-Ordered School Desegregation on Occupational Attainment, By Race n i e g n a h C 0 5 - 0 2 s e g a , ) y t r e v o P ( b o r P .1 0 -.1 -.2 -.3 -.4 -10 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 30 20 10 0 -10 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 4 2 0 6 8 12 14 16 90% CI Whites Blacks 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year observations (ages 20-50) are included except those in which individual was in school (N=142,499 person-year family income observations, 9,156 individuals from 3,702 childhood families, 645 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0 (see Appendix Figures C5b-C6b).
FIGURE 13A Effect of Court-Ordered School Desegregation on the Likelihood of Ever Being Incarcerated, By Race -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Whites Blacks FIGURE 13B Effect of Court-Ordered School Desegregation on Annual Incidence of Adult Incarceration, By Race n i e g n a h C ) d o o h t l u d A n i d e t a r e c r a c n I r e v E ( b o r P n i e g n a h C 0 3 - 8 1 s e g a , ) d e t a r e c r a c n I ( b o r P .2 .1 0 -.1 -.2 -.3 -.4 .04 .02 0 -.02 -.04 -.06 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 2 4 8 6 14 16 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, first observed before age 21 and followed until at least age 25, who grew up in school districts that were ever subject to court-ordered desegregation.

Incarceration info based on reason for non-response for each survey 1968-2013 &, where available, 1995 svy reports of whether/when ever incarcerated.

Models of annual incidence of adult incarceration include all person-year observations (ages 18-30).
(N=96,584 person-year observations, 8,539 individuals from 3,411 childhood families, 524 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age FE, svy year FE.
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0 (see Appendix Tables C7b-C8b).
FIGURE 14A Effect of Court-Ordered School Desegregation on Annual Incidence of Moderate/Problematic Health in Adulthood, By Race .3 .2 .1 0 -.1 -.2 -.3 -.4 -.5 -6 -4 -2 12 Year Aged 17 - Year of Initial Court Order 10 0 2 6 4 8 14 16 90% CI Whites Blacks FIGURE 14B Effect of Court-Ordered School Desegregation on Adult Health Status, By Race 0 5 - 0 2 s e g a 25 20 15 10 5 0 -5 -10 , ) h t l a e H d o o G y r e V / t n e l l e c x E n i t o N ( b o r P 0 5 - 5 3 s e g a , -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Whites Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year self- assessed health status observations (ages 20-50) are included except those in which individual was pregnant/yrs immediately following childbirth (Figure 14A: N=75,729 person-year health status observations, 7,527 individuals from 3,330 childhood families, 613 school districts).
Health Status index (1-100(perfect health)) based on self-assessed health (E/VG/G/F/P), 1985-2013; interval regression model estimated, where E=[95,100]; VG=[85,95); G=[70,85); F=[30,70); P=[1,30).

(Figure 14B: N=42,011 person-year observations at ages 35-50 for 5,598 individuals from 2,797 childhood families, 570 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state- funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0 (see Appendix Figures C10b-C11b).

Table 1.
Table 1.

Long-run Effects of School Desegregation on Educational, Economic, & Health Attainment: Sibling Fixed Effect Estimates Dependent variable: Years of Education Ln(Family Income) general Health Status in adulthood, Interval Regression Model: 100pt- scale, 100=perfect health Black (1) White (2) Black (3) White (4) Black (5) White (6) Years of Exposure to Court-Ordered Desegregation(age 5-17) 0.1294* (0.0729) Sibling Fixed Effects?
yes Robust Standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 Note: All models include flexible controls for age (quadratic), gender, year of birth, birth order, birth weight, whether born into a two-parent family, and parental income (coefficients supressed to conserve space).

0.6417** (0.2941) yes 0.0358* (0.0189) yes -0.0067 (0.0179) yes 0.0356 (0.0962) yes -0.1506 (0.4022) yes Table 2.
2SLS Estimates of Effects of Court-Ordered School Desegregation's Induced-Change in Racial School Integration & Induced-Change in Per-Pupil Spending on Educational Attainment & Adult Wages, By Race Years of Education Ln(Wage), ages 20-50 Dependent variable: 2SLS Estimates (school segregation & per-pupil spending instrumented using timing of court-ordered desegregation): School Segregation: Avg Black-White Exposure Index(age 5-17) *Black Avg Black-White Exposure Index(age 5-17) *White School Spending: Ln(Avg Per-Pupil Spending)(age 5-17) *Black Ln(Avg Per-Pupil Spending)(age 5-17) *White (1) (2) (3) (4) (5) (6) 0.8200 (2.7650) -1.3306 (3.3394) 0.3226 (0.9070) -0.1260 (0.8734) -3.3974 (3.1813) -2.7275 (5.1829) 4.8706** (1.8955) 1.5577 (4.2764) 3.0670* (1.8084) 0.1281 (2.6961) -1.3538 (1.0358) -1.8259 (1.2109) 2.1425** (0.9644) 2.0143* -1.0481 97,568 8,597 3,584 636 1.4367* (0.8280) 1.0692 (0.7185) 97,568 8,597 3,584 636 Number of adult person-year observations Number of Individuals Number of Childhood Families Number of School Districts Robust standard errors in parentheses (clustered at school district level).
Includes same full set of controls as main models.

*** p<0.01, ** p<0.05, * p<0.10 97,568 8,597 3,584 636 -- 8,548 3,562 631 -- 8,548 3,562 631 -- 8,548 3,562 631 Table 3.
2SLS Estimates of Effects of Court-Ordered School Desegregation's Induced-Change in Racial School Integration & Induced-Change in Per-Pupil Spending on the Annual Incidences of Poverty & Problematic Health in Adulthood, By Race Probability(Poverty), ages 20-50 Probability(Moderate/Problematic Health), ages 20-50 Dependent variable: (1) (2) (3) (4) (5) (6) -0.3524 (0.6547) 0.5339 (0.5049) 75,729 7,527 3,330 613 0.3000 (0.7067) 1.9164** (0.7829) -0.6910* (0.4134) -1.4163** (0.6317) 75,729 7,527 3,330 613 -0.5554+ (0.4275) -0.4935+ (0.3591) 75,729 7,527 3,330 613 2SLS Estimates (school segregation & per-pupil spending instrumented using timing of court-ordered desegregation) : School Segregation: Avg Black-White Exposure Index(age 5-17) *Black Avg Black-White Exposure Index(age 5-17) *White School Spending: Ln(Avg Per-Pupil Spending)(age 5-17) *Black Ln(Avg Per-Pupil Spending)(age 5-17) *White -0.2640 (0.4559) 0.2455 (0.1648) 0.3316 (0.5421) 0.5254** (0.2535) -0.7065+ (0.4643) -0.3203+ (0.2213) -0.5350+ (0.3918) -0.0508 (0.1463) Number of adult person-year observations Number of Individuals Number of Childhood Families Number of School Districts Robust standard errors in parentheses (clustered at school district level).
Includes same full set of controls as main models.

*** p<0.01, ** p<0.05, * p<0.10 142,781 9,156 3,702 645 142,781 9,156 3,702 645 142,781 9,156 3,702 645 Table 4.
2SLS Estimates of Effects of Court-Ordered School Desegregation's Induced-Change in Racial School Integration & Induced-Change in Per-Pupil Spending on the Annual Incidence of Incarceration in Adulthood, By Race Probability(Ever Incarcerated in Adulthood) Prob(Incarceration), ages 18-30 (1) (2) (3) (4) 2SLS Estimates (school segregation & per-pupil spending instrumented using timing of court-ordered desegregation) : School Segregation: Avg Black-White Exposure Index(age 5-17) *Black Avg Black-White Exposure Index(age 5-17) *White School Spending: Ln(Avg Per-Pupil Spending)(age 5-17) *Black Ln(Avg Per-Pupil Spending)(age 5-17) *White 0.1625 (0.4310) 0.2584 (0.4742) 1.2750** (0.5212) 0.4976 (0.6684) -1.1945*** (0.3958) -0.2412 (0.3854) -0.5916* (0.3583) 0.0191 (0.2723) Number of adult person-year observations Number of Individuals Number of Childhood Families Number of School Districts Robust standard errors in parentheses (clustered at school district level).
Includes same full set of controls as main models.

*** p<0.01, ** p<0.05, * p<0.10 -- 4,885 2,015 434 -- 4,885 2,015 434 -- 4,885 2,015 434 0.1078* (0.0572) -0.0226 (0.0282) -0.1047* (0.0563) 0.0277 (0.0304) 96,584 8,539 3,411 524 ONLINE APPENDIX LONG-RUN IMPACTS OF SCHOOL DESEGREGATION ON ADULT ATTAINMENTS * RUCKER C. JOHNSON UC-BERKELEY & NBER * Please direct correspondence to Rucker Johnson (ruckerj@berkeley.edu).
Appendix A: Data Sources A. Desegregation Court Case Data The desegregation court case data contains the universe of desegregation court cases in the US from 1954-90 assembled by the team of legal scholars for The American Community Project in association with Brown University (directed by John Logan).
Every court case is coded according to whether it involved segregation of students across schools, whether the court required a desegregation remedy, and what was the main component of the desegregation plan.

Multiple sources were used to compile the comprehensive desegregation case inventory.
Every case was checked against legal databases, including Westlaw, to confirm the name of the case, the school districts involved, whether the case actually covered the issue of school segregation, whether there was a court-ordered plan, the type of desegregation plan, and the year of the initial court order.

The resultant case inventory is significantly more comprehensive than the one obtained by use of data in Welch and Light (1987) alone.
The total case inventory includes 358 court cases, which resulted in desegregation plans involving 868 school districts.

Structure of Data & Information Compiled for each Court Case:  Case Name:  Year of Initial Decision:  Did the case relate to school segregation?

 Did the court require a desegregation plan, affirm an existing plan, or refer to a previous case requiring a plan?

If so, what did the plan require?


  Description of Court Case:  Current status of this court case, or if there was a plan, the status of the plan (if known):  Year of Current status:  Was there a U.S. Department of Health, Education and Welfare (HEW) action?

 Year of HEW Action:  Description of HEW Action: B. Desegregation Plan Implementation Data I augment this data with major desegregation plan implementation information in large school districts originally compiled by Welch and Light (1987).
Welch/Light investigated desegregation histories of 125 mostly large school districts.

Welch and Light (1987) report the year in which school desegregation was implemented for each school district.

The Welch/Light data cover all districts that in 1968 were 20 to 90 percent minority with enrollments of 50,000+, and a random sample of districts that were 10-90 percent minority with enrollments of between 15,000-50,000.
C. School Data The school quality, teacher salary, and school segregation data covering the period of the 1960s, 70s, and 80s come from four sources: (1) Office of Civil Rights (OCR) of the US Department of Health and Human Services, data for 1968- 1988.

OCR produced data containing school enrollment statistics broken down by race and school segregation indices for a large sample of the nation’s school districts.

(2) Census of Governments, School District Finance Data, 1962-1999.
(3) The Common Core data (CCD) compiled by the National Center for Education Statistics is an annual, national statistical database that contains detailed revenue and expenditure data for all public elementary and secondary schools and school agencies and school districts in the US.
(4) The multiple sources used to compile the comprehensive desegregation case inventory (1954-1990) assembled by the team of scholars for The American Community Project at Brown University included case dockets and bibliographies for all desegregation court orders from the Department of Justice, NAACP Legal Defense Fund, and the US Department of Education (Logan et al., 2008).
I have merged this desegregation court case data and information on major plan implementation year with district-level enrollment data from the Office of Civil Rights (OCR) Data and Common Core of Data and as collected by Welch and Light for the Office of Civil Rights.

The enrollment data is used to calculate school segregation dissimilarity and exposure indices.

I am grateful to Sarah Reber for sharing the OCR school data with me (as described further below).
Per-Pupil Spending Data The data from the Historical Database on Individual Government Finances (INDFIN) represents the Census Bureau’s first effort to provide a time series of historically consistent data on the finances of individual governments.

This database combines data from the Census of Governments Survey of Government Finances (F-33), the National Archives, and the Individual Government Finances Survey.

The School District Finance Data FY 1967-91 is available annually from 1967 through 1991.
It contains over one million individual local government records, including counties, cities, townships, special districts, and independent school districts.

The INDFIN database frees the researcher from the arduous task of reconciling the many technical, classification, and other data-related changes that have occurred over the last 30 years.

For example, this database includes corrected statistical weights that have been standardized across years, which had not been done previously.
Furthermore, although most governments retain the ID number they are assigned originally, there are circumstances that result in a government's ID being changed.

Since a major purpose of the INDFIN database is tracking government finances over time, it is critical that a government possess the same ID for all years (unless the ID change had a major structural cause).

For example, All Alaska IDs were changed in the 1982 Census of Governments.
In addition, new county incorporations, where governments in the new county area are re-assigned an ID based on the new county code (e.g., La Paz County, AZ), cause ID changes.

Thus, if a government ID number was changed, the ID used in the database is its current GID number, including those preceding the cause of the change, so that the ID is standardized across years.
In addition to standardizing the data, the Census Bureau has corrected a number of errors in the INDFIN database that were previously in other sources of data.

For example, for fiscal years 1974, 1975, 1976 and 1978 the school district enrollment data that had previously been released were useless (either missing or in error for many records).

Thus, in August 2000, these missing enrollment data were replaced with those from the employment survey individual unit files.
This enables us to more accurately compute per pupil expenditures for those years.

In addition, source files before fiscal 1977 were in whole dollars rather than thousands.

This set a limit on the largest value any field could hold.

If a figure exceeded that amount, then the field contained a special "overflow" flag (999999999).

Few governments exceeded the limit (Port Authority of NY and NJ and Los Angeles County, CA are two that did).
For the INDFIN database, actual data were substituted for the overflow flag.

Finally, in some cases the Census revised the original data in source files for the INDFIN database.

In some cases, official revisions were never applied to the data files.

Others resulted from the different environment and operating practices under which source files were created.

Finally, some extreme outliers were identified and corrected (e.g., a keying error for a small government that ballooned its data).
The Common Core of Data (CCD) School District Finance Survey (F-33) consists of data submitted annually to the National Center for Education Statistics (NCES) by state education agencies (SEAs) in the 50 states and the District of Columbia.

The purpose of the survey is to provide finance data for all local education agencies (LEAs) that provide free public elementary and secondary education in the United States.
Both NCES and the Governments Division of the U.S. Census Bureau collect public school system finance data, and they collaborate in their efforts to gather these data.

The Census of Governments, which was recorded every five years until 1992, records administrative data on school spending for every district in the United States.

After 1992, the Public Elementary-Secondary Education Finances data were recorded annually with data available until 2010.
I combine these data sources to construct a long panel of annual per-pupil spending for each school district in the United States between 1967 and 2010.

Per-pupil spending data from before 1992 is missing for Alaska, Hawaii, Maryland, North Carolina, Virginia, and Washington, D.C. Per-pupil spending data from 1968 and 1969 is missing for all states.

Spending data in Florida was also missing for 1975, 1983, 1985-1987, and 1991.

Spending data in Kansas was also missing for 1977 and 1986.
Spending data in Mississippi was also missing for 1985 and 1988.

Spending data in Wyoming was also missing for 1979 and 1984.

