R53 | Macro Paper Warehouse

The Long-Run Impacts of Public Industrial Investment on Local Development and Economic Mobility: Evidence from World War II

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

Overview

Research Question. Does government-led construction of large manufacturing plants in previously under-industrialized regions generate long-run improvements in regional economic development and in the lifetime earnings of the incumbent residents who were already living there at the outset? And, if so, through what mechanism — developmental improvements during childhood or expanded adult labor market opportunities?

Setting and Identification. The paper exploits the United States industrial mobilization for World War II, specifically the construction of 90 large, government-financed, newly-built manufacturing plants (each costing $10 million or more in contemporary dollars, approximately $150 million in 2020 dollars) in dispersed locations outside the major prewar manufacturing hubs. Strategic and security considerations — not economic optimization — drove the military to insist these plants be sited away from congested industrial centers. Because private firms were unwilling to finance construction in isolated locations with uncertain postwar value, the government built them directly as government-owned, contractor-operated (GOCO) facilities through the Defense Plant Corporation. Site selection within the set of sufficiently populated regions was governed by idiosyncratic, short-run factors — the immediate availability of suitable parcels, informal connections to procurement officers, and expedience — rather than systematic economic characteristics of the receiving counties. The paper documents no systematic association between publicly-funded wartime plant construction and prewar county-level economic or demographic characteristics conditional on population size, and finds parallel prewar trends and balanced outcome levels across treatment and comparison counties in all decades leading up to WWII. A placebo test using 1910-to-1940 intergenerational mobility in matched Census records confirms no differential prewar upward mobility in treatment counties.

The comparison group consists of 1,400 counties outside the 100 largest prewar manufacturing counties that did not receive large public plants. Treatment assignment for individuals is based on birth county, not adult county of residence, enabling the paper to track outcomes regardless of where individuals ultimately live.

Data. The analysis draws on the 1945 War Production Board data book for plant-level investment; county-level panels from Decennial and Economic Censuses spanning 1900–2000; the SSA NUMIDENT file (birth county and date); IRS Form 1040 individual income tax returns in 1969, 1974, 1979, and 1984 (covering wage earnings and adjusted gross income); the full-count 1940 Census (parent earnings, demographics); the 2000 Census long form (educational attainment); and W-2 earnings histories from the SSA Detailed Earnings Record matched to a CPS-linked subsample, with employer information linked to the Business Register.

Regional Effects. By 1970, counties receiving large public wartime plants had approximately 30 percent higher manufacturing employment, 20 percent larger populations, and 7–8 percent higher median family income than comparison counties. Manufacturing employment as a share of total employment rose and remained elevated through the 1970s before converging toward parity with the comparison group by 1990. Treated counties were permanently larger — with population stabilizing at a new, persistently higher equilibrium roughly 20 percent above comparison counties by end of century — even after the manufacturing employment share converged, consistent with path dependence and multiple equilibria. Average production worker pay in manufacturing rose by approximately 10 percent, closely tracking value-added per worker, while average retail wages rose by only one-third as much and were not statistically significant in most years. In the 40 years after the war, treated counties saw median family earnings increase by 5–10 percent, concentrated in higher average wages and employment shares in manufacturing and semi-skilled blue-collar occupations, with limited effects on non-manufacturing, white-collar occupations, or female individual income.

Individual Earnings Effects. Men born in treatment counties in the 18 years before the war (birth cohorts 1922–1940) earned approximately $1,200–$1,300 more per year (2020 dollars) in average wage earnings reported on 1040 returns in 1969, 1974, 1979, and 1984 — an increase of 2.5–3 percent and roughly a one-percentile rise in the national earnings distribution. Effects were largest for children of parents at the bottom of the 1939 earnings distribution: children of the lowest-income parents saw adult wage earnings rise by approximately $1,800–$2,000 per year (3–4 percent), with effects declining linearly by parent rank and effectively vanishing for children of the highest-earning parents. Black men experienced larger average earnings effects (4–6 percent, or $1,500–$2,500 in 2020 dollars) than White men (2–3 percent, or $1,000–$1,500), with the racial earnings gap estimated to have narrowed by about 2 percent in the treatment group. When examining Form 1040 returns (tax-unit level), effects are comparable for men and women, but W-2 individual earnings data from the SSA-CPS subsample show no positive effect on women’s own earnings — the 1040 effects for women are entirely driven by their husbands’ higher earnings.

