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We use the census block as the definition of neighborhood, which comprises a smaller geographic area than most previous studies utilize, and we match childhood residential location address histories to blocks and school district boundaries that prevailed in 1969 (the algorithm is outlined in Appendix A).17 Each record is merged with data on school spending for 1960–2000 and the aforementioned school finance variables at the school district level that correspond with the prevailing levels during their school-age years. We also merge information on studentteacher ratios and school segregation indices to the PSID data using the census block/tract contained in the geocode file based on the earliest available address in childhood (or county of birth when census block information is unavailable).

After combining information from these data sources, the main sample used to analyze adult attainment outcomes consists of PSID individuals born between 1955 and 1985. It includes


  Centers for Medicare and Medicaid Services data files (dating back to the 1960s) to identify the precise date in which a Medicare-certified hospital was established in each county of the U.S. (an accurate marker for hospital desegregation compliance).

16 The PSID maintains high wave-to-wave response rates of 95–98 percent. Studies have concluded that the PSID sample of heads of households and spouses remains representative of the national sample of adults (Gottschalk et al., 1999; Becketti et al., 1997).

17 Many school districts were counties during this period, including more than one-half of Southern school districts.


93,022 adult person-year observations of 15,353 individuals (9,035 poor children; 6,318 nonpoor children) from 1,409 school districts, 1,031 counties, and all 50 states and the District of Columbia. Given the data structure, the oldest cohort is observed at age 56, while many cohorts are observed at age 30. To compare individuals from different cohorts at around the same age, we focus on those adult observations between the ages of 25 and 45. The mean age is 32.9 years for the economic outcome measures considered. The set of adult outcomes examined chronologically over the life cycle include (a) educational outcomes—whether graduated from high school, years of completed education – and (b) labor market and economic status outcomes (all expressed in 2000 dollars)—wages, family income, and annual incidence of poverty in adulthood (ages 25–45). All analyses include men and women with controls for gender.

Summary statistics are presented in Table 1.

V. Empirical Strategy for Estimating Effects on Adult Outcomes In this section, we investigate whether changes in school spending induced by SFRs have long-run impacts on adult outcomes. Particular attention is given to determine whether the increased school spending experienced by children in lower-income communities due to SFRs had any lasting effects on their adult socioeconomic well-being. Our empirical approach uses two distinct sources of variation in per-pupil spending experienced during one’s school-age years: first we exploit the staggered timing of court-mandated school finance reforms across districts to implement a cohort level “event-study” analysis (variation in the timing of reforms across cohorts); second, we exploit the fact that the same reform led to different changes in spending across districts (variation in treatment intensity for exposed cohorts). We detail how all this variation is used within a single framework in Section V.b.

While Part I shows that many reforms change the distribution of school spending, we focus the analysis in Part II on school spending changes associated with the passage of courtordered reforms. This choice was driven by the fact that court-mandated reforms exhibited minimal trending in spending prior to those reforms (suggesting that there might be minimal prereform trending in adult outcomes across cohorts), and court-mandated reforms generated large, robust, and statistically significant increases in per-pupil spending for low-income neighborhoods (within which many of the PSID respondents resided).

While understanding the effect of school finance reforms on adult outcomes is important, exploiting exogenous variation in per-pupil spending due to reforms allows for an investigation 24     into the broader question of whether increasing school spending can improve the longer run outcomes of affected students. Simply comparing outcomes of students exposed to more or less school spending, even within the same district, could lead to biased estimates of the effect of school spending on student outcomes, if there were other factors that affect both student outcomes and school spending simultaneously. For example, a decline in the local economy could depress per-pupil spending (through home prices or tax rates) and also have deleterious effects on student outcomes through mechanisms unrelated to school spending such as parental income. This would result in a spurious positive correlation between per-pupil spending and child outcomes. Conversely, an inflow of low-income students might lead to an inflow of compensatory federal funding while simultaneously generating reduced student outcomes. This would lead to a spurious negative relationship between spending and student outcomes.

By focusing only on exogenous changes in school spending within districts associated with reforms, our approach removes potential biases that might exist when simply comparing students who have been exposed to different levels of school spending for reasons unknown to the researcher. As in the analysis of school spending, we employ a flexible event-study design to map how adult outcomes evolve over time (i.e. across cohorts) before and after reform-induced changes in school spending. The event-study models allow us to examine how subsequent adult outcomes are impacted by both the amount of (reform-induced) changes in school spending as well as the duration of exposure to these spending changes during one’s school-age years. The design also allows us to examine pre-reform trends in outcomes to test for potential endogeneity of the timing of reforms. In Section VI, we show that isolating exogenous variation in school spending leads one to very different conclusions about the productivity of education spending than simple comparisons that do not account for the possibility that changes in school spending might be endogenous to student outcomes.

