J62 | Macro Paper Warehouse

Diversifying Society's Leaders? Determinants and Causal Effects of Admission

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

This paper studies why children from high-income families are more likely to attend Ivy-Plus colleges (Ivy League, Stanford, MIT, Duke, Chicago — 12 colleges total) and whether attending these colleges causally improves post-college outcomes. The authors construct a de-identified panel dataset linking federal income tax records, Department of Education college attendance data, College Board and ACT test scores, and application and admissions records from several Ivy-Plus and flagship public colleges covering approximately 2.4 million students across entering classes from 1998–2015.

The central finding on the input side is that students from families in the top 1% of the income distribution (income above $611,000) are 2.3 times more likely to attend an Ivy-Plus college than middle-class students (defined as the 70th–80th percentiles of the national parental income distribution, approximately $91,000–$114,000) with comparable SAT/ACT scores. Two-thirds of this gap is attributable to higher admissions rates at Ivy-Plus colleges for high-income applicants; conditional on SAT/ACT scores, top-1% applicants are 58% more likely to be admitted than middle-class applicants. The remaining third splits between differences in application rates (roughly 20% of the total attendance gap) and matriculation rates (roughly 12%). In contrast, admissions rates at flagship public colleges are essentially uncorrelated with parental income conditional on test scores.

Three admissions practices drive the high-income admissions advantage at Ivy-Plus colleges. First, legacy preferences: legacy applicants from the top 1% are admitted at more than five times the rate of non-legacy applicants with comparable test scores, demographics, and admissions ratings; children of alumni of a given Ivy-Plus college are not more likely to be admitted to other Ivy-Plus colleges, confirming that legacy status is not merely a proxy for unobservable credentials. Legacy preferences account for 52 of the estimated 168 “extra” top-1% students per average Ivy-Plus class (enrollment ~1,650). Second, non-academic ratings: students from the top 1% have markedly stronger non-academic credentials (extracurricular activities, leadership ratings) partly because they disproportionately attend private high schools whose students receive higher non-academic ratings despite no higher academic ratings; this accounts for 35 additional extra top-1% students. Third, athletic recruitment: the share of recruited athletes rises from 5% among admitted students from the bottom 60% to 13% among those from the top 1%, accounting for 27 additional extra top-1% students.

On the output side, the authors estimate causal effects of attending an Ivy-Plus college using a new research design based on waitlisted applicants. The key identification assumption is that idiosyncratic variation in admissions decisions across waitlisted applicants at one Ivy-Plus college is uncorrelated with admissions decisions at other Ivy-Plus colleges — which the authors verify empirically. Under this assumption, comparisons of admitted vs. rejected waitlisted applicants identify causal effects for marginal students. The marginal student who attends an Ivy-Plus college instead of the average flagship public is approximately 50% more likely to reach the top 1% of the earnings distribution at age 33, nearly twice as likely to attend a highly-ranked graduate school, and 2.5 times as likely to work at a prestigious firm. Attending an Ivy-Plus college increases mean earnings by $101,000 at age 33 relative to a counterfactual mean of $143,000 at state flagships. Effects are concentrated in the upper tail of earnings — the impact on reaching the top quartile is small and statistically insignificant, while impacts on reaching the top 1% far exceed what a constant percentage treatment effect would predict. Effects are larger for students with weaker fallback options (i.e., whose home-state colleges channel fewer students to the top 1%).

Critically, the three credentials driving the high-income admissions advantage — legacy status, athletic recruitment, and high non-academic ratings — are uncorrelated with or negatively correlated with post-college success once the college attended is held constant. Academic credentials (SAT/ACT scores, academic ratings) remain highly predictive of outcomes.