Mechanism. The balance of evidence points to access to higher-wage jobs in adulthood as the primary channel, rather than developmental human capital improvements accumulated during childhood. War plants modestly increased male educational attainment — children from the lowest-earning families completed approximately one-quarter of a year more schooling and were 3 percentage points more likely to graduate high school — but education effects are too small to account for the full earnings increase. Critically, there is no gradient in earnings effects by birth cohort: children who were younger at the start of the war and therefore had longer childhood exposure to improved regions did not benefit more, contradicting a childhood exposure-effect mechanism as in Chetty and Hendren (2018b). Adult earnings effects are entirely accounted for by adult location: conditioning on 1979 county of residence eliminates the treatment effect. Stayers in treatment counties show large earnings differences relative to stayers in comparison counties, while movers show none. Men born in treatment counties are also directly documented to have worked in industries with higher wage premiums as adults, with coarse industry classification alone accounting for approximately one-third of the estimated log wage increase.

Policy Scope Conditions. The paper argues these effects are specific to the WWII postwar institutional context — high global demand for U.S. manufactured goods, limited international competition, labor-intensive production techniques, and strong union bargaining power — conditions that no longer hold. Reexamination of “million-dollar plant” openings in the 1980s and 1990s shows manufacturing employment expanded but average manufacturing wages did not increase, suggesting contemporary plant openings do not generate the same high-wage opportunities. The association between manufacturing employment density and upward mobility visible in 1950 has entirely vanished by the end of the twentieth century.

In depth

Q1. What exactly defines the treatment group, and why were these plants built by the government rather than private firms?

A: The treatment group consists of 90 counties outside the 100 largest prewar manufacturing regions that received at least one new, fully publicly-financed manufacturing plant costing $10 million or more (approximately $150 million in 2020 dollars) under the WWII industrial mobilization. Private firms refused to finance construction in dispersed, isolated locations with highly uncertain postwar value; the Air Force historians recorded that “industrialists’ reluctance to invest in dispersed plant facilities was at odds with the government’s hope that private capital could finance new inland construction.” The government built and owned these facilities as GOCO plants, operated by private firms under contract. The 353 plants meeting the cost threshold (including both large and smaller public plants) account for 70 percent of all spending on new plants during the war.

Q2. How do the authors establish that plant siting was quasi-random conditional on population size?

A: Identification rests on three forms of evidence. First, historical documents show procurement decisions were driven by idiosyncratic factors — availability of a suitable parcel, informal connections to procurement officers, short-run expedience — rather than systematic economic characteristics. Members of Congress had little ability to influence siting, and Rhode et al. (2018) find little evidence that federal politics drove the geographic distribution of wartime spending. Second, balance tests (estimating prewar county characteristics as outcomes in Equation 1) show no significant differences between treatment and comparison counties in earnings levels, demographics, manufacturing development, or industrial composition after conditioning on 1940 population, with a joint p-value of 0.30 (0.36 when also conditioning on geography and infrastructure). Third, a placebo test using children in the 1910 Census matched to the 1940 Census finds no differential economic outcomes or upward mobility rates in counties that would eventually receive treatment plants, conditional on basic region size.

Q3. What are the county-level effects on the structure of the labor market in the medium run?

A: By the 1960s–1970s, treated counties had higher predicted union coverage rates and a greater share of men in semi-skilled production occupations, driven primarily by movement away from farm work and supplemented by higher male labor force participation. Average wages in craftsperson and operator occupations rose by 8 percent in treated counties — more than double the increase in wages for high-skill professional and managerial occupations. Treated counties had 8 percent higher median male individual incomes by 1979. Effects on female median individual income were minimal, and there were no effects on female labor force participation rates.

