We find a strong positive raw correlation between black exposure to whites in their school district and the prevalence of later mixed-race (black-white) births, consistent with the literature on residential segregation and endogamy. However, that relationship is significantly attenuated by the addition of a few control variables, suggesting that individuals with higher propensities to have mixed-race births are more likely to live in desegregated school districts. We exploit quasi-random variation from court-ordered school desegregation to estimate causal effects of school desegregation on mixed-race childbearing, finding small to moderate effects that are largely statistically insignificant. Because the upward trend across cohorts in mixed-race childbearing was substantial, separating the effects of desegregation plans from secular cohort trends is difficult; results are sensitive to how we specify the cohort trends and to the inclusion of Chicago/Cook County in the sample. The fact that the addition of a few control variables substantially weakens the cross-sectional relationship between lower levels of school segregation and higher rates of mixed-race childbearing suggests that a substantial portion of the observed correlation is likely due to who chooses to live in places with desegregated schools. Researchers should be cautious about interpreting raw correlations between segregation—whether residential or school—and other outcomes as causal. Our results also point to the need to carefully explore specification of cohort effects in quasi-experimental designs for treatments where cumulative exposure is important.
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Batson et al. (2006) find this to be particularly important for studying endogamy, with interracial couples constituting a higher share of all cohabiting couples than of all married couples.
Atkinson, MacDorman, and Parker (2001) describe trends in mixed-race births in the USA from 1971 to 1995.
We recently became aware of a working paper by Shen (2016), which also examines the effects of court-ordered school desegregation on biracial births in addition to other birth outcomes. Our results are consistent with her findings, but we explore more specifications, which reveal the results are more sensitive than that paper suggests, so we characterize the findings differently.
Due to data limitations, we treat blacks as a monolithic group despite the within-race diversity detailed by Batson et al. (2006).
The trends in births to white mothers (and fathers) where the other parent is black are quite similar but the levels are about one-tenth of those shown in Fig. 1, reflecting blacks’ smaller share of the population.
Father’s race is not always reported on birth records. For this figure and the main analysis below, we include only observations where the father’s race is reported.
Not all districts required court supervision to desegregate—only about half of districts in the former Confederacy were ever supervised by a court by 1976. Some districts desegregated voluntarily or in response to the threat of withdrawal of federal funds. Court-ordered school desegregation plans were particularly important for larger districts, districts with high black enrollment shares, and districts with stronger historical preferences for segregation (Cascio et al. 2008).
We refer the reader to Fryer (2007) for the history of state-level anti-miscegenation laws in the USA.
Kalmijn and Van Tubergen (2010) find that culture and preferences are more important than structural factors (such as exposure per se) in determining intermarriage rates across national origin groups in the USA.
For the mixed-race birth to be observed in the natality data, the mother also must report information about the father. We discuss the implications of missing data for fathers for the analysis below.
See Pettigrew and Tropp (2006) for a review and meta-analysis of the experimental and observational literature on impact of intergroup contact.
The subjects generally describe interracial dating in these recently integrated public high schools as present, but infrequent and clandestine.
Welch and Light (1987) took a stratified random sample of large districts with significant minority and non-minority populations. See Welch and Light (1987) for more detail. Implementation of a “major desegregation plan,” as defined by Welch and Light, caused large reductions in school segregation on average (Guryan 2004 and Reber 2005; replicated in Fig. 3). The American Communities Project at Brown University collected data on desegregation court cases in a larger number of school districts. Because it was designed for examining correlates of longer-term trends in segregation over decades (Logan et al. 2008), it has less detail on when desegregation plans were actually implemented and their content.
Black exposure to whites can be interpreted as the white share of enrollment in the average black’s school and vice-versa for white exposure to blacks. The dissimilarity index can be interpreted as the share of blacks (or whites) that would have to be reassigned to another school so that every school in the district has the same racial composition. See Reber (2005) and references therein for more detail.
We report segregation for these years because they span most of the desegregation activity and have relatively little missing data.
See Reber (2005) for more details on these analyses.