Spending data for Montana is missing in 1976, data for Nebraska is missing in 1977, and data for Texas is missing in 1991.

Where there was only a year or two of missing per pupil expenditure data, we filled in this data using linear interpolation.
D. Sources of Data on Segregation I use data from the surveys conducted by the Office of Civil Rights (OCR) of the Office of Education to estimate the measures of segregation for school districts from 1968-1988.

The exposure of blacks to whites is the percent white in schools, weighted by black enrollment and vice-versa for exposure of whites to blacks; data on racial composition at the school level are required to calculate these indexes.
I obtained from Sarah Reber the original binary EBCDIC data files for the OCR surveys for 1968-1974 and 1976 (the survey was not conducted in 1975), who converted the files to ASCII for analysis.

Similar school-level data on students and teachers by race were published for 1967 by the Office of Education; these data were entered for analysis.

The exposure indexes where then calculated based on the school level enrollment by race.
The OCR surveys were not comprehensive in all years, but the large size of school districts and the heavy representation of districts that had involvement of the courts in desegregating its schools ensured that most districts with significant minority student enrollment were included in the data in most years.

Before the 1967 school year, no school-level data on enrollment by race are available.
As aforementioned, the data on school district spending, student enrollments, and numbers of teachers are obtained from the Census of Government (COG) for the available years from 1962-92.

I use the version of the COG contained in the Historical Database on Individual Government Finance -- a longitudinally consistent version of the COG produced by the Census Bureau.

The COG data are organized at the level of the school district.

These figures are converted to 2000 dollars using the CPI-deflator.
Per-pupil school expenditures is total expenditures by the district divided by total student enrollment.

Data on student-teacher ratios at the school level are not available before 1968.

Student-teacher ratios by race are calculated from Office of Civil Rights (OCR) data.

The OCR data (described below) contain information on the number of teachers in every school, as well as the number of black students and the total number of students.
To calculate the black student-teacher ratio for 1970-1972, I calculated the student-teacher ratio (total students, any race, divided by total teachers, any race) in every school; I then calculated the weighted average student-teacher ratio for schools in each district, with black enrollment in the school as weights.

For example, the analyses that analyze desegregation effects on average class size by race using school-level data, include 14,869 schools from 667 districts from 33 different states.
The demographic data on districts/counties are obtained from the 1960, 1970, 1980 and 1990 decennial censuses.

I use versions of the census data summarized at the geographic level of the census tract.

Hospital Desegregation Data Hospital Desegregation.

The desegregation of hospitals in the South can be initially dated from 1964 when federally-mandated policies began to be enforced.

In particular, developments in all three branches of government—judicial, executive, legislative—were influential.
First, Hill-Burton Act’s ‘separate but equal’ clause was ruled unconstitutional in 1963.

Second, Title VI of the Civil Rights Act of 1964 put teeth in enforcement.

Third, with the introduction of Medicare in 1965, a hospital had to be racially desegregated in order to be eligible to receive Medicare funding.
The staggered timing of hospital desegregation in the South led to differences in the timing of improved access to hospital care for minorities, and resulted in timing differences in the implementation of Medicare in parts of the South that had not desegregated their hospitals prior to 1965.
Using the American Hospital Association’s Annual Survey of Hospitals (spanning the period 1946-1980) along with the Centers for Medicare Provider of Service data files dating back to the early 1960s to identify the precise date in which a Medicare-certified hospital was established in each county of the US (an accurate marker for hospital desegregation compliance), I find that ¼ of counties in the South—and 75 percent of counties in the Mississippi Delta—lacked a Medicare-certified hospital by the end of 1966.
Almond, Chay, & Greenstone (2008) and Finkelstein and McKnight (2008) have independently used this type of data previously to measure the timing of hospital desegregation.

I also construct measures of the individual’s age at which hospital desegregation occurred and a race-specific distance to the nearest hospital as an index of segregation and access during childhood (created using GIS mapping technologies and historical hospital address and childhood residential location information).
E. County Head Start Spending & Public Transfer Program Data I use administrative data about county-level Head Start expenditures (1965-80) with single-age county- level population counts (SEER Population Data, 1969-1999).

In particular, PSID data are linked to county Head Start spending during the first 15 years of the program, when these individuals were 3-5 years old, acquired from the National Archives and Records Administration (NARA).
This historical county-level data enables me to compile an estimate of Head Start program expenditures per poor 4-year old in the county for each year between 1965 and 1980.

Special thanks to Doug Miller and Martha Bailey, who helped me compile this information and confirm the accuracy of it, and the rollout of community health centers.

I am grateful to Doug Almond, Hilary Hoynes, and Diane Schazenbach for sharing the Regional Economic Information System (REIS) data for the 1959 to 1978 period.
Per capita county transfer payments include measures for public assistance (AFDC, General Assistance, Food Stamps), medical care (Medicare, Medicaid, military), and retirement and disability benefits.

F. Pre-Existing County Characteristics The pre-existing demographic, socioeconomic, and school-related characteristics at the county level were obtained originally from the county tabulations of the 1960/2 Census, were taken from the City and County Databook.
G. Matching PSID Individuals to their Childhood School Districts In order to limit the possibility that school district boundaries were drawn in response to school desegregation, I utilize 1969 school district geographies.

The “69-70 School District Geographic Reference File” (Bureau of Census, 1970) relates census tract and school district geographies.

For each census tract in the country, it provides the fraction of the population that is in each school district.
Using this information, I aggregate census tracts to 1970 district geographies with Geographic Information Systems (GIS) software.

I assign census tracts from 1960, 1970, 1980 and 1990 to school districts using this resulting digital map based on their centroid locations.
I also use the full universe of school addresses (1970 Elementary & Secondary General Information System (ELSEGIS) Public School Universe Data) and map them to PSID childhood addresses (census blocks) to identify the closest neighborhood school in the district using GIS mapping technologies.

To construct demographic information on 1970-definition school districts, I compile census data from the tract, place, school district and county levels of aggregation for 1960, 1970, 1980 and 1990.
I construct digital (GIS) maps of 1969 geography school districts using the 1969-1970 School District Geographic Reference File from the Census.

This file indicates the fraction by population of each census tract that fell in each school district in the country.

Those tracts split across school districts I allocated to the school district comprising the largest fraction of the tract’s population.
Using the resulting 1970 central school district digital maps, I allocate tracts in 1960, 1980 and 1990 to central school districts or suburbs based on the locations of their centroids.

The 1970 definition central districts located in regions not tracted in 1970 all coincide with county geography which I use instead.
The school data from the OCR, Census of Governments, and Common Core of Data are merged to the individual-level geocoded version of the Panel Study of Income Dynamics for original sample children based on the census block where they grew up.
Based on the school district of upbringing, I compute for each individual the average per-pupil school spending, student-to-teacher ratio, and school segregation levels experienced during their school-age years (as well as averaged over their adolescent years (ages 12- 17)); similarly I compute for each individual the county per-capita transfer payments from income- support programs averaged over their school-age and adolescent years.

Figure A0.

ONLINE APPENDIX Figure A1.
ONLINE APPENDIX School Desegregation Court Order & Plan Implementation Dates School Desegregation Court Order Dates 160 140 120 100 80 60 40 20 20 15 10 5 0 54 55 56 57 58 59 60 61 62 63 64 65 67 66 70 68 Initial Year of Court Order 69 71 72 73 74 75 76 77 78 79 80 81 82 Non-South South School Desegregation Major Plan Implementation Dates 54 55 56 57 58 59 60 61 62 63 64 65 66 67 68 Implementation Year 69 70 71 72 73 74 75 76 77 78 79 80 81 82 Non-South South (1)Desegregation Court Case Data: universe of districts ever subject to court orders (N=868), Brown Univ/American Communities Project.
(2)Major Plan Implementation Dates: Welch/Light data from 125 large school districts.

FIGURE A2.

GEOGRAPHIC TIMING OF COURT-ORDERED SCHOOL DESEGREGATION 1954 – Brown v BoE 1959 1963 ONLINE APPENDIX 1970 1975 1990 The Geographic Timing of Court-Ordered School Desegregation in the U.S.

Figure A2b.
ONLINE APPENDIX # # # # # # # ## # # # # # # # # # # # ## # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # ## # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ## # # # # # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # ## # ## ## # ## # ## # # # ### ### # ## # ### ## #### # # # ## ## # # ## ##### # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # #### # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # ## # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # ## # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # ## # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # #
 # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # 900 # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # 0 # # # # # # # # # # # # # # # ### # # # # # # # # ## # ## # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # ## # # # # # # # # ## # ## # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # ## # # # # # # ## # # # ## ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # ## # # # ## # # # # # # ## # # # # ## # # # # # # # # # ## # # # # # # # # # ## # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ## # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # ## ## # # # # # # # # ## # # # ## # # ## # # # # # # # # # ## # # # # # # # # # # ## ## # # # # # ## # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # ## # ## # # # # ## # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # ## # # #
## # # # # # # ## # ## # # # # # # ## # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ### ## ## #### ###### # ## # # # # ## # # # ### # ## ## # #### # ### ## ## # ##### # # # ## # ## # ## ### ## # #### # # ## ## # ## ### # # # ## # ## ### # ### # # # ## # # #### ## ### # # # # # # # # ## # # # #### # # # # # ## # # # # # ## ## # # #### # # # # # # ## # ## # # # ### # ## # ## ### ## # ### # # # ## # # ### #### # ## # ## # # # # # ### # # # # # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # # # ## # # # # # # # ## # # ## ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # ## ## ## # # # ### # # # # # # # # # # ## # ### ## # # # ### # # # ## ## # # # # ## # ## # # # # # # # # # # # # # # # # # ######## #### # # # # # # # # # # # # ## ## # # ### # # # # ## # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # ### # # # # # # # # # # # # # # ### ### # # # # # # # # # ## # # ## # ## # # # # # # # # # # # # # # # # # # # ## # # ## # # # # # # # # # ## # # # # # # # # # ## # # # # # # # # # # # # # # # ## # ### # # # # # # # # # # # # # ## # # ## # # # # ## # # # # ## # # # ## # # # # # ### # # ## # # # # # ## # # # # # # # # # ### # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # PSID Black Children (Red Dot) # 1 Dot = 1 PSID White Children (Blue Dot) # # # # # # # # ## # ## # # # ## # # # # ## # # # ## # # # # # ## # # # # # # # # ## # ## # # # # # # # ## # # # # # # ## # ### # # # # # # # ## # # # ## # # # # # # # # # # ## # # # ## # # # # # # # ## # ## # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # ## # # # # ## # # # # # ## # # # # # # # # # 1 Dot = 1 States # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # ##
 # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # ## # # ## # # # # ## # ## # # # # ## # # # # # # # # # # # # ## ## # # # ### # # # # # # # # # # ## # # # # # # ## # # # ## # # ## # ## # # ## # # ## # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # ## # ## # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # ## # # # # ## # # ## # # # # # ## Year of Initial Court Order No Court Order 1952 - 1964 1964 - 1968 1968 - 1969 1969 - 1970 1970 - 1974 1974 - 1980 >1980 # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # W 1800 Miles N S E # 900 Figure A2c.
ONLINE APPENDIX The Geographic Timing of Implementation of Court-Ordered School Desegregation Plans in Large Districts # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # ## # ### # # ### ## # # # ## ## # # # # # # # # # ## # # # # ##### # # ### # # # # # # # # # # # # # # # # # # # # # # # ## # # # # ## # ## # # # # # # # ## ### # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # ## ## # # # # # # # # ## # # ## # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # ### # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## ## # # # ## # ## # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # #
# # # # # # # # # # # # # # # # # # # # # # # # # # # # 1000 # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # ## # # # # # ### # # # ## # # # # # # # # # # # # # # # # 0 # # # ## # # # # # ## # # # ### # # # ## ## # # # # # # ## # # # # # # # # # # ## ## # # ##### ## # # # # # ## # # ## # # # ### # # # # # # # ## # # # # # # # # # # # ## # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # ## # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ### # # # # # # # # # # # # # # # # # # # # # # # # # # # # # #### ## # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # ### # ## # # # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # ### # # # # # ## # # ## # # # # # # # # # # # # ## # ## # # # # # # # # # # # ## # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # ### # # # ## # # # # # # # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # ## # # # # # # ## # # # # # # # # # ## # # # # # ## ### # ## # # # # ### # # ## # # # # ## ## # # #### ## ## # # ## # # ### ## # # # # # # # # # # # # # # # # # ## # # ## # # # ## ###### # # # ### # # # # # # # ########### #### ## #### # # # # # # # # # # # # # ## # ## # # # # # # # # # ## # # # # # # # ## #### # # # # # # # # # # # ## ## ## # ## # # # # ## # ### ## # # # # # # # ### # # # # # # # ## # ## # # # # ### # # # # # # ## # ## # # # #### # ## # # ## # # ## # # # ##### # # # #### ### ## # # ### # # ## # # ### ## ## # # # # # # # # # ##
### # # ## ### # # ## ###### # # # ###### ## ### # # ## # ### # # # # ## # # # ## # # # # ## # # # ## # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## ## # # # # # # # # ## # # # # # ## PSID Black Children (Red Dot) # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # ### # # # # ## # # # # # # # ### # ## ## ### ## ## # # # # # # # # # ## # # # # ## # # ## # # # # # # # # # # # # # # # ## # # # # # # ## ## # # ## # # ## # ## # # ## # # # # # # # # # # # # # # # ## # # # # # # # ### # # ## # # # # ## # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # ## ## # # # # # # # ## # # # # ## # # # # # # # # ### # # # # # ## # # # # # # ## # # # # # # # # # # ## # # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # ## # # # # # ## # ## # # # # # # ## # # # ## ## # # # # ## # # ## # # # # # # # # # # ## # ## # # # # # # # # # # # ## ## # # # # # # # # #### # # # # # # ## ## # # # # # # # ## # # # ## # # # # # # # ## # # ## # ## # # # # # # # # # # # # # # # # # ## # # ### # # # # # # # # # # ### # # # # # # # # # ## # # ## # # # # # # # ## # ## # ## # # # # # # # ## # # # # # # # # ## # # # # # # # # # # # # # # # # # # ### # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ### # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # ## # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # ## # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # ## # # # # # # # # # # # # # # # # # # ### ## ## # # # # # # # # # # # # # # # # # # # ## # # ### # # # # # # ## # # # # # # # # # # # # ### # # # # # # # # # # # # # # ## # # # ### # # # # ## # # # # # # # # # ## ## # # # # # # # # # # ##
# # # # # # # # # # # # # # # # # # # # # # ## # # # ## # # # # ## # # # # # # # # # # # ### # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # ### # # # # # # # # # # # # # ## # # # # # # # ## # # # # # # # # # ## # # # # # # # # # ## # # # # # # # # # ## # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # ## ## # # # # # # # # ## # ## # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ### # # ## # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # ## # # # # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # ## # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # # # # ## # # # # # # # # # # # # ## # # ## # # # # # # # # ## # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # ### # # # # # # # # # ## # # # # # 1000 # 1 Dot = 1 PSID White Children (Blue Dot) # 1 Dot = 1 States Year of Major Plan Implementation No Major Plan Implementation 1954 - 1964 1964 - 1968 1968 - 1969 1969 - 1970 1970 - 1974 1974 - 1980 >1980 W 2000 Miles N S E Figure A3.
Geographic Variation in School Spending in the U.S. in 1962 ONLINE APPENDIX # # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ### # # ## # # # ## # ## # # # # # # # # # # # # # ## ### # # # ### # # # ## # # # # # # # # # # # # # # # # # # ## # # # # # # # # ## # # # # # # # # # # # # # ## # # # # # # # # # # # # # # ## # # # # # # # # # ## # # # # ## # ## # # # ## # # # ## # # # # ### ## # ## # # # ### # # # # # # # # # ## # # ## # # # # # # # # # # # # # # ## # # # # # # # ## # ## # # # # ## ## # ## ### ## ### ## ## # # ## # # # # # # ## ## ## ## ### # # # # ## # # # # # # ## # # # ## # ## ### ## # # # # ### # # # # # # # # # # # # # # # # ## # ### ## ## # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ## # ## # ### # # # # # ### # # # ## # ## ## # # ## # ## # # ### ## # # # # ### #### #### # ## # ### #### ### # ### ### # ## # ## # # ## # # ## #### ## # # ### # ## # ## ### ## # ## # # ## # # ## # ### # # # # # # # # # ## ### # # # ### ### # # # # # # ### ### # # ### ## ###### #### ## # ### #### ### ### # # # ### # # # # ## # # # ## ## ## ### ### ## # ## ## ## ### # # # # ## ### ## # ## # # # ## # # # # # ## ## ## # # # # # # # # # # # ## # # # ### # ## ## # # # # # ## # # # ## ## # # ## # # ## # ## # # ## # # # ### # # # # # # ## # ## # ### # # ## # ## ## # ## # # ## # # # ## # # # # # # ## # # # # ## # # ## # # # ## ## # # # # ## # # # ## ### # ## ## # # ## ## ## # ### ### # # # # ## # # ## # # # ## # #### ### # ### # # # ## # # # ### # # # # ## ## # # ## # # # #### ### #### ### # # ## #### # # # # ### ## # # # ## ## # # ## ## # # # ## # # # # # # # ### ## ## ## # # # ## ## # # # ## # ## # ## # # # ## # #### ## # # ## # ## #### ### # ## # ### # # ## #### # ## # # # # ### ## # # ## # ## ### # # # # # ### # # ## # #### # # # # ### ## ### # # # ## ## # ## # # # # ### # ### # ### ##
 ## # ## # # ## # # # ## ### ##### ## #### # ## ### ## # # # ## # # # ## ### # ## ## # # # # # # # # ## ### # ## ### # # ### ## # #### # # # # # # # # ## # # # # ## # # # # ## ## # ## ## # # # ####### ## # # # # #### # #### # # # # ## ## ## # ## ## ### # ### # ## # ## # ## # #### # ## ## ## # # # # # # # ### ## ##### # # # # # # # ## ## # # # # # # # ## # ## # # ## ## # # ## # # ## ## # ## # ### # # # # ## # ## # # # # # # # ## ### # ### # # ## # ### ## ## # # # ### # # # # ## # ## # ## ## # ## #### ### # # ### # # # # ## # # ### # # # ## ##### ### ## ## ### # ### # # # ## ## ## ## # #### ## ## # # # # # # ### ## # ### ##### # ### ## # ### # # # # # # # # ### #### ## # # # # # # # ## # # # # # ## # ### ### # ## ### # # # # ## # # ## ## # # ## ## # # # # # ### # # # # # ## ## ## ## # # ## # # # #### # # # ## # # # ## ## # # # # ### # # # # # ### # # # # ## ## ## # # ## ## # ## # # # # #### # # ## # ## # ### # # # # ## # # # # ### # # # # # ## ## # # ## # # ## # ## ### # # # # # # ### # # ###### ## ### # # # # # #### # # # ## # ## ## # # # # # # # # ## # # ## ### # # # # # ### # ## # # ## # # # # # ## # ## ## ## # # ## # # ## # ## ## ## # # # # # # ## ## ## # # # ## # # # # # # # # # # # # # # # # # # # # ## ## # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # # ## # # # # # ## # # # # # # # # # # # # # # # # # # ## # # # # # # # # # # # # # # # # # # # # # # ## # # ### # # # # # # # # # 900 0 900 1962 County Minority Population (per 100 residents) # 1 Dot = 15 States 1962 County Per-Capita School Spending <$1,440 $1,440 - 1,779 $1,779 - 2,065 $2,065 - 2,426 >$2,426 W 1800 Miles N S E FIGURE A4.
US COUNTY POVERTY RATES in 1960 Among the 300 poorest counties 2.1 – 20.99 21 – 31.29 31.3 – 45.62 45.63 – 93.07 FIGURE A5.