Counterfactual simulations show that eliminating all three high-income admissions preferences and replacing those slots with students having the same test score distribution would increase enrollment from the bottom 95% of the parental income distribution by 8.8 percentage points — comparable in magnitude to the effect of race-based affirmative action on Black and Hispanic enrollment shares. Such a policy would have small effects on monetary leadership outcomes (e.g., Fortune 500 CEO share from bottom-95% families rises by only 0.4 pp, because Ivy-Plus graduates are a small fraction of all top earners) but larger effects on non-monetary leadership positions: the share of senators from the bottom 95% would rise by 1.7 pp and the share of Supreme Court justices by 5.4 pp. With need-affirmative policies (giving low-income students preferences comparable to those currently given to legacy applicants), the share of Supreme Court justices from families in the bottom 60% would rise by 17.5 pp. These predictions assume that the causal share of Ivy-Plus attendance in explaining observational differences in leadership outcomes is the same as that estimated for early-career outcomes, and they ignore general equilibrium effects.

Q: How much more likely are top-1% students to attend an Ivy-Plus college than middle-class students with the same test scores? A: Students from families in the top 1% (income above $611,000) are 2.3 times more likely to attend an Ivy-Plus college than students from the 70th–80th percentile of the parental income distribution (approximately $91,000–$114,000) with comparable SAT/ACT scores. This “missing middle” pattern is stable across entering classes from 1998 to 2018 and persists after controlling for race and ethnicity.

Q: How is the overall attendance gap decomposed into application, admissions, and matriculation? A: Differences in admissions rates explain two-thirds of the gap in Ivy-Plus attendance between top-1% and middle-class students conditional on test scores. Of the estimated 168 “extra” top-1% students per average Ivy-Plus class, 87 come from higher admissions rates for non-recruited athletes, 27 from athletic recruitment, and the remaining slack from application rate differences (accounting for roughly 20% of the overall attendance gap) and matriculation differences (roughly 12%).

Q: How large is the admissions advantage for top-1% applicants at Ivy-Plus colleges? A: Conditional on SAT/ACT scores, applicants from the top 1% are 58% more likely to be admitted to Ivy-Plus colleges than middle-class applicants. Students from the top 0.1% are 2.5 times more likely to be admitted than middle-class applicants with comparable test scores. At flagship public colleges, admissions rates are essentially constant across the income distribution conditional on test scores.

Q: What is the magnitude of legacy preferences and how is it established that legacy is not just a proxy for other credentials? A: Legacy applicants from the top 1% are admitted at more than five times the rate of otherwise comparable non-legacy applicants at the college their parents attended. The paper isolates the legacy effect by showing that children of alumni at a given Ivy-Plus college are only slightly more likely to be admitted at other Ivy-Plus colleges — and the predicted counterfactual admissions rate for legacy students at other colleges closely matches their actual admissions rate — confirming that legacy status is not merely a proxy for other unobservable credentials. Legacy applicants constitute 2.5% of the overall applicant pool but over 9% of top-1% applicants.

Q: How do non-academic credentials differ by parental income, and what drives the difference? A: Top-1% applicants have markedly stronger non-academic ratings (measuring extracurricular participation and leadership traits) compared with other applicants, while the share achieving high academic ratings is essentially constant across the income distribution. Students from the top 1% are much more likely to have attended private high schools, whose applicants receive substantially higher non-academic ratings than students from public high schools with the same SAT/ACT scores. Non-academic ratings account for 35 of the estimated 168 extra top-1% students per Ivy-Plus class.

Q: What is the research design for estimating causal effects, and what is the key identification assumption? A: The authors focus on applicants who are waitlisted at a given Ivy-Plus college and compare those ultimately admitted versus rejected from the waitlist. The key identification assumption is that if different colleges’ admissions committees make correlated assessments of underlying student merit but uncorrelated idiosyncratic admissions errors, then residual variation in admissions outcomes for waitlisted applicants at one college is orthogonal to students’ long-run potential. The authors validate this empirically by showing that waitlist admission at one Ivy-Plus college is uncorrelated with admissions decisions and internal ratings at other Ivy-Plus colleges.