Q4. What is the estimated magnitude of the individual earnings effects, and how do they vary by parent income?

A: Men born in treatment counties averaged $1,200–$1,300 more per year in real wage earnings (2020 dollars) on 1040 tax returns across the four observation years 1969, 1974, 1979, and 1984, a 2.5–3 percent increase equivalent to roughly one percentile in the national earnings distribution. Heterogeneity by parent rank is pronounced and monotone: children of parents at the very bottom of the 1939 earnings distribution gained approximately $2,000 per year (about 4 percent), while children of the highest-earning parents experienced no significant effect. When county weighting is equalized to eliminate the differential representation of rural (lower-income) counties, effects are roughly constant across the bottom six deciles of the parent earnings distribution and then drop steeply at the top, showing that the earnings gradient was not simply an artifact of plant openings in poorer, smaller counties.

Q5. How did effects differ by race?

A: Wartime plant construction increased annual adult earnings of Black men by 4–6 percent ($1,500–$2,500 in 2020 dollars) and of White men by 2–3 percent ($1,000–$1,500 in 2020 dollars). The racial earnings gap in the treatment group is estimated to have narrowed by about 2 percent. However, the pattern of heterogeneity by parent income differs by race: for White men, effects are largest for children of below-median parents and effectively zero for children of above-median parents. For Black men, the largest effects — 7–10 percent ($4,000–$5,000 in 2020 dollars) — accrue to children of parents with earnings above the pooled-race national median, while effects for lower-income Black families range from 3–6.5 percent, suggesting that Black workers from higher-income backgrounds particularly benefited from wartime anti-discrimination policies and the opening of previously restricted manufacturing occupations.

Q6. Why do the 1040 returns show comparable effects for men and women, while W-2 data show no effect on women’s individual earnings?

A: Form 1040 returns are filed at the tax-unit level — for married couples, they report the combined wages of both spouses. Because more than 80 percent of women in the sample are married, an increase in a husband’s earnings raises the joint 1040 figure for both spouses. The SSA-CPS subsample with individual W-2 records shows that the entire effect on men’s Form 1040 wages directly reflects increases in their own W-2 earnings, while women’s own W-2 earnings show no positive treatment effect. This finding is consistent with county-level evidence of no impact on female individual income or female labor force participation, and with Rose (2018) finding that women were almost universally excluded from manufacturing jobs after the war’s conclusion despite high wartime female manufacturing employment.

Q7. What evidence tests the developmental-effects mechanism?

A: Three tests argue against childhood developmental effects as the primary driver. First, educational attainment effects — while statistically significant for children of the lowest-income parents (approximately one-quarter of a year more schooling, 3 percentage points more likely to graduate high school) — are too small to account for the earnings increase: a Mincer-equation calculation shows that the education effects can explain less than one-half of the estimated effect on 1979 wages. Second, there is no gradient in earnings effects by birth cohort — children younger at the war’s start, who had longer post-treatment childhood exposure, did not benefit more, in direct contrast to the Chetty-Hendren childhood-exposure framework. Third, postwar in-migrants into treatment counties were not drawn from better-educated or higher-income families and did not themselves have more education than in-migrants into comparison regions, ruling out peer effects from selective in-migration.

Q8. What evidence directly implicates adult labor market access as the operative mechanism?

A: Four pieces of evidence point to contemporaneous adult labor market access. First, individuals born in treatment counties lived as adults in counties with 3–4 percent higher median male earnings and higher wages in semi-skilled blue-collar occupations but not in highly-skilled professional occupations — a pattern quantitatively consistent with the individual earnings effects. Second, the entire earnings effect is concentrated among those who remain in their birth counties: stayers in treatment counties show earnings differences of similar magnitude to county-level manufacturing wage effects, while movers show no difference compared to movers from comparison counties. Third, conditioning on 1979 county of residence eliminates the earnings effect entirely (1979 location fixed effects specification). Fourth, using W-2 data matched to the Business Register in the SSA-CPS sample, men born in treatment counties are directly shown to work in industries with higher wage premiums, with coarse industry classification alone accounting for approximately one-third of the log wage increase.