COUNTY POPULATION: PERCENT AFRICAN AMERICAN - 1960 Less than 10% 10 to less than 25% 25 to less than 50% 50% or more APPENDIX B: A BRIEF HISTORY OF US SCHOOL DESEGREGATION Background.

Residential segregation may affect access to quality schools and subsequent mobility by reducing school resources (e.g., school district per-pupil spending, class size, teacher quality).
During the 1950s, 60s, and 70s when the individuals in the PSID sample were school-age, there was substantial variation across districts in school quality inputs (e.g., per-pupil spending, pupil/teacher ratio…).

During this time period, there was limited state support for K-12 education (in the vast majority of states) and a heavy reliance on local property taxes.
During the 1960s and 70s, states, on average, contributed roughly 40 percent of the cost of K-12 education, and much of this aid was a flat per pupil payment that was not related to local property wealth of the district (National Center for Education Statistics).

Before school desegregation plans were enacted, school district spending, particularly in the South, was directed disproportionately to the majority-white schools within districts, something which is not evident from district-level spending data.
While the premise of the 1954 Brown decision was “separate is inherently unequal”, the Brown decision alone was not sufficient to compel school districts to integrate.

Minimal school desegregation occurred in the 1950s and early 1960s following the Brown I and II rulings issued in 1954 and 1955.

Most school districts did not adopt major school desegregation plans until forced to do so by court order (or threat of litigation) due to individual cases filed in local Federal court.
Civil rights organizations avoided taking on legal cases early on that had a high risk of failure, even if the potential local benefits were large.

The cascading impacts that would accompany legal victory due to the role of precedent juxtaposed with the potential risks of losing outweighed considerations of where targeted efforts would have the greatest impacts or where impacts would be felt for the largest number of blacks in the short-run.
As the recorded legal history of desegregation documents, the legal arm of the NAACP (Legal Defense & Educational Fund)…“followed a strategic approach that rejected simple accumulation of big cases, in favor of incremental victories that built a favorable legal climate…” (Council for Public Interest Law, 1976, p.37).i Guryan (2004) presents this intuition formally in a model that demonstrates that in an environment in which precedent has a strong effect on the subsequent probability of success, an agent with the objective of desegregating the nation’s schools should optimally choose to prioritize the likelihood of success almost to the exclusion of any local benefits of desegregation when choosing where to bring litigation.
Timeline of School Integration in the US At the time of the Brown decision in 1954, seventeen southern states and the nation’s capitol required that all public schools be racially segregated (Figure A0).

The Supreme Court did not set a time table for dismantling school segregation and turned the implementation of desegregation over to US district courts.
The aftermath of Brown and process to see desegregation established in public schools can be characterized as consisting of several developmental periods—from neonatal and infancy (1954- 65) to adolescence (1966-75) and young adulthood (1976-1989).

The post-Brown era up through the mid-to late 1980s can be codified by two distinct periods: pre- and post-1965.
The 1954-65 period was characterized by Southern states’ intent to thwart implementation of Brown and resist compliance with the desegregation orders.

The South’s massive resistance to the Court’s rulings ensued for the next 10 years and the delay tactics were initially very successful.

The case-by-case litigation approach largely failed during the first decade following Brown.
Legal scholar Walter Gellhorn described the pace of desegregation during these years as that “of an extraordinarily arthritic snail” (cited in Wilkinson, From Brown to Bakke, p. 102).

By 1965, only 2 percent of African American children in the Deep South attended integrated schools and more than 75 percent of the schools in the South remained segregated.
Landmark Court Decisions on the Road from Segregation to Desegregation & Integration Enforcement of desegregation did not begin in earnest until the mid-1960s.

State and federal dollars proved to be the most effective incentives to desegregate the schools.
A critical turning point was the enactment of Title VI of the 1964 Civil Rights Act (CRA) and Title I funds of the 1965 Elementary & Secondary Education Act (ESEA), which prohibited federal aid to segregated schools and allowed the Justice Department to join suits against school districts that were in violation of the Brown vs. Board order to integrate.
The congressional enactment of ESEA was among the most important events in effecting compliance because it dramatically raised the amount of federal aid to education; from a few million to more than one billion dollars a year; and, for the first time, the threat of withholding federal funds became a powerful inducement to comply with federal desegregation orders (Cascio et al., 2010; Holland, 2004).
Figure A3 presents a map of the geographic variation in school spending in the US in 1962 overlaid with the residential locations of minorities in that year.

The map illustrates the concentration of minorities in the South where school district per-pupil spending levels were lowest.
Another example of how financial incentives played a role in facilitating compliance is evident in President Nixon’s proposal to provide financial incentives to school districts to comply with desegregation orders, which led to congressional enactment of the Emergency School Aid Act of 1972 to assist the federal courts in achieving desegregation (Ehrlander, 2002, p. 23).

Federal dollars soon constituted 30 percent of the budget of many Southern school systems.
The availability of federal money continued to influence desegregation into the 1980s.

I find a significant correlation in the amount of federal funds received by school districts in the years 1966-1970 with the percentage of black students enrolled in previously all- white schools.

The landmark court decision of 1968 in Green v. School Board of New Kent County required immediate actions to effectively implement desegregation plans that promised to work right away.
The 1968 Green decision led to an acceleration of desegregation activity and set the pattern for a number of court-orders and desegregation plans that followed in many other districts across the country.

Following the Supreme Court ruling in Green, the various Courts of Appeals held that desegregation plans based on “freedom of choice”, or zoning which followed traditional residential patterns, were inadequate and deemed no longer acceptable.
School desegregation encompassed not only the abolition of dual attendance systems for students, but also the merging into one system of faculty, staff, and services, so that no school could be marked as either a ''black'' or a ''white'' school.
In 1970, the Court approved busing, magnet schools, and compensatory education as permissible tools of school desegregation policy (Swann v. Charlotte-Mecklenberg Board of Education), and the ruling was among the first attempts to implement a large-scale urban desegregation plan.
Schools in other regions of the country remained segregated until the mid-1970s and these districts began accelerating school desegregation efforts after the 1973 Keyes vs. Denver School District decision (413 U.S. 189), which ruled that court-ordered litigation applied to areas which had not practiced de jure segregation.

This case was the first involving school desegregation from a major non-Southern city, and it marked the beginning of large-scale desegregation plans in regions outside the South.
The case also ushered in a period of equal desegregation efforts in both the North and the South, regardless of whether the school segregation resulted from state action (legal mandate) or residential segregation patterns.

Desegregation cases began to expand explicit goals beyond racial integration to include goals of promoting adequacy of school funding for minority student achievement.
The 1977 Milliken II decision allowed courts to mandate spending on compensatory educational programs for minority students.

This occurred in Los Angeles and Detroit, for example.

No other important court decisions occurred between 1975 and 1990.
School Desegregation Data: The Nature, Pattern, and Timing of Initial Court Orders & Implementation Most previous studies have not had access to data on the nature and timing of desegregation policy and action, and have been limited primarily to an examination of "white flight" and/or have been geographically limited.
I provide analysis of school desegregation policy to describe aspects of the nature and timing of steps taken to desegregate the schools, which is instructive for the empirical approach pursued to identify its impacts.

Extent of Desegregation Actions (post-1965 period).

Substantial steps to desegregate schools during the period 1966-75 are reported in an estimated 1,400 school districts.
While these districts represent a small proportion of the 19,000 school districts in the country, they encompass about half of the minority public school children in the country.

Although the actions to desegregate were most heavily concentrated in the Southern and Border States, such actions were found in a moderate number of districts in other regions of the country as well.

Nature of Pressure to Desegregate (pre- vs. post-1965 period).
In many districts, desegregation was a process that came as a result of pressures from many sources.

As the major impetus, court orders were most often reported in districts with high initial levels of segregation and with moderate-to-high proportions of minority students.

Districts which desegregated under local pressures generally had low initial levels of segregation and low proportions of minority students.
Figure A1 presents the dates of initial court orders and resultant major school desegregation plan implementation across the country among the 868 school districts that introduced such plans between 1954 and 1980.

In the South, the largest share of school districts desegregated over the five-year period between 1968 and 1972, and school segregation declined to a far larger extent in the South relative to the rest of the country over this period.
Most desegregation plans implemented prior to 1965 were minor (referred to as “freedom of choice” plans), were not strictly enforced, and achieved only token levels of integration.

My focus will be on the impacts of major desegregation plans whose implementation accelerated after 1965 coupled with actions spurred by the 1968 Green decision.

The desegregation activity that took place after 1965 was in stark contrast with that of earlier years.
As shown in Figure A1, the change in the pace of desegregation litigation activity and plan implementation after 1965 is striking.

Many districts took steps overnight that changed the school systems from being predominantly segregated to predominantly desegregated.

These steps were often taken subsequent to a specific court order or following direct threat from the US Department of Health, Education, and Welfare (HEW) to cut off Federal funds.
The nature of timing of initial court litigation was highly idiosyncratic.

Court-ordered desegregation by legal mandate is plausibly more exogenous than other more voluntary forms of desegregation.

The extent of voluntary desegregation prior to court intervention varied across districts, but voluntary action of districts was more endogenous.
As well, anti-integration groups can delay major desegregation plan implementation by lengthening the court proceedings or by implementing inadequate desegregation plans; thus, the timing of initial court orders is likely more plausibly exogenous than the actual implementation date of major desegregation plans (additional evidence provided near the end of this Appendix).

In Figure B6, I present evidence on the length of time between initial court order and major desegregation plan implementation.
We see this lag exhibits a clear structural break in 1965 (Figure B6).

Namely, the results suggests that for initial court orders meted out after 1965, there is roughly immediate implementation (on average, major plan implemented within 1-2 yrs of initial court order); and the lag does not differ over time for court orders after 1965.
On the other hand, for initial court orders meted out before 1965, there is more than a 10-year delay in implementation of a major plan (following initial court order, major plan is not implemented, on average, for 10 years; there is a systematic long delay that decreases in years leading up to 1965.

During the 1955-64 period (after Brown but prior to the passage of the Civil Rights Act), the earlier the initial court order, the longer the delay in implementation of a major plan.
This pattern and discontinuity after 1965 in the time lag between initial court order and major desegregation plan implementation occurs in the South and non-South.

In 1964, 1 percent of African American students in the South attended school with whites; by 1968, this had risen to 32 percent.

As shown in Figure A1, the ensuing years of 1968-1972 bracket the period of maximum desegregation activity.
Figure A2 presents a map that summarizes the overall geographic pattern and timing of initial court orders overlaid with the childhood residential locations of the (nationally-representative) PSID sample of black and white children in 1968 (Figure A2b); and, analogously, Figure A2c shows this for the resultant subsequent major desegregation plan implementation in US school districts/countiesii (among the subset of districts for which this information is available).
The figures demonstrate the strong overlap of residential locations of original sample PSID children with districts that underwent court-ordered desegregation.