Q: What are the causal effects of attending an Ivy-Plus college on post-college outcomes? A: For the marginal student (one who attends an Ivy-Plus college instead of the average flagship public), attending an Ivy-Plus college increases the probability of reaching the top 1% of the earnings distribution at age 33 by approximately 50%, nearly doubles the probability of attending an elite graduate school, and increases the probability of working at a prestigious firm by approximately 2.5 times. Mean earnings at age 33 increase by $101,000 (relative to a counterfactual mean of $143,000 at state flagships). Effects on reaching the top quartile of earnings are small and statistically insignificant, while effects at the very top tail are disproportionately large.

Q: Why do the findings differ from Dale and Krueger (2002) and related studies finding little effect of selective college attendance on earnings? A: The authors replicate the matriculation design of Dale and Krueger (comparing outcomes conditional on the set of colleges to which students were admitted) and obtain estimates statistically indistinguishable from their waitlist design — the research designs are not the source of disagreement. Instead, the differences arise because (1) the authors have direct college fixed effects rather than relying on average test scores as a proxy for college quality, and (2) the authors focus on upper-tail outcomes (top 1% earnings, elite graduate schools, prestigious firms) rather than log mean earnings, where Ivy-Plus colleges have their largest effects.

Q: Are the credentials that drive the high-income admissions advantage — legacy, athlete status, high non-academic ratings — predictive of better post-college outcomes? A: No. Recruited athletes, students with higher non-academic ratings, and legacy students have equivalent or lower chances of reaching the upper tail of the income distribution, attending an elite graduate school, or working at a prestigious firm than comparable Ivy-Plus applicants once the college attended is held constant. By contrast, SAT/ACT scores and academic ratings are highly positively predictive of all three post-college outcome measures.

Q: How much could changing admissions practices diversify Ivy-Plus enrollment and subsequently society’s leadership? A: Eliminating legacy preferences, non-academic rating weights, and the differential recruitment of high-income athletes — and filling those slots with students having the same test score distribution as the current class — would increase enrollment from families in the bottom 95% of the parental income distribution by 8.8 percentage points, a magnitude comparable to race-based affirmative action’s effect on Black and Hispanic enrollment shares. For leadership positions, predicted effects are small for monetary outcomes (Fortune 500 CEOs from the bottom 95% would increase by only 0.4 pp) but larger for positions where Ivy-Plus graduates are a larger share: senators from the bottom 95% would increase by 1.7 pp and Supreme Court justices by 5.4 pp. A stronger need-affirmative policy (giving low-income students preferences equivalent to current legacy preferences) would increase the share of Supreme Court justices from the bottom 60% by 17.5 pp.

Q: How are “elite” and “prestigious” employers defined in this study? A: Elite firms are defined as those that disproportionately employ Ivy-Plus graduates relative to flagship public graduates, pulling firms from the top of that ratio ranking until 25% of Ivy-Plus attendee employment is accounted for. Prestigious employers are defined by the residual of that ratio after controlling for the firm’s predicted top-1% income probability — they are firms that disproportionately employ Ivy-Plus graduates conditional on their salaries, capturing high-status jobs that do not necessarily lead to the highest earnings. The paper validates this algorithmic approach against external rankings (Vault.com for law and consulting firms; Scimagoir for hospitals), finding substantial overlap.

Q: How are treatment effect estimates adjusted for heterogeneity in students’ fallback options? A: Causal effects of Ivy-Plus attendance are much larger for students with weaker fallback options — specifically, students whose home-state flagship colleges channel fewer students to the top 1% of earnings. The authors exploit this heterogeneity to estimate the treatment effect for the marginal student who actually switches from a flagship public to an Ivy-Plus college. This heterogeneity also implies that the average causal effect across all admitted students may differ from the effect for the marginal admitted student.

