H75 | Macro Paper Warehouse

Marginal Returns to Public Universities

Mon, 01 Jan 0001 00:00:00 +0000

This paper asks whether enrolling in an American public university generates positive net returns for marginal students — those who barely qualify for admission — and whether those returns justify public expenditures. The question is policy-relevant because marginal students have weak academic preparation, face high dropout risk, and the net returns to expanding admission margins are theoretically ambiguous.

The author assembles administrative records spanning all 35 public universities in Texas, covering the universe of Texas public high school graduates from 2004–2014 (approximately 2.7 million students). Texas public universities collectively enroll over 10 percent of all American public university students. The data link high school records (test scores, demographics, coursework, attendance, disciplinary infractions) to college application and admission records, postsecondary enrollment and degree completion records, financial aid packages, institutional expenditure data from IPEDS, and quarterly earnings records from the Texas Workforce Commission unemployment insurance system.

The identification strategy exploits hundreds of decentralized SAT/ACT score cutoffs in university admissions — varying across schools and application years — that generate sharp discontinuities in admission probability. A fuzzy regression discontinuity design compares applicants just above versus just below each cutoff. On average, crossing a cutoff raises the probability of admission by 27 percentage points and the probability of enrolling at the target university by 15 percentage points. Density tests and pre-college covariate balance validate the smoothness assumptions. The typical cutoff complier is more disadvantaged than the average college applicant but comparable to the average Texas high school graduate.

Roughly half of cutoff compliers would fall back to another, typically less selective, four-year institution if rejected; 43 percent would fall back to a two-year community college; and only about 6 percent would forgo higher education entirely. The pooled estimates therefore blend intensive-margin effects (more selective versus less selective four-year college) with extensive-margin effects (four-year college versus community college or no college).

Main causal findings for enrollment compliers: the typical marginally admitted student completes approximately one additional year of credits in the four-year sector and becomes 12 percentage points more likely to ever earn a bachelor’s degree from any institution. About half of the additional four-year credits are offset by 15 fewer credits in the two-year sector, and associate degree or certificate completion falls by 7 percentage points. All bachelor’s degree gains are in non-STEM fields; STEM degree completion shows no detectable increase. Compliers become about 3 percentage points more likely to hold a graduate degree by 10 years out.

On earnings, admitted compliers earn less than rejected counterparts in the first five years due to continued enrollment. Year six is the crossover point; by years 8–12, compliers earn a stable 8.6 percent earnings premium in log terms (8.2 percent in dollar ratio terms, representing a LATE of $3,339 against an untreated complier mean of $40,829), with earnings ranks rising approximately 4 percentiles from a base near the 50th percentile.

Marginally admitted students pay no additional net tuition on average: $4,600 in additional gross tuition is nearly fully offset by grant aid, though they take on $5,300 more in student loans. Society incurs approximately $10,000 in additional educational expenditures per complier. Internal rates of return are 26 percent for students, 16 percent for society, and 7 percent for the government budget. At a 3 percent discount rate, the lifetime net present value of enrolling the typical marginal applicant is approximately $80,000 — $70,000 accruing to the student and $10,000 to taxpayers.

Earnings gains are similar across institutions of varying selectivity, but significantly smaller for low-income compliers, who spend more time enrolled, complete fewer degrees, and major in less lucrative fields. A bounding method shows that extensive-margin compliers (those who would otherwise not attend any four-year college) experience larger effects than intensive-margin compliers.

Q: What is the core research question and why is credible evidence scarce? A: The paper asks whether enrolling marginal students in American public universities generates positive net returns — private, social, and fiscal — and what drives heterogeneity in those returns. Credible evidence is scarce because most existing work is correlational and fails to account for selection bias: individuals with more college education may have had pre-existing advantages, confounding college’s causal effect with systematic sorting into it. Even if average returns are positive, the policy-relevant question is whether the marginal student — who has weak preparation and high dropout risk — represents a good investment.

Q: What is the regression discontinuity design, and what does the first stage look like? A: The author infers hundreds of decentralized SAT/ACT score cutoffs across approximately 700 application cells (combinations of university, year, GPA quartile, and test type) by searching for the score value with the largest discontinuity in admission and enrollment within each cell. This procedure delivers a superconsistent estimator of each cell’s true cutoff. Pooled across all cells, crossing a cutoff raises the probability of admission by 27 percentage points and the probability of enrollment at the target university by a precisely estimated 15 percentage points. The density of applicants and a rich set of pre-college characteristics run smoothly through the cutoffs, supporting the exclusion restriction.