In the figure, districts that were subject to court orders are shaded (no shading indicates no court- ordered desegregation); the shading of the districts/counties is assigned by its initial court order date, with darker shading denoting a later initial court ruling.
The lightest gray represents communities in which the initial court order occurred between 1954 and 1963—the early desegregation period; and the next darkest gray shades denotes communities in which the initial court order occurred between 1964-1968 during the expansion of federal enforcement as a “national emphasis program” and under Title VI of the 1964 CRA and Title I of the 1965 ESEA; the next darkest grays indicate communities in which the initial court order occurred between 1968 and 1972 during the expansion following the 1968 Green Supreme Court ruling; the darkest gray and black represent the corresponding smaller number of communities in which the initial court order occurred between 1974 to 1980 and after 1980, respectively.
Not surprisingly, the concentration of activity occurred in places with at least a 20 percent black population.

A substantial portion of the US population of minority children in 1960 lived in the shaded 868 districts/counties that eventually were subject to court-ordered desegregation.
As shown, districts exhibit a great deal of variation in the year in which the initial court order was issued and the subsequent timing when major desegregation plan implementation actually took place; this variation is evidenced both within and across regions of the country.
In most regions, the initial court order took place in a narrower period than the 30-year period observed in the country as a whole; similarly, the span in timing of major desegregation plan implementation is narrower within regions than across the country as a whole.

The regional pattern and clustering reflects the evolution of legal precedent.

Figure B5 highlights the significant birth cohort variation in childhood exposure to court- ordered school desegregation for the PSID sample.
The share of children exposed to school desegregation orders increases significantly with year of birth over the 1945-1970 birth cohorts analyzed in the PSID sample.

Only token desegregation efforts occurred prior to the passage of the 1964 Civil Rights Act.

The figure shows that litigation and desegregation plan implementation accelerated substantially between 1964 and 1972.
For example, only 6 percent of the districts that would eventually undergo court-ordered desegregation had implemented major plans by 1968 (when the PSID began); by 1972 this rose to over 56 percent.

It is this period of substantial growth in litigation activity, spurred by landmark court cases like the 1968 Green decision, that forms the basis of the research design.
By 1976, 45 percent of the South's African American students were attending majority-white schools, compared with just 28 percent in the Northeast and 30 percent in the Midwest.
The process became highly decentralized with a diverse set of agents that initiated court litigation following the Brown decision, which also contributed to the idiosyncratic nature of the timing and location where legal challenges arose that resulted in initial court orders.iii Differences across districts in when desegregation court cases were first filed and the length of time it took these cases to proceed through the judicial system represents a plausibly exogenous source of identifying variation in the timing of school desegregation.
The exogeneity of this timing is supported theoretically by the documented legal history of school desegregation and by my own empirical examination of the issue below.

The primary identification strategy uses this variation in the timing of major desegregation plan implementation that was induced by differences in the year of the initial court order.
Systematic variation in desegregation plan adoption could lead to spurious estimates of the plans’ impact if those same school district characteristics are associated with differential trends in the outcomes of interest.

To explore this, I compiled characteristics of school districts in 1962, prior to the surge of court-ordered desegregation cases and significant integration efforts that ensued in subsequent years (of the same decade).
I use these “pre” characteristics to predict the year in which the initial court order took place and the year in which the school district actually implemented a major desegregation plan, respectively.
The 1962 county measures used as independent variables in the model include: the log(county population), percent of the population that is minority, per-capita school spending, the percent of school spending that comes from intergovernmental grants (state/federal), median income, percent of households with income <$3,000 (in 1961 dollars), percent of households with income >$10,000, percent with 12 or more years of education, population change between 1950-60, percent of residents in an urban area, percent of residents in rural or farm area, percent of residents living in group quarters, median age, percent of residents that are school-age, percent of residents 65 or older, percent of residents that voted for the incumbent President, and the county mortality rate (all constructed from the 1962 Census of Governments, City & County Data Book).
I include the size of the population to capture the fact that large districts/counties may face differential costs and opposition to the desegregation process.

I also estimate an alternative model specification that includes the 1962 average student-to-teacher ratio and average teacher salary, instead of the per-capita school spending level (as shown in Table B1, similar patterns emerge).

These data are linked with the desegregation court case and plan implementation data.
Columns (1)-(6) of Table B1 presents estimates from least-squares regressions of the year each school district had an initial court order (among those that first became subject to court order after 1962) on 1962 characteristics and region fixed effects, while the final two columns ((7)-(8)) use the same set of independent variables to examine determinants of the delay between the initial court order and major desegregation plan implementation (in years).
Column (1) shows estimates for the full sample, column (3)-(8) show results for the subset of counties in which original sample PSID children grew up, and columns (5)-(8) display results for the subsample of counties for which information is available on the dates of major desegregation plan implementation.

The magnitude of the association between the school district characteristics and the year of the initial court order is weak.
I find that districts that had either significant minority proportion, larger per- capita school spending, teacher salary, smaller average student-to-teacher ratios, or greater income, generally did not experience an initial court order earlier or later than other districts (columns 1-6); however, these characteristics are significant predictors of the delay between the initial court order and major desegregation plan implementation (columns 7-8).
Aside from differences in population concentration, only the proportion of the population with 12 or more years of education significantly predict coming under court order later; while the proportion of the population that is school-age is predictive of coming under court order sooner.

Because parental education, neighborhood SES characteristics, and region of birth will be included in regression specifications, this correlation need not be a threat to the internal validity of the analysis.
Interestingly, holding spending levels constant, districts that received a greater proportion of 1962 school spending from state and federal sources were more likely to have initial court orders sooner.

This pattern may be expected if intergovernmental grants result in the financial ramifications of desegregation to not be borne solely by local residents, which may lessen opposition to desegregation implementation.
Furthermore, I find that neither urbanicity, the proportion of the population in rural areas, nor the county mortality rate is generally predictive of the timing of initial court orders.

While these regression results show a few statistically significant impacts of district characteristics on the timing of the initial court order, the quantitative importance of these predictors is small and most of the variation remains unexplained.
I find little evidence that pre-treatment characteristics significantly predict the timing of court orders.iv On the other hand, I find that districts with a larger minority population, greater per-capita school spending, and smaller proportion of residents with low income are each strongly associated with longer delays in major desegregation implementation following the initial court order.
These results are consistent with the legal history of school desegregation, and suggest that the timing of initial court litigation is more plausibly exogenous than the timing of major desegregation plan implementation.
In sum, the idiosyncratic nature of court litigation timing documented in the legal history of school desegregation make a prima facie case for treating initial court orders as exogenous shocks, which influenced the timing of major desegregation plan implementation and generated changes in school quality from abrupt shifts in racial school segregation.

This case is bolstered by the empirical evidence that the bulk of 1962 district/county characteristics fail to predict the timing of initial court orders.
i An elaborate discussion of the legal history of the school desegregation court decisions and the strategy used by the NAACP is contained in NAACP (2004) and www.naacp.org/legal/history/index.htm.

ii While the data is available at the school district level, the maps are presented at the county level for convenience, so I use counties and school districts interchangeably here in reference to the maps.
iii School desegregation litigation cases have been initiated by school districts, plaintiffs, federal district court judges, parents of students in affected districts, and non-school governmental organizations.

iv I find similar results when I also define as “under court order” those districts that implemented desegregation plans in response to pressure from HEW in addition to school districts covered by formal court orders.
y where Appendix B1: Desegregation effects on school inputs using all districts ever under court order School- and district-level data used to analyze racial school segregation among students span the period 1968-1988 and include 815 districts; school district-level data used to analyze per-pupil spending span the period 1962-1992 and include 669 districts; and the school- and district-level data used to analyze class size and racial school segregation among teachers is available for the period 1968-1972 and include 759 districts and 33,952 schools.
The first analysis with district-level panel data exploits the plausibly exogenous timing of initial court orders to estimate the following event study equation (1): 6   y 1    g  dt  1 Tt   1 Tt   )  y 5  ( W   1960 X * d * d Y Z  dt         * y y , td  t t    1 d d y t   dt tdY , is per-pupil spending, student-to-teacher ratio, segregation dissimilarity index or black-white exposure index among students in school district d in year t = (1962,…,1992); g indexes region (defined by 9 census division categories); and the indicator function,  1 , is equal to one when the year of observation is y = (…,-5, -4, -3,…, 1, 2,…,6,…) years removed dT , when school district d was first issued the court order (y=0 is omitted).i The from the date, t ), and census division- d ), year fixed effects ( models include school district fixed effects ( * specific linear time trends ( g * ).
t School desegregation efforts occurred against the backdrop of the broader civil rights movement and overlapped the same period as federal “War on Poverty” initiatives were implemented.ii To control for possible coincident policies and the expansion of other programs, I include measures at the county-level for the timing of hospital desegregation, roll-out of "War on Poverty" policy initiatives ( dtZ )—community health centers, Head Start and Project Follow- Through—and real per capita transfer programs ( care, and retirement and disability programsiii (REIS)).
Also included are measures of 1960 county characteristics ( population size, percent voted for Strom Thurmond in 1948 Presidential election (proxy for segregationist preferences)) each interacted with linear time trends to control for differential time trends in district outcomes that might be correlated with the timing of initial court orders.
W d  poverty rate, percent black, education, percent urban, dtX : per capita cash income support, medical 1960 : t The point estimates of interest, y and y , are identified using variation in the timing of initial court orders.

Because the indicator for y = 0 is omitted, y is interpreted as the average difference in outcomes y years before the court order was issued, and in outcomes y years after the desegregation court order.
Estimates of y is the average difference y allow a visual and statistical evaluation of the potential importance of pre-treatment, time-varying school district- level, unobservables; estimates of y allow the post-treatment dynamics to be explored.

A key asset of this identification strategy is that estimates of y and y will be unbiased even if there are pre-existing and permanent differences between school districts.
The school district fixed effects control for time-invariant community characteristics such as preferences for racial integration and education.

With the inclusion of year fixed effects and census division- specific time trends, the estimates will provide unbiased estimates of the impact of court-ordered school desegregation even if regions varied in their K-12 education policies or their average levels of funding support from year to year.
Additionally, time-varying, community-level characteristics and measures of government transfers adjust the estimates for observed differences in characteristics and changes in federal programs.
The regression models are weighted by 1968 district student enrollment to yield estimates that are representative of the impacts for the average child.iv I make sure the results are robust to the use of a balanced panel to avoid confusing the time path of how communities respond to desegregation with changes in the composition of school districts in the analytic sample.

The standard errors are clustered at the school district level to account for serial correlation (Bertrand et al., 2004).
Finally, I use school-level data to estimate event-study models that examine impacts of court-ordered desegregation on average class size, separately by race.

These regression models include school-level fixed effects, year fixed effects, and are weighted by the school's pre- treatment race-specific student enrollment, to yield estimates that are representative of the impacts for the average black child and white child, respectively; standard errors are once again clustered at the school district level.
The Effectiveness of School Desegregation.

I build on the findings of Welch and Light (1987), Guryan (2004), Reber (2005), and Weiner et al.

(2008) by first analyzing the effectiveness of desegregation court-orders in reducing the extent of racial school segregation (but using a larger sample of 815 districts, instead of the 125 that prior studies had).
I then extend these findings to show that in the years immediately following court orders, desegregation had notable impacts on two key school quality resource indicators among blacks—1) increases in per-pupil spending and 2) reductions in the student-to-teacher ratio.

The average level of per- pupil school spending in 1967 among districts that had not yet implemented a plan was $2,738 (in 2000 dollars).

These results are presented in Figures B1a-B4.


The figures plot the regression coefficients on indicator variables for years before and after desegregation orders are enacted (year before initial court-order is the reference category) on school district racial segregation among both students and teachers, per-pupil spending, and the student-to-teacher ratio, respectively.

The changes are all statistically significant.


The similarity of the results among all districts ever under court order and the subset of those districts that overlap the PSID affirm the representativeness and generalizability of the findings reported from the PSID.
I also estimate identical models of the level of school district per-pupil spending from state revenue sources on the timing of court-ordered desegregation (with the inclusion of school district fixed effects and region-specific year effects), separately for school districts with a small proportion of black students (<0.2) versus districts with a large proportion of black students (>0.4).
Among the set of school districts that underwent court-ordered school desegregation at some time between 1954 and 1980, the 25th and 75th percentile of the school district proportion of students who were black was 0.2 and 0.4, respectively, in 1970.
As shown in Figure B3c, I find precisely this pattern: no significant changes in per-pupil school spending among districts that had a small proportion of black students; in contrast, we see substantial and statistically significant increases in per-pupil spending from state revenue sources among districts that had a large proportion of black students.

These results complement the findings of Reber (2010) for Lousiana, and Cascio et al.

(2010), and employ larger samples and geographic coverage.
i The models estimated upon which Figures B1a-B4 are based also include dummy indicators for each of the corresponding years in excess of 6 before and after court-ordered desegregation, respectively; these are not displayed in the figures because of the lack of precision due to limited observations that far away from the year of initial court order.
ii For example, this period included the desegregation of hospitals (and workplaces), and the introduction of Medicaid, Medicare, Head Start, and the Supplemental Nutrition Program for Women, Infants and Children (WIC).

Further, AFDC, Social Security, and disability income programs expanded.

iii I am grateful to Doug Almond, Hilary Hoynes, and Diane Schanzenbach for sharing the Regional Economic Information System (REIS) data for the 1959 to 1978 period.
iv If I instead treat individual school districts as the observational unit and estimate unweighted regressions, then the estimates will represent the impact experienced for the average school district.

While this parameter is intriguing, I am most interested in documenting the impacts of school desegregation for the average black student.

ONLINE APPENDIX B1: Desegregation effects on school inputs using all districts ever under court order FIGURE B1a.

FIGURE B1b.
The Effect of Court-Ordered Desegregation on School Segregation Among Students The Effect of Court-Ordered Desegregation on School Segregation Among Students - k c a B l .1 .05 0 -.05 -.1 -.15 -.2 -.25 -.3 -5 -4 -3 -2 x e d n I n i e g n a h C e r u s o p x E e t i h W - k c a B l .2 .15 .1 .05 0 -.05 -1 1 3 Years Since Court Order 0 2 4 5 6 7 -5 -4 -3 -2 -1 1 3 Years Since Court Order 2 0 4 5 6 7 95% CI Dissimilarity Index 95% CI Exposure Index Data: Office of Civil Rights (OCR) School-level & School district-level Data, 1968-1988; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all school districts from OCR data that were ever subject to court-ordered desegregation (N=815 school districts; 7,527 school district-year observations).
Models: Results are based on event-study models that include school district fixed effects, year fixed effects, census division-specific linear time trends, and controls at the county-level for the timing of hospital desegregation, roll-out of "War on Poverty" policy initiatives--community health centers, Head Start and Project Follow-Through--and controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election (proxy for segregationist preferences)) each interacted with linear time trends.
Models are weighted by 1968 district student enrollment, so that estimates are representative of the impacts for the average child; standard errors are clustered at the school district level.