a. Hypothesized Effects Across Cohorts There are two natural tests of whether spending changes associated with school finance reforms have a causal effect on adult outcomes. The first test is whether exposed cohorts from those districts that experienced increases in per-pupil school spending also had improved outcomes relative to unexposed cohorts from the same district. The second test is whether the improvements observed for exposed cohorts (relative to unexposed cohorts) are larger for those from districts that experienced larger increases in per-pupil school spending. Because not all cohorts within a district are equally treated (some are exposed to spending increases for more of 25     their school years than others), and not all districts experience the same changes in spending after reforms (some districts experience larger spending increases than others), both of these tests can be implemented within a single event-study framework. We lay out the cross-cohort and crossdistrict patterns in outcomes one should observe in an event-study analysis if there is a causal effect of increased spending due to reforms on adult outcomes.

If there is a causal effect of increased school spending on adult outcomes, and there are no pre-existing cohort trend differences across districts that experience increases in spending, then an event-time figure across cohorts for a given increase in school spending should follow patterns similar to the stylized patterns presented in Figure 11. On the x-axis is the years of exposure to the reform for a given cohort, and on the y-axis is the cohort-level mean of some outcome for which higher values are better.

For those cohorts who were too old to be exposed to any reform-induced spending increases (to the left of 0 such that they were 18 or older at the time of the passage of reforms), there should be no systematic increase or decrease in the outcome across cohorts because none of these cohorts was exposed. As such, an event-study graph of outcomes by cohort should be relatively flat across cohorts that were too old to be affected by the reforms. Also, because prereform cohorts are not exposed to any spending changes, outcomes should be similar across the pre-reform cohorts both in districts that experienced large increases in school spending due to reforms and those that experienced small increases in school spending due to reforms.

For those cohorts who were of school-going age when reforms were implemented (i.e.

those who were between the ages of 5 and 17, indicated by relative years 0 to 12 on the x-axis), outcomes should both be better than those for the unexposed cohorts and increasing in the number of years of exposure. That is, cohorts that are exposed to increased spending for a longer period of time should have better outcomes than cohorts exposed to the same spending increase but for a shorter period of time (variation in timing). Additionally, for a given duration of exposure, individuals from districts that experienced larger increases in spending should have larger improvements in outcomes than those from districts with smaller increases in spending (variation in intensity). As such, the relationship between years of exposure and good outcomes should be positive and it should be more positive for districts that experience larger increases in spending. This is depicted in the two upward sloping segments for the partially exposed cohorts, where the dashed line is steeper for larger increases in spending.

Finally, among more recent cohorts (i.e., those who were younger than 5 or unborn at the 26     passage of reforms) all 12 of their school-age years were post-reform, and as a result, we hypothesize these cohorts should have better outcomes than the partially exposed cohorts, and there should be no systematic increase or decrease in the outcome among these fully treated cohorts. As with the partially exposed cohorts, for a given duration of exposure individuals in districts with larger increases in spending should have larger improvements in outcomes than those in districts that experienced smaller increases in spending. This leads to better outcomes (relative to untreated cohorts) for the fully treated cohorts from high-increase spending districts than low-increase spending districts.

In sum, if (a) there is a causal effect of spending on outcomes and (b) the district-level spending increases due to reforms are exogenous to changes in the outcomes, then the plot of the event-time indicator variables for districts that experience small and large spending increases due to reforms should follow the stylized patterns in Figure 11. That is, outcomes should be improving in years of exposure to reforms (variation in time) and the relative improvements should be larger in districts that experienced larger increases in school spending (variation in intensity).

b. Analyzing the Effect of School Spending on Adult Outcomes To show evidence of causal relationships, we test for the specific patterns hypothesized in Figure 11 semi-parametrically across a variety of adult outcomes. While looking for differences across cohorts can be achieved with a flexible event-study analysis, testing for differences across districts that experienced larger or smaller increases in spending requires a good measure of the court-mandated reform-induced increase in school spending. The event-study analysis documented that districts in the bottom quartile of the state’s income distribution in 1962 experienced larger increases in school spending than those in high-income quartiles. As such, the district’s quartile in the income distribution pre-reform could serve as a proxy for the extent to which reforms increased funding in the district. However, this is a relatively weak proxy for increases in spending at the individual district level because (a) not all court-mandated reforms had the same effect on all districts, and (b) not all reforms had the same distributional effects on districts within a state. As such, to test for whether those districts that experienced larger increases in school spending were those that experienced larger improvements in adult outcomes requires having a good measure of the increases in school spending resultant from the implementation of a court-mandated reform at the individual district level.

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