Q: Who are the cutoff compliers, and are they representative of any broader population? A: Compliers — applicants who enroll in the target university if and only if they barely cross its cutoff — comprise approximately 15 percent of marginal applicants. In observable characteristics, compliers are roughly representative of the broader population of marginal applicants at the cutoff. They are significantly more disadvantaged than the average public university applicant, but broadly comparable to the average Texas public high school graduate in terms of academic preparation and family income.

Q: What are the next-best alternatives for marginal applicants who are rejected? A: Approximately 47 percent of compliers would fall back to another Texas four-year college (mostly public), 43 percent to a two-year community college, and approximately 9 percent would not enroll in any Texas institution. National Student Clearinghouse data for the 2008–2014 cohorts confirm that only 4 percent of untreated compliers attend a college outside the THECB universe, meaning approximately 6 percent of all compliers truly forgo higher education altogether if rejected. The empirically relevant extensive margin is therefore between the four-year sector and the two-year sector, not between college and no college.

Q: How does cutoff crossing change the institutional characteristics a complier experiences? A: Compliers are propelled into substantially better-resourced environments: the average math test score of college peers rises by half a standard deviation; peers are 12 percentage points less likely to have been low-income; gross tuition rises by $2,400 (a 42 percent increase over the untreated complier mean of $5,700); educational spending per student rises by $3,200 (43 percent over the untreated mean); peers’ 10-year BA completion rate rises by 28 percentage points; and peer mean earnings 8–12 years after college entry are $6,700 higher.

Q: What are the educational attainment effects? A: Cutoff crossing causes compliers to complete approximately 28 additional credits at any four-year institution (roughly one full year of a four-year program) and increases the probability of ever earning a bachelor’s degree by 12 percentage points, raising the completion rate from approximately 40 percent to just above 50 percent. About 15 fewer two-year sector credits are offset against the four-year gains, and associate degree or certificate completion falls by 7 percentage points. All bachelor’s degree gains are in non-STEM fields; there is no detectable increase in STEM degrees. Graduate degree completion rises by approximately 3 percentage points by 10 years out.

Q: What is the earnings trajectory, and when does the premium materialize? A: Admitted compliers earn less than rejected counterparts in the first five years after application because they remain enrolled longer. Year six is the crossover point. By years 8–12, the earnings premium stabilizes at approximately 8.6 percent in log terms and 8.2 percent in dollar ratio terms (a LATE of $3,339 against an untreated complier mean of $40,829). Earnings rank rises by approximately 4 percentiles from a base near the 50th percentile. These results are robust across sandwich earnings, all-quarters-with-earnings, and zero-imputed specifications.

Q: What does the cost-benefit analysis show? A: Marginally admitted students pay no additional net tuition on average: $4,600 in additional gross tuition is nearly fully offset by additional grant aid. They do borrow $5,300 more in student loans, likely financing higher room, board, and consumption costs at four-year colleges. From society’s perspective, compliers generate approximately $10,000 in additional educational expenditures. Cumulative undiscounted earnings benefits surpass costs after 8 years for students, 11 years for society, and 19 years for taxpayers. At a 3 percent discount rate, the lifetime net present value is approximately $80,000 total — $70,000 accruing to the student and $10,000 to taxpayers — with internal rates of return of 26 percent for students, 16 percent for society, and 7 percent for the government budget.

Q: Does selectivity of the admitting institution predict larger earnings returns? A: No. Compliers at more selective institutions experience substantially larger increases in peer quality than those at less selective institutions, but they are also less likely to be on the extensive margin of four-year enrollment and experience smaller BA attainment gains. These factors roughly offset, producing no systematic difference in earnings gains across institutions of varying selectivity. More selective institutions also impose no additional cumulative cost on society, while compliers actually pay slightly less in additional net tuition at more selective schools.

Q: How does the commonly used measure of college value-added (mean peer earnings) compare to actual complier returns? A: Mean peer earnings overpredicts actual value-added for marginal students by a factor of two: compliers attend an institution with $6,700 higher average peer earnings as a result of admission but gain only $3,300 themselves. The measure also overpredicts the earnings return to selectivity by a factor of three: a 100-SAT-point increase in target school selectivity predicts $3,000 higher peer earnings but only a statistically insignificant $900 higher gain in the complier’s own earnings.