ONLINE APPENDIX B1: Desegregation effects on school inputs using all districts ever under court order FIGURE B2a.

FIGURE B2b.
The Effect of Court-Ordered Desegregation on School Segregation Among Teachers The Effect of Court-Ordered Desegregation on School Segregation Among Teachers - k c a B l .1 0 -.1 -.2 -.3 -.4 .4 .3 .2 .1 0 n i e g n a h C x e d n I e r u s o p x E e t i h W - k c a B l -3 -2 -1 1 0 Years Since Court Order 2 3 -5 -4 -3 1 -2 Years Since Court Order -1 0 2 3 4 95% CI Dissimilarity Index 95% CI Exposure Index Data: Office of Civil Rights (OCR) School-level & School district-level Data, 1968-1972; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all school districts from OCR data that were ever subject to court-ordered desegregation (N=759 school districts; 3,324 school district-year observations).

Models: Results are based on event-study models that include school district fixed effects, year fixed effects, and controls at the county-level for the timing of hospital desegregation, roll- out of "War on Poverty" policy initiatives--community health centers, Head Start and Project Follow-Through.
Models are weighted by 1968 district black student enrollment, so that estimates are representative of the impacts for the average black child; standard errors are clustered at the school district level.
ONLINE APPENDIX B1: Desegregation effects on school inputs FIGURE B3a Effect of Court-Ordered School Desegregation on Avg School-Age Per-Pupil Spending e g a - - r e P 2500 2000 1500 1000 500 0 -500 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 8 6 4 2 14 16 90% CI Blacks Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state- funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.

ONLINE APPENDIX B1: Desegregation effects on school inputs using all districts ever under court order FIGURE B3b.

FIGURE B3c.
The Effect of Court-Ordered Desegregation on Per-Pupil School Spending The Effect of Court-Ordered Desegregation on Per-Pupil School Spending, By Revenue Source n i e g n a h C i g n d n e p S l i p u P - r e P ) $ 0 0 0 2 l a e r n i ( 1200 1000 800 600 400 200 0 -200 -2 -1 0 1 2 Years Since Court Order n i e g n a h C i g n d n e p S l i p u P - r e P ) $ 0 0 0 2 l a e r n i ( 1200 1000 800 600 400 200 0 -200 3 4 5 -2 -1 0 95% CI Per-Pupil Spending Years Since Court Order State Federal Local Data: Census of Governments (COG) School District Finance Data, 1962-1992; court- ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all school districts from COG data that were ever subject to court-ordered desegregation (N=669 school districts; 13,933 school district-year observations).

FIGURE B3d.
The Effect of Court-Ordered Desegregation on Per-Pupil Spending From State Revenue Source: By Proportion of District that is Black Models: Results are based on event-study models that include school district fixed effects, year fixed effects, census division-specific linear time trends, and controls at the county- level for the timing of hospital desegregation, roll-out of "War on Poverty" policy initiatives--community health centers, Head Start and Project Follow-Through--and controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election (proxy for segregationist preferences)) each interacted with linear time trends.
Models are weighted by 1968 district student enrollment, so that estimates are representative of the impacts for the average child; standard errors are clustered at the school district level.

n i e g n a h C i g n d n e p S l i p u P - r e P 1200 1000 ) $ 0 0 0 2 l a e r n i ( 800 600 400 200 0 -200 -2 -1 0 1 2 Years Since Court Order 3 4 5 Large %Black (>.4) Small %Black (<.2) ONLINE APPENDIX B1: Desegregation effects on school inputs using all districts ever under court order FIGURE B4.
The Effect of Court-Ordered Desegregation on Avg Class Size, By Race 1 n i e g n a h C i e z S s s a C l 0 -1 -2 -3 -4 -5 -3 -2 -1 0 1 Years Since Court Order 2 3 4 90% CI Event-Study Estimates Blacks Whites Data: Office of Civil Rights (OCR) School-level Data, 1968-1972; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).

Analysis sample includes all schools from OCR data that were ever subject to court-ordered desegregation (N= 33,952 schools).
Models: Results are based on non-parametric event-study models that include school fixed effects and year fixed effects.

Models are weighted by 1968 school's race-specific student enrollment, so that estimates are representative of the impacts for the average black child and white child, respectively; standard errors are clustered at the school district level.
Also shown are results of representative impacts for black children that use a parametric event- study model specification with pre-treatment linear time trend (with confidence interval), which include school FE and year FE.

ONLINE APPENDIX B FIGURE B5.

Birth Cohort Variation in Childhood Exposure to Court-Ordered School Desegregation 1 .9 .8 .7 .6 .5 .4 .3 .2 .1 0 1950 1955 1960 Year of birth 1965 1970 1975 PSID individuals born 1947-1975, followed up to 2007.
95% CI Black Children f o n o i t r o p o r P s r a e y d o o h d l i h C e g a - l o o h c S ONLINE APPENDIX B Figure B6.
Time Lag Between Initial Court Order & Implementation of Major Desegregation Plan: Structural Break Pre- & Post-1965 20 15 10 5 0 1955 1960 1965 1970 Year 1975 1980 1985 90% CI-U Predicted 90% CI-L n e e w t e b s r a e Y f o # n o i t a t n e m e p m l I l n a P & r e d r O t r u o C l a i t i n I Appendix Table B1: Determinants of the Timing of Court-Ordered School Desegregation Using 1962 County Characteristics Dependent variable: Initial Year of Court Order Delay b/w Initial Court Order & Major Desegregation Plan Implementation (years) ONLINE APPENDIX B 1962 County variables: Log population Percent minority, spline (< 20) Percent minority, spline (≥ 20) Per-capita school spending ($000s) % of school spending revenue from state/fed govt (1) -0.8040*** (0.2768) 0.0877* (0.0449) -0.0159 (0.0253) 0.0082 (0.0162) -0.0899*** (0.0186) Student-to-teacher ratio Average teacher salary Median income % of households with income <$3,000 % of households with income > $10,000 % of adults with 12 or more years of education 1950-60 population change % of residents in urban areas % of residents in rural or farm area % living in group quarters Median age % of residents who are school-age (5-20) % of residents who are elderly (65+) % who voted for incumbent President Mortality rate (annual deaths per 10,000 residents) (2) -0.8541*** (0.2847) 0.0858* (0.0450) -0.0182 (0.0252) -0.0940*** (0.0191) -0.0039 (0.0311) 0.0005 (0.0006) -0.0002 (0.0014) 0.0761 (0.0996) 0.1065 (0.1380) 0.0903** (0.0396) 0.0051 (0.0088) 0.0058 (0.0137) 0.0361 (0.0256) 0.0568 (0.0586) -0.4281** (0.1747) -0.2933 (0.1911) 0.2209 (0.2046) 0.0508 (0.0468) -0.6125 (1.8842) yes yes no no 616 (3) -0.1439 (0.8200) -0.1660 (0.1486) -0.0322 (0.1125) 0.5960 (1.3015) -0.1298** (0.0655) -0.0034 (0.0043) 0.1065 (0.3589) -0.0208 (0.3786) 0.2574** (0.1070) -0.0232 (0.0177) -0.0437 (0.0595) 0.1822 (0.1279) 0.1397 (0.2185) -1.3912*** (0.5256) -2.2507*** (0.6443) 0.1049 (0.6581) 0.2834** (0.1237) -16.0529* (9.0305) yes no yes no 161 (4) 0.4198 (0.8907) -0.1629 (0.1489) 0.0026
 (0.1136) -0.1043 (0.0666) -0.2896 (0.1787) -0.0020 (0.0015) -0.0033 (0.0044) 0.1170 (0.3594) 0.0416 (0.3807) 0.1992* (0.1116) -0.0191 (0.0175) -0.0402 (0.0591) 0.1970 (0.1281) 0.1957 (0.2196) -1.4594*** (0.5283) -2.4145*** (0.6489) -0.0283 (0.6616) 0.3241** (0.1252) -13.7160 (9.0891) yes no yes no 161 (5) -1.3639 (1.0195) -0.1791 (0.2081) -0.1762 (0.2520) -2.3282 (2.1433) -0.0833 (0.0879) 0.0086 (0.0067) 0.8007 (0.6187) -0.0672 (0.7080) -0.2369 (0.1660) -0.0016 (0.0216) 0.0339 (0.1150) 0.2554 (0.4184) 0.3980 (0.2847) -0.4847 (1.0443) -0.9571 (1.1669) 0.7359 (0.8173) 0.0059 (0.1801) -14.4197 (14.2740) yes no yes yes 62 (6) -1.9489* (1.0794) -0.0635 (0.2123) -0.1913 (0.2547) -0.0805 (0.0877) 0.1965 (0.1867) 0.0021 (0.0019) 0.0062 (0.0069) 0.4575 (0.6321) -0.0378 (0.7071) -0.1699 (0.1732) -0.0041 (0.0215) 0.0282 (0.1145) 0.3849 (0.4209) 0.3673 (0.2860) -0.2984 (1.0532) -0.5218 (1.2006) 0.6766 (0.8171) -0.0241 (0.1830) -11.1113 (14.1562) yes no yes yes 62 (7) 1.1884 (0.9768) 0.2001 (0.1943) 0.5389** (0.2359) 5.4804** (2.2330) 0.0684 (0.0825) -0.0207*** (0.0065) -2.5174*** (0.5757) 0.8514+ (0.6280) -0.0071 (0.1606) -0.0184 (0.0220) -0.0199 (0.1147) 0.5533 (0.4473) -0.1526 (0.2866) -0.3123 (1.0220) 0.1894 (1.1408) 0.0935 (0.8227) 0.0204 (0.1636) 5.1065 (14.5443) yes no yes yes 62 (8) 1.3207 (1.1221) 0.1527 (0.2085) 0.5381** (0.2568) 0.0758 (0.0877) -0.3806 (0.2894) 0.0014 (0.0019) -0.0210*** (0.0070) -2.4205*** (0.6244) 0.9291 (0.6656) 0.0009 (0.1788) -0.0159 (0.0232) -0.0150 (0.1214) 0.4997 (0.4840) -0.2322 (0.3074) -0.1917 (1.0951) 0.1512 (1.2355) 0.0097 (0.8788) 0.0579 (0.1818) 2.7650 (15.3410) yes no yes yes 62 -0.0002 (0.0015) 0.0713 (0.1005) 0.1178 (0.1377) 0.0877** (0.0393) 0.0050 (0.0088) 0.0060 (0.0137) 0.0352 (0.0248) 0.0617 (0.0534) -0.4279** (0.1754) -0.2907 (0.1894) 0.2258 (0.2039) 0.0615 (0.0444) -0.6088 (1.8752) yes yes no no 616 Region controls?
Full sample?

Subsample that overlaps PSID original sample kids?

Subsample with desegregation implementation dates?

Observations Standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.10 Data: 1962 Census of Governments, City & County Data Book; Desegregation court case data compiled by legal scholars for American Communities Project/Brown University; Major desegregation plan implementation dates obtained from Welch/Light data.
Appendix C: PSID Data, Measures, & Supplementary Regression Results PSID sample Studies have concluded that the PSID sample of heads and wives remains representative of the national sample of adults (Fitzgerald, Gottschalk, and Moffitt, 1998a; Becketti et al, 1988), and that the sample of “split offs” is representative (Fitzgerald, Gottschalk and Moffitt, 1998b).

The 95-98% wave-to- wave response rate of the PSID makes this possible.
Appendix Table C0 reports descriptive statistics for the sample used in the models of adult outcomes, separately by race.

The substantial race differences in childhood family characteristics are highlighted in this table.
Multinomial Models of Education Attainment In addition to the main education models reported, I also estimate multinomial logit models of educational attainment, where the four categories are: High School Dropout/GED (reference category (0)); (1) High School Graduate, no college; (2) Attend College, no 4-year degree; and (3) 4-year College Graduate or more.
I find that the effects of school desegregation for blacks were not limited to those on the margin of dropping out of high school, but also had significant effects that led to increased college attendance and completion rates.
The results demonstrate that there is a significant difference in both high school dropout rates and college attendance and completion rates among blacks between cohorts that were born less than 7 years apart but differed in whether and how long they attended integrated schools; with no significant effects for whites across any of the educational attainment categories.
Incarceration Measures Spells of incarceration are recovered from information on PSID respondents’ collected in each survey (1968-2013) that includes whether a respondent was incarcerated at the time of the interview.

The 1995 wave added a supplemental crime history module to the PSID including several key questions that I use to augment and obtain more precise information about the timing and duration of incarceration and minimize measurement error.

The annual data alone on incarceration has limitations.
Among the most important is that this will only identify incarceration in a given year if it were on-going at the time of the survey interview.

As a result, we are likely to miss individuals serving shorter sentences that did not coincide with the time of the interview.
The supplemental crime history module that was added to the 1995 wave of the PSID aims information on whether respondents had ever been to address suspended/expelled from school; ever been booked or charged with a crime; whether ever placed in a juvenile correctional facility; whether ever served time in jail or prison, the number of times and the month and year of release.
This information is used together to analyze the annual incidence of incarceration and whether ever incarcerated by age 30. limitation and includes this Health Index A number of previous studies using surveys have demonstrated that a change in GHS from fair to poor represents a much larger degree of health deterioration than a change from excellent to very good or very good to good (e.g., Van Doorslaer and Jones, 2003; Humphries and Van Doorslaer, 2000).
More generally, this research has shown that health differences between GHS categories are larger at lower levels of GHS.

Thus, assuming a linear scaling would not be appropriate.

To analyze health disparities in the presence of a multiple-category health indicator, three alternative approaches have been used, each with its own set of advantages and disadvantages.
The most common and simplest approach is to dichotomize GHS by setting a cut-off point above which individuals are said to be in good health (e.g., excellent/very good/good vs. fair/poor).

The disadvantage of this approach is that it does not utilize all of the information on health.

Additionally, it uses a somewhat arbitrary cut-off for the determination of healthy/not-healthy, and the measurement of inequality over time can be sensitive to the choice of cut-off (Wagstaff and Van Doorslaer, 1994).
A second approach is to estimate an ordered logit or ordered probit regression using the GHS categories as the dependent variable, and rescale the predicted underlying latent variable of this model to compute “quality weights” for health between 0 and 1 (Cutler and Richardson, 1997; Groot, 2000).
The key shortcoming of this approach is the probit and logit link functions are inadequate to model health due to the significant degree of skewness in the health distribution (i.e., the majority of a general population sample report themselves to be in good to excellent health).
Van Doorslaer and Jones (2003) assess the validity of using ordered probit regressions to impose cardinality on the ordinal responses comparing it with a gold standard of using the McMaster ‘Health Utility Index Mark III’ (HUI).1 They conclude “…the ordered probit regression does not allow for any sensible approximation of the true degree of inequality.” The third approach, adopted first by Wagstaff and Van Doorslaer (1994), assumes that underlying the categorical empirical distribution of the responses to the GHS question is a latent, continuous but unobservable health variable with a standard lognormal distribution.
This assumption allows “scoring” of the GHS categories using the mid-points of the intervals corresponding to the standard lognormal distribution.

