«THE EFFECT OF SCHOOL FINANCE REFORMS ON THE DISTRIBUTION OF SPENDING, ACADEMIC ACHIEVEMENT, AND ADULT OUTCOMES C. Kirabo Jackson Rucker Johnson ...»
The 2SLS/IV estimates for adult economic outcomes are presented in Table 3. As shown 37 in the top panel of Column 4, the 2SLS/IV estimates reveal that, for children from poor families, increasing per-pupil spending by 20 percent in all 12 school-age years increases adult wages by
24.6 percent. The 95 percent confidence interval is between 3.4 and 45 percent. The point estimate of 0.246 implies an elasticity of wages with respect to per-pupil spending of close to one. However, standard errors support a range of elasticities between 0.17 and 2.28. The results suggest that the effect of increasing school spending by 20 percent in all school age years is large enough to eliminate the wage gap between children from low- and high-income families. In contrast, the 2SLS estimate for children from non-poor families is statistically insignificant and of the opposite sign (top panel of column 6).
The 2SLS/IV estimates for the adult family income are similar to those of other outcomes. As shown in the middle panel of Column 4, the results indicate that for children from poor families, increasing per-pupil spending by 20 percent in all 12 school-age years increases family income by 52.2 percent. The 95 percent confidence interval is between 17.4 and 86 percent. As with wages, the results suggest that the effect of increasing school spending by 20 percent in all school age years is large enough to completely eliminate the family income gap between children from low-income families and those from non-poor families. We do not find any statistically significant effects of per-pupil spending on adult family income for children from non-poor families (middle panel of column 6).
The final outcome we present evidence on is the annual incidence of adult poverty.
Because this is an undesirable outcome, estimates should be interpreted such that lower numbers are better. The event study is presented in Figure 16. As with the other outcomes, there is strong evidence of a causal effect of school spending on outcomes for children from poor families and no effect for children from non-poor families. The left panel of Figure 16 shows that there is no pre-reform trending in outcomes across unexposed cohorts for individuals from poor families.
However, the exposed cohorts have steady declines in the annual incidence of adult poverty that become more pronounced in both years of exposure and the size of the districts’ increase in spending. In stark contrast to that for poor children, the event study for children from non-poor families (right) shows no systematic change in outcomes across cohorts/timing or treatment intensity. The 2SLS/IV results (lower panel of Table 3) mirror the findings from the event study models. The 2SLS/IV estimate for children from poor families indicates that increasing perpupil spending by 20 percent in all 12 school-age years reduces the annual incidence of poverty in adulthood by 19.7 percentage points. This estimated effect is statistically significantly at the 38 one percent level and the 95 percent confidence interval is between 8.23 and 31 percentage points.
To sum up, we find that for individuals from poor families, increases in school spending led to increases in adult economic attainment that rose in line with their educational improvements (likely reflecting a combination of improvements in both the quantity and quality of education received).26 Taken together, the event study graphs and the instrumental variables regression estimates based on exogenous changes in school spending present a compelling case that increased school spending caused by school finance reforms has meaningful causal effects on adult earnings, family income, and poverty status. We now present a few more robustness tests and discuss the findings in the context of prior studies in the literature.
a. Robustness Checks Falsification Tests: We probed the robustness of these 2SLS estimates further in several ways.
First, as a placebo falsification test using the 2SLS models, we estimate the marginal effect of school spending during non-school-age years. That is, we estimate 2SLS models similar to equation  where in addition to including school spending between the ages 5 and 17, we also include school spending between the ages 0 and 4 (when there should be no effect) and school spending between the ages of 20 and 24 (when there should also be no effect). Note that because some students do remain in school through age 19, we did not include school spending during ages 18 and 19 in the falsification test. To isolate exogenous changes in school spending for the different age ranges we use an instrument for exposure during the respective age ranges. As before, we instrument for school spending between ages 5 and 17 (school-age years) with the number of years of exposure between ages 5 and 17 interacted with the district-specific increase in spending. We instrument for school spending between ages 0 and 4 (pre-school-age years) with the number of years of exposure between ages 0 and 4 interacted with the district-specific increase in spending, and we instrument for school spending between ages 20 and 24 (postschool-age years) with the number of years of exposure between ages 20 and 24 interacted with the district-specific increase in spending. There is a strong first-stage relationship for each of the three endogenous regressors. If the effects documented for poor children are truly reflective of
the causal impacts of school spending, these effects should be present during school-age years with no corresponding effects for non-school-age years. The results of the placebo tests reveal this is indeed the case, as presented in Table 4 across the various long-run outcomes for children from poor families. For all outcomes, there are statistically significant effects of school spending during school-age years and no statistically significant effect of school spending for non-schoolage years. As further evidence of no effect for the non-school-age years, the placebo estimates are in different directions for the various outcomes showing that there was no tendency toward improving or deteriorating outcomes among unexposed cohorts in districts that saw larger or smaller increases in school spending. These falsification tests strongly support a causal interpretation of our main school spending estimates.