Q: How do earnings returns differ by family income? A: Compliers from low-income families experience significantly smaller earnings gains compared to higher-income compliers. The gap is not explained by differential changes in college quality induced by admission. Instead, low-income compliers gain fewer degrees despite spending more time in college and major in less lucrative fields, consistent with related findings in the literature on family income gaps in degree completion and major choice.

Q: How do earnings returns differ by gender and by race? A: Female and male compliers eventually earn similar log earnings and earnings rank gains, but women reach their gains more quickly — likely because men take longer to finish college. White and Asian compliers experience similar earnings gains and BA completion improvements as Black and Hispanic compliers, despite white and Asian students experiencing larger increases in college selectivity and spending per student as a result of admission.

Q: What is the method for separating intensive- and extensive-margin effects? A: The two complier types are not directly distinguishable in the data. The author first uses an endogenous but strong stratification variable — having at least one other Texas public university admission offer — to identify some mean potential outcomes for each type. He then imposes an empirically-informed rank assumption to bound the remaining unknown mean potential outcomes, delivering tightly informative upper and lower bounds on each margin’s effects without requiring full nonparametric identification. The results show that pooled effects are driven by larger returns for extensive-margin compliers who would not have attended any four-year college, with smaller contributions from intensive-margin compliers shifting between four-year institutions.

Q: How do this paper’s earnings estimates compare to prior studies, and what explains the differences? A: This paper’s 8 percent earnings gain is smaller than the 17–26 percent reported in prior studies (Zimmerman 2014: 22%; Kozakowski 2023: 26%; Smith, Goodman, and Hurwitz 2025: 17%; Bleemer 2024: 21%; Hoekstra 2009: 20%). The differences are likely explained by the much larger educational attainment and institutional quality gains induced by those studies’ natural experiments: in Zimmerman (2014), enrollment compliers gain roughly three additional years of four-year education versus one year in this paper; in Bleemer (2024), compliers experience roughly $30,000 more in institutional spending per student versus approximately $3,000 in this paper.

Q: What are the scope conditions for these results? A: The results pertain to marginal applicants to Texas public universities (excluding UT-Austin, which uses holistic admission with no detectable SAT/ACT cutoffs) from the 2004–2014 high school graduation cohorts. The identified effects are local average treatment effects for compliers — applicants who would enroll in the target university if and only if they barely crossed its admission cutoff — and do not represent effects for always-takers or infra-marginal students. Earnings are measured only for Texas-based workers covered by the state unemployment insurance system, which captures an estimated 90 percent of the civilian labor force.

Cutoff complier: An applicant who enrolls in their target university if and only if their SAT/ACT score barely exceeds that university’s admission cutoff. Compliers are the population whose behavior — and thus whose treatment effects — are identified by the fuzzy RD design. They comprise approximately 15 percent of marginal applicants and are more disadvantaged than the average public university applicant but broadly comparable to the average high school graduate.

Extensive versus intensive margin: The extensive margin refers to the contrast between attending any four-year college versus falling back to a two-year community college or no college. The intensive margin refers to the contrast between attending a more selective versus a less selective four-year institution. Approximately half of cutoff compliers are on each margin; the paper treats them as economically distinct parameters requiring separate identification.

Fuzzy regression discontinuity (RD) design: An identification strategy that uses the discontinuous jump in admission probability at a test score cutoff as an instrument for enrollment, recovering the LATE for compliers via the ratio of the reduced-form discontinuity in outcomes to the first-stage discontinuity in enrollment. “Fuzzy” refers to the fact that crossing the cutoff changes admission and enrollment probabilities with a discrete jump rather than with certainty.

Internal rate of return (IRR): The discount rate at which the net present value of an investment equals zero — here, the discount rate equating the discounted stream of earnings benefits to the discounted stream of costs. The paper estimates IRRs separately for students (26 percent), society (16 percent), and the government budget (7 percent), reflecting different cost and benefit definitions from each perspective.

Rank assumption (bounding method): An empirically-informed assumption about the ordering of mean potential outcomes across latent complier types (extensive vs. intensive margin) that, combined with partial identification from a strong endogenous stratification variable, yields tight upper and lower bounds on each margin’s causal effects without requiring full nonparametric identification.