The lognormal distribution allows for skewness in the underlying distribution of health.
The health inequality results obtained using this scaling procedure have been shown to be comparable to those obtained using truly continuous generic measures like the SF36 (Gerdtham et al., 1999) or the Health Utility Index Mark III (Humphries and van Doorslaer, 2000) in Canada, but has not been validated as an appropriate scaling procedure using U.S. data.
The disadvantage of this approach is it inappropriately uses OLS on what remains essentially a categorical variable and does not exploit the within-category variation in health.

This is particularly problematic for the analysis of health dynamics over a relatively short time horizon.
Ignoring within-category variation in health will cause health deterioration estimates to be biased and induce (health) state dependence because within-category variation increases when going down from excellent to poor health.

Several surveys have been undertaken that contain both the GHS question and questions underlying a health utility index.

In this paper, we adopt a latent variable approach that combines the advantages of approaches two and three above, but avoids their respective pitfalls.
Specifically, utilizing external U.S. data that contain both GHS and health utility index measures, we use the distribution of health utility-based scores across the GHS categories to scale the categorical responses and subject our indicators to the transformation that best predicts quality of life.

This scaling thus translates our measures into the metric that reflects the underlying level of health.
Specifically, using a 100-point scale where 100 equals perfect health and zero is equivalent to death, the interval health values associated with GHS are: [95, 100] for excellent, [85, 95) for very good, [70,85) for good, [30,70) for fair, and [1,30) for poor health.

Interval Regression Model.

The method assumes that underlying the categorical empirical distribution of the responses to the GHS question is a latent, continuous health variable.
I estimate interval regression models using the aforementioned values to scale the thresholds for GHS, where interval regression models are equivalent to probit models with known thresholds.

The measure of health status has categorical outcomes excellent (E), very good (VG), good (G), fair (F), and poor (P).
The model can be expressed as Hi = 1 (E) if 95 ≤ Hi 2 (VG) if 85 ≤ Hi 3 (G) if 70 ≤ Hi 4 (F) if 30 ≤ Hi 5 (P) if 1 ≤ Hi * ≤ 100 = perfect health * < 95 * < 85 * < 70 * < 30 , 1 The McMaster Health Utility Index can be considered a more objective health measure because the respondents are only asked to classify themselves into eight health dimensions: vision, hearing, speech, ambulation, dexterity, emotion, cognition, and pain.
The Health Utility Index Mark III is capable of describing 972,000 unique health states (Humphries and van Doorslaer, 2000).

where H* is the continuous latent health variable and is assumed to be a function of socio-economic variables x: Hi * = xiβ + vi , vi ~ N(0, 2 v ).
Given the assumption that the error term is normally distributed, the probability of observing a particular value of y is             ix ix   –   , L U   v Pij = P(Hi = j) =   v   is the standard normal distribution function, and μ represent the where j indexes the categories, threshold values previously discussed.

Because the threshold values are known, it is possible to identify v .
Because I use the health utility-based values to score the thresholds for the variance of the error term GHS, the linear index for the interval regression model is measured on the same scale.

This scaling thus translates the measures into the metric that reflects the underlying level of health.

With independent observations, the log-likelihood for the interval regression model takes the form: 2 log L =  i j H log ij P ij , where the Hij are binary variables that are equal to 1 if Hij = j.
This can be maximized to give estimates of β. ONLINE APPENDIX C: PSID data Appendix Table C0.
Descriptive Statistics by Race Blacks (N=4,473) Whites (N=3,993) Adult Outcomes: High School Graduate Years of Education Ln(Wages), at age 30 Annual Work Hours, at age 30 Adult Family Income, at age 30 In Poverty, at age 30 Occupational Prestige Index Ever Incarcerated, by age 30 Annual Incidence of Incarceration, at age 25 Adult Health Status Index, at age 30 Age (range: 20-50) Year born (range: 1945-1968) Female Childhood school variables: Per-pupil spending (avg, ages 5-17) Black-White Dissimilarity Index (avg, ages 5-17) Any court-ordered desegregation, age 5-17 # of exposure yrs to desegregation, age 5-17 1960 District Percent Black 1960 District Poverty Rate (%) Childhood family variables: Income-to-needs ratio (avg, ages 12-17): In poverty (%) Mother's years of education Father's years of education Born into two-parent family 0.79 12.60 2.26 1540.06 $31,020 0.24 34.42 0.08 0.0063 84.16 32.7 1958 0.45 $3,508 0.58 0.68 5.58 26.18 28.29 1.54 0.41 10.15 9.21 0.40 0.86 13.51 2.63 1895.99 $52,937 0.05 48.57 0.04 0.0014 88.78 34.3 1957 0.43 $3,865 0.49 0.57 4.22 12.13 18.32 3.48 0.07 11.81 11.74 0.70 Childhood neighborhood variables: Neighborhood poverty rate Residential segregation dissimilarity indexcounty Note: All descriptive statistics are sample weighted to produce nationally-representative estimates of means.
Dollars are CPI-U deflated in real 2000 $.
0.20 0.72 0.07 0.71 ONLINE APPENDIX C: Additional Analysis from Section V FIGURE C1a Effect of Court-Ordered School Desegregation on Educational Attainment, Blacks -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Blacks FIGURE C1b Effect of Court-Ordered School Desegregation on Educational Attainment, Whites n i e g n a h C n o i t a c u d E f o s r a e Y 2 1.5 1 .5 0 -.5 -1 n i e g n a h C n o i t a c u d E f o s r a e Y 2 1.5 1 .5 0 -.5 -1 -1.5 -2 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

(N=8,548 individuals from 3,562 childhood families, 631 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.
ONLINE APPENDIX C: Additional Analysis from Section V FIGURE C2a Effect of Court-Ordered School Desegregation on Likelihood of Graduating from High School, Blacks n i e g n a h C ) d a r G l o o h c S h g H ( b o r P i .4 .3 .2 .1 0 -.1 -.2 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Blacks FIGURE C2b Effect of Court-Ordered School Desegregation on Likelihood of Graduating from High School, Whites .4 .3 .2 .1 0 -.1 -.2 -.3 -8 -6 -4 -2 12 Year Aged 17 - Year of Initial Court Order 10 8 6 0 2 4 14 16 n i e g n a h C ) d a r G l o o h c S h g H ( b o r P i 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

(N=8,548 individuals from 3,562 childhood families, 631 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Standard errors are clustered at the school district level.
FIGURE C3a FIGURE C3b Effect of Court-Ordered School Desegregation on Adult Wages, Blacks Effect of Court-Ordered School Desegregation on Adult Wages, Whites ONLINE APPENDIX C: Additional Analysis from Section V n i e g n a h C 0 5 - 0 2 s e g a , ) s e g a W ( n L .75 .5 .25 0 -.25 -.5 -10 -8 -6 n i e g n a h C 0 5 - 0 2 s e g a , ) s e g a W ( n L .75 .5 .25 0 -.25 -.5 12 14 16 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 8 0 4 2 6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 0 8 4 2 6 12 14 16 90% CI Blacks 90% CI Whites FIGURE C4a FIGURE C4b Effect of Court-Ordered School Desegregation on Adult Earnings, Blacks Effect of Court-Ordered School Desegregation on Adult Earnings, Whites 1.25 1 .75 .5 .25 0 -.25 -.5 n i e g n a h C , ) s g n n r a E i l a u n n a ( n L 0 5 - 0 2 s e g a -10 -8 -6 -4 Year Aged 17 - Year of Initial Court Order 10 -2 8 4 6 2 0 12 1.25 1 .75 .5 .25 0 -.25 -.5 0 5 - 0 2 s e g a , ) s g n n r a E i l a u n n a ( n L n i e g n a h C 14 16 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 8 6 0 2 4 12 14 16 90% CI Blacks 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year positive earnings observations (ages 20-50) are included except those in which individual was in school (N=97,568 person-year wage observations, 8,597 individuals from 3,584 childhood families, 636 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.
FIGURE C5a FIGURE C5b Effect of Court-Ordered School Desegregation on Adult Family Income, Blacks Effect of Court-Ordered School Desegregation on Adult Family Income, Whites ONLINE APPENDIX C: Additional Analysis from Section V n i e g n a h C , ) e m o c n l i I y m a F l a u n n a ( n L 0 5 - 0 2 s e g a 1.5 1.25 1 .75 .5 .25 0 -.25 -.5 -10 -8 -6 n i e g n a h C 1.5 1.25 1 .75 .5 .25 0 -.25 -.5 0 5 - 0 2 s e g a , ) e m o c n l i I y m a F l a u n n a ( n L -4 Year Aged 17 - Year of Initial Court Order 10 -2 6 8 2 4 0 12 14 16 -10 -8 -6 -2 -4 Year Aged 17 - Year of Initial Court Order 10 6 2 4 0 8 12 14 16 90% CI Blacks 90% CI Whites FIGURE C6a FIGURE C6b Effect of Court-Ordered School Desegregation on Annual Incidence of Poverty in Adulthood, Blacks Effect of Court-Ordered School Desegregation on Annual Incidence of Poverty in Adulthood, Whites n i e g n a h C 0 5 - 0 2 s e g a , ) y t r e v o P ( b o r P .1 0 -.1 -.2 -.3 -.4 -10 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order n i e g n a h C 0 5 - 0 2 s e g a , ) y t r e v o P ( b o r P .1 0 -.1 -.2 -.3 -.4 -10 -8 -6 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order 90% CI Blacks 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year observations (ages 20-50) are included except those in which individual was in school (N=142,499 person-year family income observations, 9,156 individuals from 3,702 childhood families, 645 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.
FIGURE C7a FIGURE C7b Effect of Court-Ordered School Desegregation on Annual Incidence of Adult Incarceration, Blacks Effect of Court-Ordered School Desegregation on Annual Incidence of Adult Incarceration, Whites ONLINE APPENDIX C: Additional Analysis from Section V n i e g n a h C 0 3 - 8 1 s e g a , ) d e t a r e c r a c n I ( b o r P .04 .02 0 -.02 -.04 -.06 14 16 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 6 8 2 4 14 16 -6 -4 -2 0 12 Year Aged 17 - Year of Initial Court Order 10 2 6 4 8 90% CI Blacks 90% CI Whites FIGURE C8a FIGURE C8b Effect of Court-Ordered School Desegregation on the Likelihood of Ever Being Incarcerated, Blacks Effect of Court-Ordered School Desegregation on the Likelihood of Ever Being Incarcerated, Whites n i e g n a h C ) d o o h t l u d A n i d e t a r e c r a c n I r e v E ( b o r P .2 .1 0 -.1 -.2 -.3 -.4 16 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order -4 -2 0 2 4 6 8 10 12 14 Year Aged 17 - Year of Initial Court Order n i e g n a h C 0 3 - 8 1 s e g a , ) d e t a r e c r a c n I ( b o r P n i e g n a h C ) d o o h t l u d A n i d e t a r e c r a c n I r e v E ( b o r P .04 .02 0 -.02 -.04 -.06 .2 .1 0 -.1 -.2 -.3 -.4 90% CI Blacks 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, first observed before age 21 and followed until at least age 25, who grew up in school districts that were ever subject to court-ordered desegregation.

Incarceration info based on reason for non-response for each survey 1968-2013 &, where available, 1995 svy reports of whether/when ever incarcerated.

Models of annual incidence of adult incarceration include all person-year observations (ages 18-30).
(N=96,584 person-year observations, 8,539 individuals from 3,411 childhood families, 524 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age FE, svy year FE.
Standard errors are clustered at the school district level.

ONLINE APPENDIX C: Additional Analysis from Section V FIGURE C9.
The Effect of Court-Ordered Desegregation on Adult Work Hours, By Race n i e g n a h C s r u o h k r o w l a u n n A 450 350 250 150 50 -50 -150 -4 -2 0 2 4 6 8 10 12 14 Year Aged 17 - Year of Initial Court Order 90% CI Whites Blacks Event-Study Estimates Data: PSID geocode Data (1968-2013), matched with childhood school and neighborhood characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year observations (ages 20-50) are included except those in which individual was in school or pregnant/yrs immediately following childbirth.

(N=85,497 person-year work hours' observations, 8,396 individuals from 3,557 childhood families, 633 school districts).
Models: Results are based on event-study models--both non-parametric and parametric (w/CI) estimates- -that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.

Results for whites not statistically significant from 0.
FIGURE C10a FIGURE C10b ONLINE APPENDIX C: Additional Analysis from Section V Effect of Court-Ordered School Desegregation on Annual Incidence of Moderate/Problematic Health in Adulthood, Blacks .3 .2 .1 0 -.1 -.2 -.3 -.4 -.5 -6 -4 , ) h t l a e H d o o G y r e V / t n e l l e c x E n 0 5 - 0 2 s e g a n i e g n a h C i t o N ( b o r P n i e g n a h C 0 5 - 5 3 s e g a , x e d n I s u t a S h t t l a e H 25 20 15 10 5 0 -5 -10 , ) h t l a e H d o o G y r e V / t n e l l e c x E n n i e g n a h C 0 5 - 0 2 s e g a Effect of Court-Ordered School Desegregation on Annual Incidence of Moderate/Problematic Health in Adulthood, Whites .3 .2 .1 0 -.1 -.2 -.3 -.4 -.5 -6 -4 -2 12 Year Aged 17 - Year of Initial Court Order 10 0 2 6 4 8 14 16 -2 12 Year Aged 17 - Year of Initial Court Order 10 4 6 8 0 2 i t o N ( b o r P 14 16 90% CI Blacks 90% CI Whites FIGURE C11a FIGURE C11b Effect of Court-Ordered School Desegregation on Adult Health Status, Blacks Effect of Court-Ordered School Desegregation on Adult Health Status, Whites 25 20 15 10 5 0 -5 -10 n i e g n a h C 0 5 - 5 3 s e g a , x e d n I s u t a S h t t l a e H 12 14 16 -4 -2 0 2 4 6 8 10 12 14 16 Year Aged 17 - Year of Initial Court Order -4 -2 0 2 4 6 8 10 Year Aged 17 - Year of Initial Court Order 90% CI Blacks 90% CI Whites Data: PSID geocode Data (1968-2013), matched with childhood school characteristics; court-ordered desegregation case litigation data (1954-2000; Brown Univ/American Communities Project).
Analysis sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.

All person-year self-assessed health status observations (ages 20-50) are included except those in which individual was pregnant/yrs immediately following childbirth (Figure C10a-C10b: N=75,729 person-year health status observations, 7,527 individuals from 3,330 childhood families, 613 school districts).
Health Status index (1-100(perfect health)) based on self-assessed health (E/VG/G/F/P), 1985-2013; interval regression model estimated, where E=[95,100]; VG=[85,95); G=[70,85); F=[30,70); P=[1,30).