Q9. Is the persistence of regional effects driven by continued Cold War military spending at the plants?

A: No. The paper separates ordnance and ammunition plants — which predominantly became GOCO facilities or Air Force Bases after WWII and received disproportionately more Vietnam War-era defense spending — from general manufacturing plants, which overwhelmingly transitioned to privatized civilian production. Both types of plants show similarly persistent effects on manufacturing employment and comparable impacts on the long-run earnings of local children. Moreover, general manufacturing plants — which did not generate increased postwar military spending — had large permanent effects on overall population growth, while ordnance plants had smaller population effects. The persistence therefore does not appear to reflect continued federal expenditure.

Q10. What mechanism explains the permanent population effect even after manufacturing employment shares converge?

A: The authors interpret the permanent population differential — treated counties remain roughly 20 percent larger than comparison counties even at the end of the 20th century, after manufacturing employment shares converge — as evidence of path dependence and multiple equilibria. Once a region reaches a new, larger equilibrium, self-sustaining forces (expanded non-tradable employment, public infrastructure investment) maintain it. Treatment counties are more likely to have been connected to the interstate highway system in subsequent decades and show positive effects on local government capital outlays for utilities. The medium-term persistence is attributed partly to the sunk costs of site establishment (surveying, local approvals, infrastructure connections), which make reinvestment at existing sites more attractive than greenfield construction elsewhere.

Q11. Do smaller plant openings generate comparable effects?

A: No. Counties receiving smaller publicly-financed plants costing between $1 and $10 million show no detectable effects on manufacturing employment, population, median family income, or individual adult earnings comparable to those from the large plants. The authors cannot rule out the presence of small effects, but the null results for smaller plants — combined with evidence that the largest effects are in counties with the highest investment intensity per 1940 resident — are consistent with threshold effects (“big push”) in regional development, though the wide confidence intervals do not allow the authors to conclusively distinguish threshold effects from a linear-in-investment model.

Q12. What do modern “million-dollar plant” openings reveal about the contemporary relevance of these findings?

A: Reexamining plant openings from Greenstone et al. (2010) using an event-study design, the authors find that 1980s–1990s million-dollar plant openings expanded manufacturing employment (consistent with Greenstone et al.) but had no impact on average manufacturing wages — in sharp contrast to the WWII findings. Slattery and Zidar (2020) similarly find no impacts on county-level incomes for plant openings since 2000. The correlation between manufacturing employment density and upward mobility rates visible in 1950 had entirely vanished by the end of the 20th century. The authors attribute the divergent results to the changed institutional environment: contemporary production is highly automated, relies on interchangeable labor from staffing agencies, faces intense international competition, and is conducted under much weaker collective bargaining institutions.

Q13. What is the paper’s assessment of aggregate welfare implications?

A: The paper is explicit that its local estimates do not allow clean conclusions about aggregate effects. Publicly-financed plant construction in peripheral locations may have crowded out private investment that would otherwise have occurred in major manufacturing hubs. If so, the documented regional gains represent geographic reallocation of manufacturing activity rather than a net increase in the aggregate plant stock. Aggregate gains from reallocation would require that the benefits in the selected dispersed locations exceeded what would have occurred in the counterfactual locations — a plausible conjecture given the paper’s evidence that effects are larger in counties with lower prewar manufacturing employment shares and lower initial market access, but one the authors cannot demonstrate decisively.