Net tuition: Gross tuition charges minus grant aid. For the typical marginal complier, gross tuition rises by $4,600 but is nearly fully offset by additional grant aid, yielding approximately zero additional net tuition cost — meaning the private financial cost of attending a public university for marginal students is effectively zero on net, though they take on $5,300 more in student loans to finance room, board, and consumption.

Sandwich earnings measure: A procedure applied to quarterly state earnings data that retains only quarters with positive earnings sandwiched between other quarters with positive earnings, discarding high-variance transition quarters between employment spells. Annualized by multiplying the quarterly average by four; used to reduce noise from entry and exit transitions in administrative earnings records.

What Works and for Whom? Effectiveness and Efficiency of School Capital Investments Across the U.S.

Mon, 01 Jan 0001 00:00:00 +0000

What Works and for Whom? Effectiveness and Efficiency of School Capital Investments Across the U.S.

Research Question

This paper investigates which types of school facility investments benefit students (as measured by test scores) and are valued by homeowners (as measured by house prices), and for which student populations these investments are most effective. Prior state-level studies had reached conflicting conclusions about the returns to school capital spending, and no nationwide evidence had distinguished impacts across spending categories or student backgrounds.

Data and Methodology

The authors assemble a novel panel dataset covering approximately 14,000 school bond referenda in 29 U.S. states and 10,146 districts enrolling 71% of all U.S. students, for the period 1990–2017. The dataset combines: (1) ballot-level bond election records including vote shares, proposed amounts, and ballot text; (2) district-level test scores from the Stanford Education Data Archive (SEDA) extended backward to 2003 for all states and as early as 1995 for some, normalized to a national scale via NAEP; (3) a Census-tract-level house price index (Contat and Larson, 2022) aggregated to school districts; and (4) NCES district finance and demographic data.

Bond ballot texts are classified into eight spending categories using text-analysis: classroom construction/renovation; HVAC; other infrastructure (plumbing, roofs, furnaces); safety and health (pollutant removal, building safety); STEM equipment and labs; athletic facilities; land purchases; and transportation vehicles.

The identification strategy exploits quasi-random variation from close bond elections, building on the dynamic regression discontinuity (DRD) framework of Cellini et al. (2010). A key methodological contribution is a stacked DRD design that addresses heterogeneous treatment effects correlated with timing: each treatment cohort (districts that narrowly authorize a bond in year c) is matched against “clean controls” — districts that also proposed a bond in the same cohort but narrowly failed to authorize it and did not authorize any bond in the following ten years. Cohorts are stacked, and a dynamic RD model is estimated controlling for cohort fixed effects and a district’s bond proposal history.

Main Findings with Quantitative Magnitudes

Average effects. Bond authorization raises capital spending by approximately $1,650 per pupil cumulatively over five years. Test scores increase gradually, reaching 0.079 standard deviations (sd) higher five to eight years after authorization, and 0.073 sd higher nine to twelve years after. 2SLS estimates, amortizing spending over a 30-year project life at a 9% depreciation rate, imply that a $1,000 increase in the flow value of capital spending raises test scores by 0.048 sd. House prices rise by approximately 9% eight to nine years after authorization. When house price effects are estimated against only locally-financed capital spending (not state aid), the 2SLS estimate is 0.8% per $1,000 — roughly consistent with efficiency — suggesting that the larger reduced-form house price response is driven primarily by state aid that supplements local funds rather than by an inefficiently low ex ante spending level.

Heterogeneity by spending category. Category-specific estimates reveal that only certain project types raise test scores: HVAC (+0.20 sd, largest effect), safety and health (+0.15 sd), other infrastructure/plumbing/roofs (+0.15 sd), STEM equipment (+0.15 sd implied), and classroom space (+0.10 sd), all measured three to six years post-election. By contrast, bonds for athletic facilities, land purchases, and transportation produce no detectable effects on test scores. The pattern for house prices is the inverse: athletic facilities generate a 17% house price increase; classroom space generates 14%; STEM generates 11% — while HVAC and safety/health bonds produce no significant effect on house prices. The correlation between category-level test score and house price estimates is −0.07, indicating these are largely orthogonal outcomes.