(Figure C11a-C11b: N=42,011 person-year observations at ages 35-50 for 5,598 individuals from 2,797 childhood families, 570 school districts).
Models: Results are based on non-parametric event-study models that include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight); and controls for gender, age (cubic), svy year FE.
Standard errors are clustered at the school district level.
FIGURE D1a FIGURE D1b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Educational Attainment, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Educational Attainment, Whites ONLINE APPENDIX D: Check Robustness to Residential Mobility n i e g n a h C n o i t a c u d E f o s r a e Y 1 .5 0 -.5 -4 -2 n i e g n a h C n o i t a c u d E f o s r a e Y 1 .5 0 -.5 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 6 2 8 10 12 0 4 Year Aged 17 - Year of Initial Court Order 2 8 6 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order FIGURE D2a FIGURE D2b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Likelihood of Graduating from High School, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Likelihood of Graduating from High School, Whites n i e g n a h C ) d a r G l o o h c S h g H ( b o r P i .25 .2 .15 .1 .05 0 -.05 -.1 -4 -2 .25 .2 .15 .1 .05 0 -.05 -.1 n i e g n a h C ) d a r G l o o h c S h g H ( b o r P i 0 4 Year Aged 17 - Year of Initial Court Order 2 6 8 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 2 8 6 10 12 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order FIGURE D3a FIGURE D3b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Adult Earnings, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Adult Earnings, Whites ONLINE APPENDIX D: Check Robustness to Residential Mobility n i e g n a h C 0 5 - 0 2 s e g a , ) s g n n r a E i l a u n n a ( n L .6 .5 .4 .3 .2 .1 0 -.1 -.2 n i e g n a h C 0 5 - 0 2 s e g a , ) e m o c n I y m a F l i l a u n n a ( n L .5 .4 .3 .2 .1 0 -.1 -.2 .6 .5 .4 .3 .2 .1 0 -.1 -.2 0 5 - 0 2 s e g a , ) s g n n r a E i l a u n n a ( n L n i e g n a h C 10 12 -4 -2 0 4 Year Aged 17 - Year of
 Initial Court Order 2 6 8 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 6 8 2 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order FIGURE D4a FIGURE D4b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Adult Family Income, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Adult Family Income, Whites n i e g n a h C 0 5 - 0 2 s e g a , ) e m o c n I y m a F l i l a u n n a ( n L .5 .4 .3 .2 .1 0 -.1 -.2 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 6 8 2 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 6 2 8 10 12 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order FIGURE D5a FIGURE D5b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Annual Incidence of Adult Poverty, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Annual Incidence of Adult Poverty, Whites ONLINE APPENDIX D: Check Robustness to Residential Mobility n i e g n a h C 0 5 - 0 2 s e g a , ) y t r e v o P ( b o r P 0 -.1 -.2 -.3 -4 -2 n i e g n a h C 0 5 - 0 2 s e g a , ) y t r e v o P ( b o r P 0 -.1 -.2 -.3 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 2 6 8 10 12 0 4 Year Aged 17 - Year of Initial Court Order 6 8 2 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order FIGURE D6a FIGURE D6b Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Likelihood of Ever Being Incarcerated, Blacks Address Endogenous Residential Mobility: Similar Estimated School Desegregation Effects on Likelihood of Ever Being Incarcerated, Whites ONLINE APPENDIX D: Check Robustness to Residential Mobility n i e g n a h C ) d o o h t l u d A n i d e t a r e c r a c n I r e v E ( b o r P .1 0 -.1 -.2 -.3 -4
 -2 0 4 Year Aged 17 - Year of Initial Court Order 2 6 8 n i e g n a h C ) d o o h t l u d A n i d e t a r e c r a c n I r e v E ( b o r P .1 0 -.1 -.2 -.3 10 12 -4 -2 0 4 Year Aged 17 - Year of Initial Court Order 2 6 8 10 12 All Blacks Only Blacks w/Address Prior to Court Order All Whites Only Whites w/Address Prior to Court Order Appendix Table E1.
Falsification Tests Using Unsuccessful Desegregation Court Litigation: Placebo Effects on Adult Outcomes, by Race Dependent variable: ONLINE APPENDIX E: Falsification/Placebo Tests Probability (High School Graduate) Years of Education Occupational Prestige Index Probability (Ever Incarcerated) Ln(Wage), ages 20-50 Ln(Family Income), ages 20-50 Probability (Poverty), ages 20-50 Adult Health Status Index, ages 20-50 0.0031 (0.0044) -0.0137 (0.0247) Years of Exposure to Unsuccessful Desegregation Court Litigation(age 5-17) Years of Exposure to Unsuccessful Desegregation Court Litigation*White Number of person-year adult observations Number of individuals Number of childhood families Number of school districts Number of childhood counties Robust standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 -0.0008 (0.0036) -- 6,921 2,816 613 437 0.0182 (0.0267) -- 6,921 2,816 613 437 -0.2906 (0.2561) 0.2951 (0.3261) -- 6,341 2,938 602 428 -0.0001 (0.0029) 0.0009 (0.0012) -- 6,341 2,938 602 428 -0.0076 (0.0056) 0.0061 (0.0076) 54,139 6,014 2,607 591 427 -0.0177 (0.0112) 0.0144 (0.0132) 72,191 6,570 2,723 613 437 0.0046 (0.0039) -0.0059 (0.0040) 72,191 6,570 2,723 613 437 0.0240 (0.1267) -0.0086 (0.1472) 54,139 6,014 2,607 591 427 Sample includes all PSID individuals born between 1945-1968, followed into adulthood through 2013, who grew up in school districts that had desegregation court litigation at some point b/w 1954-90 (desegregation court case data, American Communities Project).
All models include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Results in this table demonstrate that timing of UNSUCCESSFUL court litigation is unrelated to adult attainment outcomes; only the timing of initial year of successful litigation that led to court-ordered school desegregation is significantly associated with black's adult socioeconomic & health attainments (see Figures 5-14).
Appendix F: Exploring Potential Mechanisms r  1 r   3  t  idb  To attempt to identify the potential mechanisms, I isolate for every district the desegregation-induced change in per-pupil spending and racial school integration, respectively, independent of district-specific trends and other coincident policies.
For each district, I compute the change in school district per-pupil spending (school segregation) induced by the court order from the year preceding enactment to the first several years following it..

The district-specific changes in per-pupil spending and racial integration resultant from court-ordered desegregation are interpreted as markers for the intensity of treatment.
In order to further assess the relative roles of school resources and peer effects as potential mechanisms underlying the desegregation effects, I estimate parametric event study models of the form: (F1) Y   t  t    * 1 tDT t  d db idb idb    * 01 DT t   d idb  1 tDT       12 SPEND d SPEND SEG  * T d 12 SPEND * T d     SEG SEG  t  idb    r  0 * T d * T d 12 12 d                0 0 idb idb db db t   d * T d * d idb db d   1 tDT  db  01 t   1 tDT  db ( W *  d idb  * DT  d   * d Z  idb idb   idb r   2 r  4 X  idb * T  d d r ) b   g    r d r b  r d r  5 b * * d d d db idb 1960 dT is the year of the initial is the year the individual from school district d turned age 17; SPEND is the desegregation-induced change in per-pupil spending SEG is the desegregation-induced change in racial school segregation among idb where idbt court order in school district d; in district d; students in district d (as measured by the black-white exposure index); with the inclusion of the same set of controls as previously discussed in Section IV.i The terms used in the specification to capture the duration of desegregation exposure is simplified to improve precision in this expanded model (which is supported by the earlier desegregation results reported which were roughly linear in school-age exposure years to a first approximation).
This can be viewed as a triple-difference strategy that compares the difference in outcomes between treated and untreated cohorts within districts (variation in exposure) and across districts with larger or smaller changes in school spending due to desegregation (variation in intensity).
The event study framework allows one to inspect whether districts that underwent larger changes in school spending (segregation) resultant from desegregation exhibited differential trends in outcomes preceding the enactment of court orders, which I use as an additional specification test.

The results are presented in Table F1.

For blacks’ educational, economic and health attainments, the results suggest that changes in school quality resulting from integration played an important role.
The results indicate significant interactive effects of school desegregation exposure with the resultant change in access to school quality, as proxied by changes in per-pupil spending.

I find that court-ordered desegregation that led to larger improvements in school quality resulted in more beneficial educational, economic, and health outcomes in adulthood for blacks who grew up in those court-ordered desegregation districts.
These significant effects persist after the inclusion of corresponding increases in the black-white exposure index that accompanied desegregation.

Importantly, I find no evidence that districts that underwent larger changes in school spending resultant from desegregation exhibited differential trends in outcomes preceding the enactment of court orders, which provides additional support for the identification strategy.
On the other hand, there is suggestive evidence that reductions in school segregation levels that were not accompanied by significant changes in school resources did not have equally large impacts on blacks’ adult attainments.

In general, the magnitudes of the desegregation impacts across the various adult outcomes for blacks were insensitive to how much reduction in racial school segregation resulted from court orders.
Interestingly, once again I find no effects on whites in either the duration of desegregation exposure nor the resultant change in school resources.
In order to summarize the results on the mechanisms, I estimate 2SLS models in which the key explanatory variables of interest—average per-pupil spending experienced during one’s school-age years and the average level of racial school integration (i.e., the average black-white exposure index during ages 5-17)—are predicted in a first-stage model using the individual’s duration of desegregation exposure interacted with the respective school district's desegregation- induced change in school spending (segregation).
The 2SLS models are presented in Table F2 for the main adult attainment outcomes, and include the same set of controls as the prior models, estimated separately by race.

These estimates are not intended to be interpreted as the causal impacts of school spending per se, but rather as markers of the intensity of treatment that may capture the combined effects of improvements in school resources and teacher quality.
To facilitate interpretation of marginal effects, the units of the average per-pupil spending during an individual’s school-age years are in thousands of dollars—thus, a 1-unit change represents a $1,000 change in spending (2000 dollars) in each of one’s K-12 years.
In similar fashion, the key school segregation variable is defined such that a one-unit increase in "Black- White Exposure Index (age 5-17)" represents a 0.15 increase in the black-white exposure index or a standard deviation increase in racial school integration experienced in each of one's K-12 years.ii The 2SLS results highlight significant positive effects of desegregation-induced increases in school spending on blacks’ adult attainments.
In contrast, these 2SLS models reveal small, insignificant effects for increases in racial integration (holding spending changes constant).

As a placebo falsification test using the 2SLS models, it is shown in Table F3 that school spending increases have no significant impacts on adult outcomes when they occur during non-school ages (after age 19), but rather all the estimated long-run effects of per-pupil spending are confined to school-age years of exposure, as we would expect.
The results for blacks indicate that a $1,000 increase in school spending (which corresponds to roughly a 25-30 percent increase) experienced throughout one’s school-age years is associated with an additional 1.4 years of completed education, a 58 percent increase in wages, an increase of $18,635 in annual family income, a 34 percentage-point reduction in the annual incidence of adult poverty, and a 2.1 percentage-point reduction in the annual incidence of adult incarceration.
These magnitudes are similar to the previously discussed event study results (Figures 5-13) in comparisons of individuals exposed to desegregation beginning in one’s elementary school years relative to growing up in segregated schools throughout one’s school years.

There are no corresponding significant effects for whites on either of these markers of the intensity of treatment across the adult outcomes.
i The estimated equation also includes the main effects without the interaction terms in school spending and segregation; equation (F1) abstracts from this to ease the number of terms shown.
The school spending and segregation terms are centered around the average desegregation-induced changes ($1,000 for per-pupil spending; 0.15 for black-white exposure index), so that the coefficient on the main desegregation exposure term represent the desegregation impact for the average change in these key school inputs.
These models use the same sample as the aforementioned ones but include dummy indicators if district-specific desegregation induced-changes in per-pupil spending (school segregation) cannot be computed because of missing data; the occurrence of missing data occurs most often in small, rural areas.
ii The excluded instrument for this school spending (segregation) variable is the number of school-age-years of desegregation exposure interacted with the respective school district’s desegregation-induced change in school spending (segregation).

ONLINE APPENDIX F: Exploring Mechanisms FIGURE F1.
Relationship between Magnitudes of Desegregation-Induced Changes in School Segregation & School Spending n i e g n a h C ) s 0 0 0 ( i g n d n e p S l o o h c S 3 2.5 2 1.5 1 .5 0 -.1 Change in Racial Integration (Black-White Exposure Index) .2 .3 .1 0 .4 Fitted values District-specific effect Note: I find that the main predictor of desegregation-induced changes in school spending is pre- treatment (1960) District % black, not 1960 county poverty rates & other factors.
Furthermore, I find that the desegregation-induced changes in per-pupil spending & racial school integration are similar in districts that overlap the PSID sample vs the full universe of court-ordered districts.

This lends further support to the representativeness of the PSID & generalizability of results for these birth cohorts.

ONLINE APPENDIX F: Exploring Mechanisms Table F1.
Interactive Effects of Court-Ordered School Desegregation & Induced-Change in Per-Pupil Spending on Educational Attainment, by Race Exposure to Court-Ordered Desegregation (Year aged 17 - Year of Initial Court Order), spline: (-7 to -1): (no exposure, linear trend prior to court order) (-7 to -1)*↑ΔPer-Pupil Spending(t-1,t+4) (-7 to -1)*↑ΔBlack-White Exposure Index(t-1,t+4) >0: any exposure (dummy indicator)1 (any exposure)*↑ΔPer-Pupil Spending(t-1,t+4) (any exposure)*↑ΔBlack-White Exposure Index(t-1,t+4) (1 to 12): # of school-age exposure years (# of exposure years)*↑ΔPer-Pupil Spending(t-1,t+4) (# of exposure years)*↑ΔBlack-White Exposure Index(t-1,t+4) ≥13: exposed for all K-12 years (dummy indicator) (exposed all K-12)*↑ΔPer-Pupil Spending(t-1,t+4) (exposed all K-12)*↑ΔBlack-White Exposure Index(t-1,t+4) Dependent variable: Years of Education (1) (2) (3) (4) Blacks Whites 0.0185 (0.0629) -0.0433 (0.0486) 0.4990** (0.2414) 0.3443* (0.1827) 0.1021** (0.0442) -0.0282 (0.0270) 0.3984+ (0.2723) 0.3202+ (0.02233) 0.0226 (0.0648) -0.0423 (0.0498) -0.0198 (0.0249) 0.4362* (0.2369) 0.3587** (0.1812) -0.0203 (0.0943) 0.1043** (0.0419) -0.0222 (0.0288) -0.0595*** (0.0181) 0.3821+ (0.2898) 0.2512 (0.2361) 0.0874 (0.1694) 3,962 1,404 312 0.0382 (0.0589) 0.0244 (0.0440) -0.1636 (0.3462) 0.1274 (0.1759) 0.0161 (0.0551) -0.0265 (0.0378) -0.2249 (0.3546) 0.1501 (0.3771) 2,878 1,398 457 0.0458 (0.0559) 0.0236 (0.0442) -0.0070 (0.0134) -0.1600 (0.3308) 0.1333 (0.1765) -0.0315 (0.0719) 0.0162 (0.0558) -0.0259 (0.0380) -0.0029 (0.0174) -0.2278 (0.3577) 0.1421 (0.3797) -0.1589 (0.2805) 2,878 1,398 457 Number of individuals Number of childhood families Number of school districts Robust standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 (2-tailed test); +p<.10 (one-tailed test) 3,962 1,404 312 Footnote 1: The variable "# of school-age exposure years " is centered around 5 (i.e., any exposure *(# of exposure yrs - 5)), so that the coefficient on the "any exposure " dummy indicator can be interpreted as the average effect of 5 years of desegregation exposure.
The estimated district-specific induced-change in per-pupil spending (school segregation) are net of school district fixed effects and district-specific time trends; these changes are centered around the respective average change ($1,000 for per-pupil spending; 0.15 for black-white exposure index) in the model, so that the main effects capture the average desegregation impact (see also Figures 1-3).
Sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
All models include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
The models include dummy indicators for each event study year < -7 and each event study year > 13 -- the coefficients on these vars are suppressed to conserve space.