Key Concepts

Government-Owned, Contractor-Operated (GOCO) Plants: Manufacturing facilities built and owned by a U.S. government agency (typically the Defense Plant Corporation) during WWII but built and operated by private firms under cost-plus contracts. GOCO status meant the government bore full construction risk and that post-war disposition (sale to private buyers at a fraction of construction cost, or continued GOCO operation for ordnance production) was determined by public agencies, not by the constructing firm’s investment calculus.

Place-Based Predistribution: The paper’s term for the mechanism by which wartime plant construction raised the incomes of existing residents — not through ex-post redistribution of income via taxes and transfers, but by expanding the set of high-wage employment opportunities available to incumbent workers in the region, thereby changing the pre-tax, pre-transfer wage structure facing those workers.

Adult Labor Market Access (vs. Childhood Developmental Exposure): A distinction the paper draws in explaining why children born in treated counties had higher adult earnings. The “developmental exposure” mechanism (as in Chetty and Hendren 2018b) implies benefits scale with the amount of time spent in an improved childhood environment. The “adult labor market access” mechanism means children benefit irrespective of years of childhood exposure because they can access improved local labor market conditions when they reach working age as adults — what the paper operationalizes through the finding that earnings effects are entirely accounted for by 1979 county of residence and are concentrated among individuals who remain in their birth counties.

Upward Mobility (Absolute and Relative): Following Chetty et al. (2014), the paper uses both concepts: absolute upward mobility means children from low-income backgrounds have higher lifetime earnings than comparable children in counterfactual regions; relative upward mobility means their outcomes converge toward those of children from affluent backgrounds. The paper documents both: large earnings effects for the lowest parent-income deciles, declining linearly to zero for the top deciles.

Conditional Independence (Plant Siting as Quasi-Random): The paper’s identification assumption — that among counties with observably similar population sizes and basic geographic/infrastructure characteristics, the specific choice of plant siting locations was driven by idiosyncratic, short-run factors uncorrelated with potential postwar outcomes. This is a level-balance assumption (not merely a parallel-trends assumption), required because individual outcomes are only observed in the post-period.

Industry Wage Premium: The paper uses Krueger and Summers (1988) estimates of inter-industry wage differentials (the portion of a sector’s average wage unexplained by worker characteristics) to classify adult employers of treated individuals. Finding that men born in treatment counties work at employers in higher-premium industries — with industry category alone explaining approximately one-third of the log wage increase — provides direct evidence of the adult labor market access mechanism operating through industry sorting.

Path Dependence / Multiple Equilibria in Regional Development: The paper documents that treated counties remain permanently larger in population than comparison counties even after manufacturing employment shares converge and the original plants begin to close. This self-sustaining population differential, inconsistent with a unique spatial equilibrium, is interpreted as evidence that the temporary wartime shock shifted treated regions into a permanently higher equilibrium, sustained by subsequent infrastructure investment and non-tradable sector expansion proportional to the larger population base.

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.

R53 | Macro Paper Warehouse

The Long-Run Impacts of Public Industrial Investment on Local Development and Economic Mobility: Evidence from World War II

Overview

In depth

Q1. What exactly defines the treatment group, and why were these plants built by the government rather than private firms?

Q2. How do the authors establish that plant siting was quasi-random conditional on population size?

Q3. What are the county-level effects on the structure of the labor market in the medium run?

Q4. What is the estimated magnitude of the individual earnings effects, and how do they vary by parent income?

Q5. How did effects differ by race?

Q6. Why do the 1040 returns show comparable effects for men and women, while W-2 data show no effect on women’s individual earnings?

Q7. What evidence tests the developmental-effects mechanism?

Q8. What evidence directly implicates adult labor market access as the operative mechanism?

Q9. Is the persistence of regional effects driven by continued Cold War military spending at the plants?

Q10. What mechanism explains the permanent population effect even after manufacturing employment shares converge?

Q11. Do smaller plant openings generate comparable effects?

Q12. What do modern “million-dollar plant” openings reveal about the contemporary relevance of these findings?

Q13. What is the paper’s assessment of aggregate welfare implications?

Key Concepts

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