Heterogeneity by student socioeconomic status. Effects are concentrated in districts serving socioeconomically disadvantaged students (top tercile of the share of students eligible for free or reduced-price meals, denoted low-SES). In low-SES districts, bond authorization raises test scores by 0.13 sd after seven years and house prices by 15%; in high-SES districts, neither outcome shows a significant effect. 2SLS estimates confirm that a $1,000 increase in cumulative spending raises test scores by 0.08 sd in low-SES districts but produces no detectable change in high-SES districts. The SES gradient persists after conditioning on spending amounts, spending categories, and baseline capital stock, indicating that students in disadvantaged districts have higher marginal returns to capital improvements independent of these channels. High-minority districts (top tercile of Black and Hispanic share) similarly see a 0.12 sd test score gain and 15% house price gain after seven years, versus 0.04 sd and 3% in low-minority districts.

Role of baseline capital stock. Among districts with below-median capital stock, test score effects are 0.20 sd in low-SES districts seven years post-election. Even among above-median-stock districts, low-SES districts see house price effects exceeding 10% while high-SES districts see no effect. Differences by SES persist after conditioning on capital stock.

Policy simulation. Closing the spending gap between high- and low-SES districts (approximately $1,000 over 10 years) without changing the composition of spending would raise low-SES test scores by roughly 0.08 sd, closing about 8% of the roughly 1 sd achievement gap. Targeting that same additional spending toward HVAC and safety/health (the highest-impact categories) would generate test score increases approximately three times as large, potentially closing up to 25% of the observed achievement gap.

Reconciling prior literature. Replicating state-level estimates, the authors show that Ohio’s positive effects are explained by a high share of bonds in low-SES districts funding infrastructure, while Texas’s near-zero effects reflect a high share of bonds in higher-SES districts funding classrooms and athletic facilities.

In depth

Q1. What is the first-stage effect of bond authorization on capital spending, and does it contaminate other spending categories?

A1: Bond authorization raises per-pupil capital spending by approximately $700 per year at two years post-election and $590 at three years, with cumulative spending $1,650 higher over five years in treated districts relative to districts that narrowly failed to authorize a bond. Bond revenues are legally restricted to capital uses, and the paper confirms that non-capital (current) spending and instructional spending are not affected following authorization. This establishes a clean first stage: bond authorization raises only capital outlays.

A2: The original CFR estimator assumes treatment effects are uncorrelated with the timing of treatment — an assumption potentially violated when, for example, bonds financing HVAC (high-impact) versus athletic facilities (amenity-focused) have different propensities to be proposed at different points in time. The stacked DRD design avoids “forbidden comparisons” by comparing each treatment cohort only against clean controls that propose but fail to authorize a bond in the same year and do not authorize any bond in the subsequent ten years. This ensures consistency even when treatment effects are heterogeneous across cohorts and correlated with timing.

Q3. How do the authors validate the quasi-random assignment assumption of the regression discontinuity design?

A3: Three tests are performed. First, a McCrary (2008) density test on the vote margin distribution shows no discontinuity at the cutoff in the pooled or stacked data (p-values of 0.59 and 0.24, respectively), though discontinuities are found in Arkansas, Missouri, and Oklahoma — those three states are excluded. Second, pre-election district covariates (income, education, SES shares, enrollment, revenues, expenditures) are smooth around the cutoff in both datasets. Third, pre-election trends in test scores and house prices are flat and parallel between marginally approved and marginally rejected districts.

Q4. How are the eight spending categories constructed, and how many bonds are successfully classified?

A4: Categories are drawn from the SchoolBondFinder.com classification produced by The Amos Group, then refined by splitting capital improvements into HVAC versus other infrastructure, splitting construction/renovation into classroom versus athletic facility projects, and adding land purchases as a separate category. Keyword-based text analysis of ballot language successfully assigns 75% of the approximately 14,000 bonds to at least one of the eight categories. More than two-thirds of classified bonds receive multiple category designations, with a mean of 2.9 categories per proposed bond and 3.2 per authorized bond.

Q5. Why do HVAC bonds raise test scores but not house prices, while athletic facility bonds raise house prices but not test scores?

A5: The authors interpret this divergence as reflecting what different types of improvements offer to different stakeholders. HVAC improvements reduce excessive heat and air pollution exposure in classrooms, directly improving students’ learning experiences — consistent with Park et al. (2020) on heat and Gilraine and Zheng (2022) on air pollution. These improvements are not visibly salient to homeowners without school-age children and carry no amenity value for the broader community. Athletic facilities, by contrast, are highly visible and provide a community amenity valued in the housing market regardless of their impact on academic instruction. The near-zero correlation (−0.07) between category-level test score and house price estimates confirms that the two outcomes respond to largely distinct features of capital investments.