Validating Using Other Data: While the tests thus far show that our estimates are internally valid, readers might wonder how these patterns might generalize to districts that are not included in the PSID. To speak to this issue, we replicated the analyses for high school graduation using the Common Core Data (CCD)—Local Education Agency Universe Survey and Non-Fiscal Survey Database—for all school districts in the US for available years 1987with the preferred research design, as reported in Appendix B. We find a similar pattern of results for the effects of reform-induced school spending changes on district-level graduation and high school dropout rates (these effects are not broken up by poverty level). Using a variant of the models (based only on state-level variation), we are also able to replicate the patterns of our main findings using the Intergrated Public Use Microdata Series from the Census for educational attainment and adult earnings (Appendix C). The similar pattern of the PSID, CCD, and Census results demonstrate that the findings are generalizable and representative for these birth cohorts, and assuage concerns that the results are specific to the PSID.
The results support a causal interpretation of the effects of per-pupil spending by uncovering sharp differences in the estimated long-run effects on cohorts born within a fairly narrow window of each other based on whether, how long, and how much SFR influenced perpupil spending during their K–12 school years. The evidence is not consistent with alternative counter-explanations or causes. Based on the robustness of the results, such an alternative cause would have to meet the following strict criteria: (a) it closely follows the timing of passage of court-mandated SFRs (given the evidence showing no pre-existing time trends); (b) its effects are constrained only to school-age years of exposure (given the evidence showing no effects for 40 non-school-age years for both pre-school ages and beyond age 17); (c) it had the largest effects on poor children in communities where SFR resulted in the largest changes in school spending;
and (d) it had no effects on individuals from non-poor-childhood families. Because we can think of no such counter-example, and because we are careful to control for a variety of potentially confounding policies and effects, we are confident that these effects can be taken as causal.
b. The Importance of Using Exogenous Variation As mentioned previously, comparing outcomes of individuals exposed to different levels of school spending without accounting for changes in school spending that may be the result of other factors that also directly affect the outcomes of interest, could lead to bias. One of the benefits of our framework is that we only exploit plausibly exogenous variation in school spending that is driven by the reforms. To gauge the extent to which this matters, we also estimated naïve OLS regression for all our models.
For all outcomes and subsamples, the OLS estimates are orders of magnitudes smaller than the 2SLS/IV estimates and only one of the 15 OLS estimates is statistically significantly different from zero. Looking to poor children, where we find sizable effects in 2SLS models, the OLS estimates are all economically insignificant and not statistically significant from zero at the 10 percent level. The stark contrast between the OLS and the 2SLS estimates underscores the importance of relying on exogenous variation in school spending. Importantly, the contrast between the OLS and the 2SLS estimates in our data provides an explanation for why these estimates might differ from other influential studies in the literature (e.g., Coleman et al., 1966, Betts, 1995, Hanushek, 1996, and Grogger, 1996). We suspect some prior studies that lacked a compelling research design to isolate causal effects of spending may have produced modest estimated effects of school spending due to unresolved endogeneity biases.
c. Exploring the Mechanisms.
A limitation of the results on the long-term impacts of school spending is their reducedform nature. We cannot separately identify the pathways through which various types of K-12 education spending, and the composition of school expenditures, impacts subsequent adult attainments. We did, however, explore these issues using extensions of our main model specifications to examine the impacts of SFRs on instructional spending, school support services, physical capital and school building expenditures. To speak to these issues, we employ data from the CCD on the types of school spending (available for years 1992 through 2010) and student staff ratios (available for years 1986 through 2010). The earliest CCD data start in 1986 so that 41 we do not have detailed data for the same cohorts that are exposed to the early reforms in the PSID. However, an analysis of mechanisms for the more recent cohorts is instructive. To determine how each additional dollar associated with reforms was spent, we employ instrumental variables models similar to equation  where the main outcomes are capital expenditure, expenditure on instruction, and instruction on services. To gain an understanding of how these reforms affected student-staff ratios we employ the same instrumental variables models similar to equation , where the main outcomes are the student-to-teacher ratio, students per school,, students per counselor, and students per administrator. The endogenous regressor is the level of per-pupil spending and the excluded instrument is the number of years of exposure to reforms interacted with the district specific spending increase. Results are presented in Table 5.
SFRs led to increases in all categories of spending. When a district sees an increase in school spending of $1,000 due to reforms, spending on capital increases by $86, spending on instruction increases by $559, and spending on support services increases by $405 on average.
Relative to mean levels, these increases are roughly proportional to the allocation of funds on average – suggesting that schools simply increased spending in all categories with little effect on the allocation of funds across categories. The increases for instruction and support services (which includes expenditures to hire more teachers and/or increase teacher salary and also funds to hire more guidance counselors and social workers) are consistent with the large, positive effects for those from low-income families.
We also estimate effects on student-staff ratios. For these models the endogenous regressor is the natural log of school spending. Districts that experience a 20 percent increase in spending due to reforms see reductions in student-to-teacher ratios and school size. Both of these have been found to benefit students in general, with larger effects for children from disadvantaged backgrounds (e.g., Krueger and Whitmore 2001, Bloom and Unterman 2013). We also find that schools in these districts have fewer students per counselor and fewer students per administrator. These have also been found to improve student outcomes (e.g., Reback 2010, Carell and Carell 2006). While there may be other mechanisms through which increased school spending may improve student outcomes, results suggest that the positive effects may be driven, at least in part, by reductions in class size and having more adults per student in schools. Other
possible mechanisms include changes in peer composition and changes in teacher quality.27 Separately identifying and disentangling the mechanisms underlying the overall causal impact of spending is very difficult with available data and is left for future work.