Q: What share of the overrepresentation of top-1% families at Ivy-Plus colleges is attributable to pre-application factors versus admissions practices? A: Of the 245 “extra” top-1% students in an average Ivy-Plus class relative to an unconditionally income-neutral benchmark, 77 (31%) are attributable to the higher test scores of top-1% students (a pre-application factor). The remaining 168 (69%) reflect higher attendance rates conditional on test scores, of which the large majority is attributable to admissions practices (legacy, non-academic ratings, athletic recruitment) rather than application or matriculation rate differences.

Ivy-Plus colleges: The twelve highly selective private colleges comprising the eight Ivy League institutions plus Stanford, MIT, Duke, and the University of Chicago — the focus group of the study, which together account for more than 10% of Fortune 500 CEOs, a quarter of U.S. senators, and three-fourths of Supreme Court justices appointed in the last half century despite enrolling less than 0.5% of Americans.

Missing middle: The pattern by which attendance rates at Ivy-Plus colleges conditional on SAT/ACT scores are lowest for students from the middle class (70th–80th percentile of the parental income distribution, approximately $91,000–$114,000) — lower than both the top 1% and, slightly, the bottom 40% — producing a non-monotone income gradient in attendance.

Legacy preference: An admissions advantage given to applicants whose parent(s) obtained an undergraduate degree from the college to which the student is applying. In the paper’s data, legacy applicants from the top 1% are admitted at more than five times the rate of non-legacy applicants with comparable test scores, demographics, and admissions ratings; the preference is college-specific (children of alumni are only slightly more likely to be admitted at other Ivy-Plus colleges).

Waitlist research design: The paper’s primary identification strategy for causal effects, which exploits idiosyncratic variation in admissions decisions among waitlisted applicants. The design’s validity rests on the empirical finding that waitlist admissions at one Ivy-Plus college are uncorrelated with admissions decisions and internal ratings at other Ivy-Plus colleges, implying that residual variation conditional on being on the waitlist is orthogonal to students’ long-run potential outcomes.

Prestigious employers: Firms defined by the paper’s algorithm as disproportionately employing Ivy-Plus graduates conditional on those firms’ predicted top-1% income probability — capturing high-status employment that does not necessarily lead to the highest earnings (e.g., prominent law firms, consulting firms, elite hospitals). Validated against external rankings (Vault.com, Scimagoir).

Non-academic ratings: Numerical scores assigned by admissions officers measuring aspects of an application outside academic achievement, such as extracurricular activities and leadership traits. In the paper’s data, non-academic ratings differ substantially by parental income — particularly because top-1% applicants disproportionately attend private high schools whose students receive higher non-academic ratings — while academic ratings do not differ across the income distribution.

Surrogate index: A prediction of later earnings outcomes (specifically, probability of reaching the top 1% at age 33 and mean income rank) constructed from individuals’ graduate school attendance and employer fixed effects at ages 22–25, used to extend the outcome window for cohorts observed only early in their careers. The approach follows the terminology and methodology of Athey et al. (2019).

Labor Market Shocks and Monetary Policy

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

Overview

Research question. The paper asks two related questions: (1) How much, and through which channels, do employer-to-employer (EE) worker transitions affect macroeconomic outcomes — particularly inflation? (2) What is the optimal monetary policy within a class of Taylor rules when EE flows are taken explicitly into account?

Motivation. Standard monetary policy frameworks condition on the unemployment rate as the primary labor market slack measure and underemphasize the “quality” dimension of employment. The paper documents a striking empirical pattern: the 2016–2019 recovery and the 2021–2022 recovery from COVID-19 featured nearly identical declines in the unemployment rate, yet exhibited dramatically different EE rate dynamics and inflation outcomes. During 2016–2019, the EE rate remained flat despite a roughly 25 percent decline in the unemployment rate from trend. During 2021–2022, the EE rate rose by around 8 percent above trend over a comparable unemployment decline. Correspondingly, unit labor cost (ULC) growth reached approximately 6 percent during the COVID-19 recovery when unemployment fell below 4 percent, compared with only about 2 percent ULC growth in the 2016–2019 period at similar unemployment levels.