We exclude three Virginia counties (Norfolk, Roanoke, and Pittsylvania) that include WL districts because their geography is not consistently coded over time, and Richland County, SC, because comparison of counts of births in the natality file to the population of the county and counts of births in the 1960 County Data book suggest it is miscoded in the natality data. Two counties contain more than one treated district; we code the desegregation years for these counties as follows: Los Angeles County contains three treated districts (Los Angeles Unified School District (1978), Long Beach Unified School District (1980), and Pasadena Unified School District (1970); because Los Angeles Unified is by far the largest district in the county, we assign 1978 as the treatment year for Los Angeles County. Jefferson County, AL, contains two treated districts (Birmingham City School District (1970) and Jefferson County School District (1971)); both have considerable enrollment, so we assign Jefferson County the earlier treatment year (1970).
We use the 1970 School District Data Book (SDDB) to calculate this; this calculation excludes that of Rochester and Buffalo due to difficulties processing the raw files for New York State.
In some early years and states, the available births data are a 50% sample of all births. We use the appropriate weights to account for this sampling, and the samples are typically quite large.
While this will not hold for all cases, we do not observe information on year of high school graduation in the birth records. We ultimately examine effects of the timing of desegregation over multi-year ranges, reducing the measurement error we expect to be associated with this assumption.
Although the level of segregation experienced throughout an individual’s schooling may influence subsequent mixed-race partnering, we assign the segregation index from the cohort’s senior year because the segregation data start in 1968, so we do not have information about the levels of segregation early in the careers of the early cohorts. We could impute or estimate these values, but we prefer the transparency and consistency of the senior-year measure. Following the endogamy literature, we use an exposure/isolation measure, rather than racial balance index such as the dissimilarity index; the results are broadly similar if we use the dissimilarity index.
The literature on endogamy suggests that residential segregation is a strong correlate of endogamy; unfortunately, we do not have good measures of residential segregation for this sample in 1960 to include in this analysis.
For consistency with the quasi-experimental analysis, the sample restrictions are the same as for Table 3 and described in the next section.
Housing discrimination limits the residential choice set for blacks.
In theory, we could also control for potential determinants of mixed-race childbearing at the individual level by estimating Eq (2) with micro data. For example, age and education are both predictors of exogamy and mixed-race childbearing. However, if school desegregation affects these outcomes, they are endogenous and including them would constitute over-controlling. In practice, education is not consistently reported in the natality data for the cohorts we study. In results not reported, we have controlled for parental age (even though it is potentially endogenous), and the results are unaffected.
The likelihood that a black mother, for example, has a child with a white father depends on the attitudes and availability of potential white partners and may therefore depend on potential partners’ exposure to desegregation plans. We do not have the statistical power to explicitly consider or control for the desegregation treatment status of potential partners, though it is likely highly correlated with own treatment status since potential partners are typically similarly aged. That is, in the mother sample, we consider exposure based on the mother’s birth year, and similarly for the father sample. In some sense, individuals are partially treated if potential partners are treated, so this may bias the results towards zero by creating measurement error in the assignment of treatment status.
Reber 2005 and our Fig. 3 show that desegregation plans reduced within-district segregation quickly, phasing in over only a couple of years. White flight played out over time, however, and did offset some of the initial increases in black exposure to whites. This implies that while blacks attending high school in a newly desegregated school had slightly more exposure to whites compared to later cohorts in the same district, the whites who remained might have been more (or less) tolerant of blacks. In any case, we cannot separate the effects of age of exposure, length of exposure, and phase-in of the plan itself.
White flight could have affected the probability that blacks who remain in the county have a white partner by changing the number and type of white partners available. In theory whites who “fled” (or did not come) could be more or less tolerant than those who stayed, but if those who “fled” had a low propensity to form a mixed-race relationship, their departure should have little effect on the mixed-race partnering of blacks in desegregating counties.
For the 1971, 1972, and 1973 cohorts, we could observe all births between ages 15 and 48; this should capture the overwhelming majority of lifetime fertility, especially for women. For these cohorts, 82, 83, 87, and 82% of all births were to parents ages 18 to 35 for black mothers, black fathers, white mothers, and white fathers, respectively.
The top five counties by sample size are Chicago/Cook County, Los Angeles County, Detroit/Wayne County, Philadelphia County, and Houston/Harris County. Table 5 in Appendix 1 repeats the specification reported in Table 3, and column 2 then reports estimates of the same specification, excluding one county at a time.