Q6. What are the three candidate explanations for the larger effects of bond authorization in low-SES districts, and which explanations survive empirical scrutiny?

A6: The three candidates are: (1) larger spending increases after authorization in low-SES districts; (2) a different composition of spending categories (more toward high-impact HVAC and safety); and (3) higher marginal returns per dollar for disadvantaged students, holding spending size and composition fixed. The data confirm all three operate, but the third is the residual: 2SLS estimates show a $1,000 increase raises test scores by 0.08 sd in low-SES districts versus a statistically zero effect in high-SES districts, and within-category estimates show HVAC bonds raise scores by 0.27 sd in low-SES districts but have no detectable effect in high-SES districts. Differences by SES also persist after conditioning on the estimated baseline capital stock, though low capital stock accounts for part of the gap.

Q7. How does the role of state aid alter the interpretation of the house price effect for spending efficiency?

A7: A 9% house price increase after bond authorization, if taken at face value under Brueckner’s (1979) efficiency test, would suggest the ex ante level of school capital spending was inefficiently low. However, state grants that partly match local bond revenues raise actual spending without raising local property taxes proportionally. When the 2SLS house price effect is estimated against only locally financed capital spending (using proposed bond size as the relevant measure), the implied house price increase is just 0.8% per $1,000 — consistent with rough efficiency on average across the full sample. The authors conclude that the large reduced-form house price response is driven primarily by the capitalization of state aid, not by an undersupply of capital investments at the aggregate level.

Q8. Does household sorting account for the observed test score and house price gains following bond authorization?

A8: Bond authorization produces small but detectable compositional changes: the share of high-SES students is approximately 3 percentage points higher seven years after an election (a roughly 4% increase relative to an average share of 0.73), while enrollment and the share of white students are largely unaffected. However, controlling for district-by-year shares of each sociodemographic group only slightly attenuates the test score and house price estimates, indicating that sorting accounts for a small share of the observed gains.

Q9. Are the findings robust to alternative research designs?

A9: The results are robust to five alternative estimation approaches: (1) the original one-step TOT estimator of Cellini et al. (2010); (2) a version of the stacked DRD where clean controls are districts that do not approve any bonds in the full [c−5, c+10] window; (3) a version that matches treated and control districts in each cohort based on bond history; (4) a version not controlling for future bond history; and (5) the extended two-way fixed effects (ETWFE) estimator of Wooldridge (2021). Results are also robust to linear polynomials with different slopes and quadratic polynomials of the vote margin.

Q10. How does the capital stock measure illuminate mechanism, and what are its limitations?

A10: The authors construct a district-level capital stock as the 30-year depreciated sum of capital spending from Census of Governments data (1967–2017) at a 5% depreciation rate. This stock is negatively correlated with the share of low-SES students, confirming that more disadvantaged students attend schools in worse structural condition. Conditioning on this proxy, the SES gradient in bond impacts is reduced but remains. Among districts with below-median capital stock, low-SES districts see test score gains of 0.20 sd after seven years, while among above-median-stock districts the gap narrows to approximately 0.10 vs. 0.05 sd. A key limitation is that detailed school-condition data are unavailable nationally, so the capital stock is a proxy only.

Q11. What is the quantitative policy implication of the targeting exercise?

A11: On average, low-SES districts receive about $97 per pupil per year less in capital spending than high-SES districts, so closing this gap over ten years implies approximately $970 in additional cumulative spending. Without changing spending composition, this would raise test scores by roughly 0.08 sd in low-SES districts, closing about 8% of the approximately 1 sd achievement gap between high- and low-SES districts. Redirecting that same additional spending toward the highest-impact categories (HVAC and safety/health) would generate test score gains roughly three times larger, potentially closing up to 25% of the observed achievement gap.

Q12. How do the cross-state differences documented in prior literature map onto the paper’s heterogeneity findings?

A12: The authors replicate earlier state-level estimates and show that Ohio’s relatively large positive effects — found by Conlin and Thompson (2017) — are explained by a high concentration of bonds in low-SES districts funding infrastructure, while Texas’s near-zero effects — found by Martorell et al. (2016) — reflect a high share of bonds in higher-SES districts funding classrooms and athletic facilities. Wisconsin and Michigan, which showed null effects in earlier studies, similarly have bond compositions and student demographics that predict small impacts under the paper’s heterogeneity framework.