Methodology. The authors develop a Heterogeneous Agent New Keynesian (HANK) model with a frictional labor market featuring on-the-job search (OJS). Workers are heterogeneous in wealth (mutual fund shares), human capital, match-specific productivity, and endogenous piece-rate wages. Human capital stochastically appreciates when employed and depreciates when unemployed, capturing scarring effects and job-stayer wage growth. Wage determination follows a Bertrand competition protocol based on flow output: workers switch to higher-productivity matches and extract the full surplus from the new firm, while outside offers from lower-productivity firms can still trigger rebargaining with the incumbent firm and raise the piece rate without a job switch. Three vertically integrated sectors — labor services, intermediate goods, and final goods — are linked so that the real price of labor services pl is the real marginal cost for intermediate firms and the sole driver of inflation in the New Keynesian Phillips curve (absent aggregate productivity shocks). The economy is subject to AR(1) shocks to the discount rate β (demand), aggregate labor productivity z (supply), and OJS efficiency ν (the relative search efficiency of employed workers). The model is solved using the Sequence-Space Jacobian (SSJ) method, extended to handle discretized worker distributions as direct inputs to equilibrium conditions.

The model is calibrated to U.S. pre-Great Recession data (2004–2006), targeting the fraction of hand-to-mouth individuals (16 percent of SIPP sample), unemployment rate (5.1 percent), EU separation rate (3.8 percent quarterly), EE rate (2 percent quarterly from LEHD), earnings drop upon job loss (35 percent), wage growth of job switchers (9 percent), and the labor share (0.67). Shock processes are estimated by minimizing deviations from empirical correlations and standard deviations of output, unemployment, EE rate, and inflation over 1995:Q3–2008:Q4.

Main findings — positive analysis. Shocks to OJS efficiency account for 43.1 percent of fluctuations in inflation in the variance decomposition, and 78.7 percent of fluctuations in the EE rate. The mechanism: a higher OJS efficiency lowers the expected match value EJ for labor services firms through three channels — (i) a compositional shift toward employed job seekers who extract the entire match surplus, (ii) shorter expected match duration as workers face higher poaching probabilities, and (iii) more frequent wage rebargaining where outside offers bid up wages without accompanying productivity gains. To maintain the free-entry condition, the real price of labor services pl must rise, increasing the real marginal cost and inflation. This direct labor market effect explains 139 percent of the total increase in pl; general equilibrium effects through reduced tightness θ — which raises expected match values by making vacancies easier to fill and workers less likely to be poached — offset −42 percent; the remainder (3 percent) comes from real rate changes driven by the monetary policy reaction.

In two historical simulations, muted OJS efficiency during 2016–2019 generated approximately 0.23 percentage points lower annualized inflation at the peak relative to a counterfactual economy with the same unemployment path but an endogenously rising EE rate. Conversely, elevated OJS efficiency during 2021–2022 generated approximately 0.56 percentage points higher annualized inflation compared to the flat-EE-rate counterfactual. The paper notes that strong worker mobility accounts for roughly 10 percent of the approximately 6 percentage point total rise in annual inflation during the COVID-19 recovery episode.

An important cross-model comparison shows that the Representative Agent New Keynesian (RANK) version of the model overestimates the decline in demand, output, and labor market tightness upon a positive OJS shock, and underestimates the rise in real rate, marginal cost, and inflation. Household heterogeneity is therefore quantitatively important: hand-to-mouth households’ demand responds directly to labor income increases from job switches, mitigating the demand decline and amplifying inflation.