Chicago has a large influence on the results because (a) it contributes many observations to the analysis, (b) it had an unusually flat trend in mixed-race birth through the early cohorts, and (c) it had a relatively late plan implementation date (1982). Intuitively, this means that Chicago mostly acts as a control, “pulling down” the estimated trend in cohort effects and making the trends (and treatment effects) in other districts look more positive. While we prefer not to drop observations on an ad hoc basis, we would also not want to draw too strong a conclusion from analysis that is so sensitive to a single county. We therefore present a range of specifications demonstrating this sensitivity.
It is plausible that treatment effects are heterogeneous along county characteristics such as the share of the county that was black in 1960, the black/white median family income gap in 1970, region, and county population. Unfortunately, we lack the statistical power for these analyses to be informative, so we do not report the results.
For example, Bifulco et al. (2015) use the same identification strategy (court-ordered desegregation) and find that desegregation did not affect fertility for white teenagers, but increased teen fertility rates for blacks by three to 5%.
In theory, these compositional effects could be present without affecting total births, and we could see an effect on fertility without there being compositional effects. Since we cannot say much about the effects on fertility empirically, we do not explore this further.
We do not repeat this exercise for fathers because their state of birth is not reported in the natality data.
Information about the father, including race, is more likely to be missing when parents were not married. Though reporting of unmarried fathers’ characteristics increased over time, the simultaneous increase in the prevalence of non-marital births swamped this effect so that the overall share of births missing paternal race data increased nonetheless.
In our sample from 1968 to 2003, the share of births to black mothers in which the father’s race was not reported grew from 23 to 36%, while the share of births to black mothers in which the father’s race was reported as white grew from just 0.4 to 3.2%.
We cannot do the same sensitivity analysis for missing black fathers, as we do not know who they are.
For example, Shen analyzes first births in the main specifications, while we consider all births; Shen restricts the main analysis to mothers residing in the same state where they give birth, while we include all mothers (and all fathers for the black father sample). On these two issues, both papers do the opposite in at least some specification tests. We include data for 1968 and 1969, whereas Shen begins with 1970. Shen includes all ages but excludes some observations if the mom would have been too young to be exposed to desegregation when the birth took place; instead, we limit the sample to parents who were 18 to 35 consistently across counties (and check the sensitivity to the choice of ages in sensitivity analysis). We assign a treatment year of 1978 to Los Angeles County, whereas she assigns 1970; and we exclude a few counties from the analysis because we were worried about data quality (see footnote 23). We describe the more consequential differences in the main text.
Typically, in a difference-in-differences (or modified DD) analysis, the years (or cohorts) covered are the same for all counties, and the observations further from the treatment date are available to help pin down the cohort effects. For example, Oakland implemented a plan in 1966; this means that the younger cohorts (who graduated from high school after 1978) are dropped from Shen’s analysis. More typically, those observations would be kept so that they can contribute to the identification of the cohort effects for younger cohorts. We analyze a consistent set of cohorts for all counties. When the sample is restricted in this way, the estimates tend to be larger, likely because difficulty in estimating the cohort effects causes cohort trends to be attributed to treatment.
Both approaches are taken in the literature, but Cameron and Miller (2015) note that it is common when the treatment indicators vary at the cohort-county level to aggregate to that level before estimation.
In results not shown, we estimate our models separately for Southern and non-Southern counties. The estimates for the non-South show a similar pattern as the full sample; the estimates for the South are imprecise and even more sensitive to specification (and sometimes negative).
Court rulings in the early 1990s made it easier for districts to be released from court-ordered desegregation plans, and a number of districts discontinued their plans in the following decades. These changes do not affect the cohorts in our study.
Theoretically, desegregation could have produced a more gradual change in segregation. For example, if there was a long phase in of the plan (for example, if districts desegregated one grade at a time), we would not expect a break in the trend around the time of plan implementation, but rather a change in slope, which is more difficult to identify.
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The authors thank Sarena Goodman, Paco Martorell, Martin West, seminar participants at UCLA, the Bureau of Labor Statistics, APPAM, Georgetown, UC Irvine, the University of Virginia, and the Association for Education Finance and Policy, and two anonymous referees for helpful comments.
Conflict of interest
The authors declare that they have no conflict of interest.
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Gordon, N., Reber, S. The effects of school desegregation on mixed-race births. J Popul Econ 31, 561–596 (2018). https://doi.org/10.1007/s00148-017-0662-z
- School desegregation
- Interracial births
- Cohort effects