Key Concepts

Stacked Dynamic Regression Discontinuity (Stacked DRD). The paper’s primary estimation strategy, which combines the dynamic RD framework of Cellini et al. (2010) with a stacked-cohort design adapted from the staggered difference-in-differences literature. For each treatment cohort (year in which a bond barely passes), “clean controls” are defined as districts that also proposed a bond in the same year but narrowly failed to authorize it and did not authorize any subsequent bond within ten years. Cohort-specific datasets are stacked and estimated jointly with cohort fixed effects, ensuring that estimates are robust to treatment effect heterogeneity correlated with timing.

Clean Controls. Districts used as the counterfactual for treated districts in a given cohort: those that propose a bond in the same year as the treated cohort, barely fail to authorize it, and remain untreated for ten subsequent years. Their “clean” status is quasi-random because their future non-authorization results from narrow electoral loss rather than any endogenous district choice.

Bond Spending Categories. Eight mutually-non-exclusive classifications of bond spending derived from ballot text using keyword analysis: classroom space; HVAC; other infrastructure (plumbing, roofs, furnaces); safety and health (pollutant removal, compliance upgrades); STEM equipment and labs; athletic facilities; land purchases; and transportation. These categories are defined in the paper not by administrative accounting codes but by the stated intended use of funds in ballot language.

Treatment-on-the-Treated (TOT) Estimator. The CFR estimator that captures the effect of bond authorization against the counterfactual of never authorizing a bond in the foreseeable future, achieved by including leads and lags of a district’s bond proposal history as controls. This addresses the problem that multiple elections over time make simple treated-vs-control comparisons confounded by past and future bond activity.

Capital Stock (District-Level Proxy). A measure of each district’s accumulated school facility capital at a given point in time, constructed as the depreciated 30-year running sum of capital expenditures from the Census of Governments, using a 5% annual depreciation rate. Used as a proxy for facility conditions in the absence of nationally available building-quality data, and confirmed to be negatively correlated with district share of low-SES students.

Brueckner Efficiency Test. An application of the theoretical framework linking public good provision levels to house price responses. If a spending increase raises house prices, the initial spending level was below the efficient level; if it lowers house prices, spending was too high. In this paper, the test is refined to use only locally-financed capital spending as the explanatory variable, to strip out the capitalization of state aid and isolate the efficiency assessment for locally-determined spending.

Socio-Economic Status (SES) Terciles. Districts are ranked by the share of students eligible for free or reduced-price school meals as of 1995. “Low-SES districts” refers to those in the top tercile of this share (most disadvantaged); “high-SES districts” refers to those in the bottom tercile (least disadvantaged). Effects are estimated separately for these subsamples throughout.

H75 | Macro Paper Warehouse

Marginal Returns to Public Universities

What Works and for Whom? Effectiveness and Efficiency of School Capital Investments Across the U.S.

What Works and for Whom? Effectiveness and Efficiency of School Capital Investments Across the U.S.

Research Question

Data and Methodology

Main Findings with Quantitative Magnitudes

In depth

Q1. What is the first-stage effect of bond authorization on capital spending, and does it contaminate other spending categories?

Q2. Why does the standard DRD estimator of Cellini et al. (2010) require refinement, and what problem does the stacked DRD design solve?

Q3. How do the authors validate the quasi-random assignment assumption of the regression discontinuity design?

Q4. How are the eight spending categories constructed, and how many bonds are successfully classified?

Q5. Why do HVAC bonds raise test scores but not house prices, while athletic facility bonds raise house prices but not test scores?

Q6. What are the three candidate explanations for the larger effects of bond authorization in low-SES districts, and which explanations survive empirical scrutiny?

Q7. How does the role of state aid alter the interpretation of the house price effect for spending efficiency?

Q8. Does household sorting account for the observed test score and house price gains following bond authorization?

Q9. Are the findings robust to alternative research designs?

Q10. How does the capital stock measure illuminate mechanism, and what are its limitations?

Q11. What is the quantitative policy implication of the targeting exercise?

Q12. How do the cross-state differences documented in prior literature map onto the paper’s heterogeneity findings?

Key Concepts