Table F2.

Exploring the Mechanisms: School Spending vs Racial School Integration.

2SLS Estimates of Desegregation-Induced Effects of Per-Pupil Spending on Adult Socioeconomic Attainments by Race.
ONLINE APPENDIX F: Exploring Mechanisms Years of Education Ln(Wage), age 20-50 age 20-50 Annual Family Income, Poverty: Prob(Poverty), age 20-50 Annual Incidence of Incarceration: Prob(Incarceration), age 18-30 Second Stage, Dependent variable: Annual Incidence of Adult School District Per-pupil Spending(age 5-17) Black-White Exposure Index(age 5-17) (1) Blacks 1.4475* (0.8963) -0.2810 (0.7693) (2) Whites 0.1619 (0.8841) -0.4774 (1.6172) (3) Blacks 0.6602* (0.3786) -0.2952 (0.4580) (4) Whites -0.1851 (0.2301) 0.1889 (0.3910) (5) Blacks (6) White 18,634,65* 17,045.85 (9,183.16) (21,066.61) -8,077.57 6,608.08 (11,412.88) (42,839.11) (7) Blacks -0.3399* (0.1984) 0.2033 (0.2395) (8) Whites -0.0758 (0.0594) 0.0713 (0.0821) (9) Blacks -0.0212* (0.0118) -0.0093 (0.0119) (10) Whites -0.0102 (0.0166) 0.0136 (0.0095) -- 4,291 1,458 274 -- 2,611 1,328 326 18,435 2,289 904 192 16,063 1,651 878 265 Number of person-year observations Number of individuals Number of childhood families Number of school districts Robust standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 Data: Sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
The estimated district-specific desegregation induced-change in per-pupil spending (school segregation) are net of school district fixed effects, district-specific time trends, & coincident policy changes (see also Figures 1B, 3A).
The key (instrumented) variables are defined such that a one-unit increase in "School District Per-pupil Spending(age 5-17) " represents a $1,000 spending increase in each of one's K-12 years (roughly a standard deviation increase); and a one-unit increase in "Black-White Exposure Index (age 5- 17) " represents a 0.15 increase in the black-white exposure index or a standard deviation increase in racial school integration experienced in each of one's K-12 years.
Models: The first-stage models, which are highly significant, include as predictors the # of school-age years of exposure to desegregation interacted with the respective district's desegregation-induced changes in school spending and racial school segregation, respectively; these are the excluded instruments for the school spending and segregation variables.
Results are based on 2SLS models that include: school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight) and controls for gender, age (cubic).
26,863 2,630 966 198 39,032 2,581 792 132 31,016 1,920 896 290 31,100 2,611 1,328 326 26,863 2,630 966 198 31,100 2,611 1,328 326 ONLINE APPENDIX F: Exploring Mechanisms Table F3.

Exploring the Mechanisms.
2SLS Estimates of Desegregation-Induced Effects of Per-Pupil Spending on Black's Adult Socioeconomic Attainments: Placebo Tests for non-school ages Blacks Second Stage, Dependent variable: School District Per-pupil Spending(age 5-17) School District Per-pupil Spending(age 20-24) Years of Education (1) 1.1841*** (0.4522) -0.4702 (0.3285) Annual Family Ln(Wage), age 20-50 Income, age 20-50 Annual Incidence of Adult Poverty: Prob(Poverty), Annual Incidence of Incarceration: Prob(Incarceration) age 18-30 age 20-50 (2) 0.5176** (0.2611) -0.0255 (0.1538) (3) 13,732.27+ (9065.39) -16,010.87*** (4,457.67) (4) -0.2796* (0.1529) 0.1740*** (0.0538) (5) -0.0170+ (0.0126) -0.0056 (0.0072) -- 3,951 1,341 202 138 Number of person-year observations Number of individuals Number of childhood families Number of school districts Number of childhood counties Robust standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 (2-tailed test); +p<.10 (one-tailed test) Data: Sample includes all PSID black individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
The estimated district-specific desegregation induced-change in per-pupil spending is net of school district fixed effects, district-specific time trends, and coincident policy changes (see also Figure 3).

The key (instrumented) variables are defined such that a one-unit increase in "School District Per-pupil Spending(age 5-17)" represents a $1,000 spending increase in each of one's K-12 years (roughly a standard deviation increase).
38,701 2,565 781 118 63 24,839 2,457 916 147 102 24,839 2,457 916 147 102 17,654 2,204 875 147 102 Models: The first-stage models, which are highly significant, include as predictors the # of years of exposure to desegregation (for relevant ages 5-17; 20- 24) interacted with the respective district's desegregation-induced change in school spending; these are the excluded instruments for the school spending variables.
Results are based on 2SLS models that include: school district fixed effects, race-specific year of birth fixed effects, race*census division- specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight), and controls for gender, age (cubic)).
Appendix G: Supplementary Regression Results & Validating the PSID Results Using Other Data: While the tests thus far show that the estimates are internally valid, readers might wonder how these patterns generalize to districts that are not included in the PSID.
To address this, I replicated the analyses for high school graduation using the combined Office of Civil Rights (OCR) data and Common Core Data (CCD)—Local Education Agency Universe Survey and Non-Fiscal Survey Database—for all school districts in the US, which together span the period 1972 to 1999.

I combine the district-level data and focus on dropout rates (grades 9-12) because this is the most reliable data that can be compared across time.
I focus on districts ever under court order with the preferred research design.

To validate the PSID analysis, I compute district-specific desegregation-induced increases in school spending and racial integration using the same method as that employed for the PSID data.

I link the timing of school desegregation and the district-specific induced changes in per-pupil spending and racial segregation (black-white exposure index) to the high school dropout data from the OCR-CCD by year.
I then estimate the effects of desegregation exposure and resultant increases in school spending (due to desegregation) on the district dropout rate.

Because high school dropout information at the district level is not disaggregated by race, I weight these models by the district’s (pre-desegregation) percent of enrollment that is black to attempt to capture average effects for black children.

I include the set of controls as the main results.


It is important to note that while one might expect the patterns in the OCR-CCD district-level data to be similar to those in the PSID, there are numerous reasons to expect some differences between the results presented in the PSID and the OCR-CCD samples.
First, because these data are at the district level rather than the individual level and because the OCR-CCD data are based on the school district attended (rather than the school district of birth) any effects might reflect changes in school composition that occur as a result of school quality changes associated with desegregation.
Finally, while I analyze the effect of desegregation exposure and induced effects of changes in school spending for an individual over their entre 12 years of public schooling in the PSID, in the OCR-CCD I analyze the effect of contemporaneous spending in a given year.

In sum, there are numerous reasons to expect differences between the results presented in the PSID and the OCR-CCD samples.
However, should the results be similar between the OCR-CCD data and the PSID sample, this robustness check would indicate that my findings are robust and generalizable.

I estimate a parametric event study model with event study years interacted with the desegregation- induced changes in school spending and racial segregation, respectively (results presented in Appendix Table G2).
First, I find that districts that underwent larger changes in school spending resultant from desegregation exhibited increasing high school dropout rates in the years preceding the enactment of court orders.

The results show that this pre-existing trend was subsequently reversed in districts in which desegregation led to significant increases in per-pupil spending.
In particular, the results indicate that a $1,000 increase in per-pupil spending is associated with a 5-percentage point reduction in high school dropout rates in the first five years following desegregation.

Note that this estimate is not directly comparable to that from the PSID sample because this estimate is based on annual spending at the district level, not the cumulative effect of a sustained spending increase (experienced at the student level) for all 12 years of a student’s life.
Because we expect the latter to be much larger, the results from the OCR- CCD data are consistent with those from the PSID.

The results suggest that high school dropout rates were insensitive to how much reduction in racial school segregation results from court orders.

In this respect as well, the findings reveal similar patterns with my main PSID results.

Identification from Timing of Initial Court Orders (exogenous) vs Timing of Major Desegregation Plan Implementation: Appendix Table G1.
Replicating Guryan (AER , 2004) using PSID.
Effects of Court-Ordered School Desegregation on Educational Attainment, by Race Dependent variable: ONLINE APPENDIX G: Supplementary Regression Results, Validating the PSID Results Using Other Data Timing of Major Desegregation Plan Implementation: (Year aged 17 - Year of Major Plan Implementation) (-7 to -1): (no exposure, linear trend prior to major plan implementation) >0: any exposure (dummy indicator)1 (1 to 12): # of school-age exposure years Exposure to Court-Ordered Desegregation: (Year aged 17 - Year of Initial Court Order), spline: (-7 to -1): (no exposure, linear trend prior to court order) >0: any exposure (dummy indicator)1 (1 to 12): # of school-age exposure years ≥13: exposed for all K-12 years (dummy indicator) 14: (beyond school-age years of exposure) 15: (beyond school-age years of exposure) Probability(High School Graduate) Replicating Guryan, Use Timing of Major Desegregation Plan Implementation Use Timing of Initial Court Orders (1) Whites (2) -0.0071 (0.0510) 0.0419* (0.0244) (3) Blacks -0.0151* (0.0082) 0.0468* (0.0273) (4) (5) (6) Blacks -0.0152+ (0.0105) 0.0460* (0.0267) -0.0002 (0.0051) 0.0039 (0.0104) 0.0072 (0.0149) 0.1375*** (0.0531) 0.0201*** (0.0072) 0.0961** (0.0482) -0.0244 (0.0429) 0.0119 (0.0544) no 4,116 1,465 326 269 0.0667* (0.0390) 0.0195*** (0.0060) 0.1001* (0.0587) -0.0261 (0.0616) 0.0462 (0.0724) yes 2,901 894 120 75 Sample restricted to districts that overlap Welch/Light Deseg Data?
Number of individuals Number of childhood families Number of school districts Number of childhood counties Robust standard errors in parentheses (clustered at school district level) *** p<0.01, ** p<0.05, * p<0.10 Footnote 1: In columns (4)-(6), the variable "# of school-age exposure years " is centered around 5 (i.e., any exposure *(# of exposure yrs - 5)), so that the coefficient on the "any exposure " dummy indicator can be interpreted as the average effect of 5 years of desegregation exposure.
yes 2,293 1,194 194 98 yes 2,901 894 120 75 yes 2,901 894 120 75 yes 2,901 894 120 75 Sample includes all PSID individuals born 1945-1968, followed into adulthood through 2011, who grew up in school districts that were ever subject to court-ordered desegregation.
All models include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division-specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; and controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender).
Models include dummy indicators for each event study year <-7 (columns 3-6) and each event study year > 15 (columns 4-6) -- the coefficients on these vars are suppressed to conserve space.

See corresponding non-parametric & parametric event study model results presented in Figure 1.

Appendix Table G2.

Using OCR-CCD District-level Data to Explore the Mechanisms: ONLINE APPENDIX G: Supplementary Regression Results, Validating the PSID Results Using Other Data School Spending vs Racial School Integration.
2SLS Estimates of Desegregation-Induced Effects of Per-Pupil Spending on High School Dropout Rates.
Pre-Desegregation: (-7 to -1): (no exposure, linear trend prior to court order) (-7 to -1)*↑ΔPer-Pupil Spending(t-1,t+4) (-7 to -1)*↑ΔBlack-White Exposure Index(t-1,t+4) Exposure to Court-Ordered Desegregation: (exposed)*↑ΔPer-Pupil Spending(t-1,t+4) (exposed)*↑ΔBlack-White Exposure Index(t-1,t+4) Number of district-year observations Number of school districts Second Stage, Dependent variable: High School Dropout Rate (%) (1) 0.9629* (0.5223) 3.2876*** (0.9095) -5.3806* (3.0060) 3,066 587 (2) 0.7778 (0.7073) 3.2716*** (0.9037) 0.0313 (0.2375) -5.5910* (2.9516) 3.6711 (5.1750) 3,066 587 ONLINE APPENDIX G: Supplementary Regression Results Appendix Table G3.
Additional Specifications: Similar Estimated Effects of Desegregation in South and Non-South (Main Effects apply to Blacks) Years of Exposure to Court-Ordered Desegregation(age 5-17) Years of Exposure to Court-Ordered Desegregation(age 5-17)*South Years of Exposure to Court-Ordered Desegregation(age 5-17)*White Years of Exposure to Court-Ordered Desegregation(age 5-17)*South*White Number of individuals Number of childhood families Number of school districts ***p<0.01, **p<0.05, *p<0.10; Robust standard errors in parentheses (clustered at school district level) Model includes same sample and set of control variables as main results.
Dependent variable: Years of Education 0.1049** (0.0424) -0.0108 (0.0528) -0.0618 (0.0501) -0.0391 (0.0494) 8,548 3,562 631 Appendix Table G4.
Effects of Desegregation Exposure on Blacks' Adult Outcomes & the Returns to Education ONLINE APPENDIX G: Supplementary Regression Results Years of Education Probability Annual Work Ln(Wage), (Poverty), age 20-50 age 20-50 Hours, age 20-50 Annual Family Income, age 20-50 Occupational Prestige Index Probability (Ever Incarcerated) Probability (Incarcerated), age 18-30 Adult Health Status Index, age 20-50 5-Year Exposure to Desegregation 0.4800** (0.1905) 0.1516*** (0.0506) 164.5327** (76.4113) -0.1101** (0.0470) 5,893.032** (2,695.461) 5.1932** (2.2841) -0.1420*** (0.0378) -0.0147** (0.0065) 3.3401*** (1.2434) Implied Wald Estimate of Returns to Education (quantity/quality) Mean for Blacks (at age 30) Mean for Whites (at age 30) *** p<0.01, ** p<0.05, * p<0.10 -- 0.3158 342.7765 0.2294 $12,277 10.8192 0.2958 0.0306 6.9585 12.60 13.51 2.26 2.63 1,540.06 1,895.99 0.24 0.05 $31,020 $52,937 34.42 48.57 0.08 0.04 0.0063 0.0014 84.16 88.78 This sumary table contains the main results for blacks based on event study estimates shown in Figures 5-14.
Sample includes all PSID individuals born 1945-1968, followed into adulthood through 2013, who grew up in school districts that were ever subject to court-ordered desegregation.
All models include: race-specific school district fixed effects, race-specific year of birth fixed effects, race*census division- specific linear cohort trends; controls at the county-level for the timing of hospital desegregation*race, roll-out of "War on Poverty" & related safety-net programs (community health centers, county expenditures on Head Start (at age 4), food stamps, medicaid, AFDC, UI, Title-I (average during childhood yrs), timing of state-funded Kindergarten intro); controls for 1960 county characteristics (poverty rate, percent black, education, percent urban, population size, percent voted for Strom Thurmond in 1948 Presidential election*race (proxy for segregationist preferences)) each interacted with linear cohort trends; controls for childhood family characteristics (parental income/education/occupation, mother's marital status at birth, birth weight, gender) and age (cubic).