Main findings — normative analysis. The optimal monetary policy within an augmented Taylor rule — adding an EE gap term ΦEE(EEt − EE*) alongside the standard inflation and unemployment gap terms — prescribes Φ*_u = −3.18 and Φ*_EE = 2.22 (with Φπ fixed at 1.5). This yields a 78.7 percent reduction in the central bank loss relative to the baseline Taylor rule. A policy that ignores EE dynamics and optimizes only the unemployment gap coefficient (finding Φu = −2.71, ΦEE = 0) produces a 12 percent larger central bank loss than the full optimal policy. In terms of welfare, the optimal policy delivers 0.16 percent additional lifetime consumption equivalent in the aggregate. Workers at the bottom of the match quality distribution gain the most (0.24 percent), as do the unemployed (0.20 percent), while those at the top of the wealth distribution gain the least due to larger share price fluctuations under the more aggressive policy.

Scope conditions. Results are derived conditional on a dual-mandate central bank objective (variance of inflation and output gaps), within a class of Taylor-type rules (not fully optimal Ramsey policy), under first-order approximation around a non-stochastic steady state. The historical simulations abstract from supply shocks active in the normative exercises and assume the economy starts from steady state in 2016.

In depth

Q1. What is the OJS efficiency shock, and how does it differ from a standard demand or supply shock?

An OJS efficiency shock is modeled as a time-varying shift in νt, the relative job search efficiency of employed workers compared with unemployed workers. Unlike demand shocks (discount rate β innovations) and productivity shocks (aggregate z innovations), which move inflation and unemployment in opposite directions under standard New Keynesian logic (divine coincidence), OJS efficiency shocks move inflation and unemployment in the same direction: a positive OJS shock raises inflation while also raising unemployment (because the higher real rate induced by the central bank’s reaction reduces demand and employment). This makes OJS shocks behave like cost-push shocks and introduces a genuine policy trade-off for a dual-mandate central bank.

Q2. What are the three mechanisms through which higher OJS efficiency raises the real price of labor services, and what is the quantitative contribution of each?

The decomposition (Figure 8) shows that the direct effect of ν on EJ — encompassing the composition channel (more employed job seekers who extract the full surplus), the match-duration channel (shorter expected match lives), and the wage rebargaining channel (outside offers raise wages without productivity gains) — explains 139 percent of the total increase in pl. The general equilibrium reduction in labor market tightness θ, which raises EJ and partially offsets the cost increase, explains −42 percent in total: −18 percent through increased supply of labor services L (productivity-enhancing job switches improve the match distribution) and −24 percent through reduced output Y (lower aggregate demand). Real rate effects account for the remaining 3 percent net (8 percent from the inflation channel and −5 percent from the unemployment channel). Labor market effects in total therefore explain 97 percent of the marginal cost increase.

Q3. Does the positive relationship between EE rates and inflation require wage increases upon job switches?

No. The paper demonstrates (Section 2.4.2, Figure 3) that even when the piece rate for workers hired from unemployment is set to α = 0.95 (so that outside offers have negligible wage effects), a positive OJS efficiency shock still generates a decline in output and a rise in inflation in both the RANK and TANK models. Quantitatively, the inflation response is similar across the baseline and near-zero composition-channel specifications, confirming that the shorter expected match duration is the primary driver of the increase in the real price of labor services. The match duration channel operates independently of wage increases: firms anticipate shorter matches and require a higher flow price to break even on vacancy costs.

Q4. How does household heterogeneity change the quantitative effects of OJS shocks relative to the RANK benchmark?

Under a constant real rate, in the RANK model a higher OJS efficiency increases the real price of labor services and inflation but has no effect on aggregate demand or output (because higher labor income for the PIH household is exactly offset by lower firm profits). In the TANK model, hand-to-mouth households consume their entire labor income, so the rise in labor income from job switches directly boosts their demand, raising output and tightness and further amplifying inflation. Under an endogenous real rate, the RANK model overestimates the decline in demand and output, and underestimates the rise in real rate and inflation, compared with the TANK model. The TANK model requires a substantially larger equilibrium real rate increase to contain inflation because HtM households’ demand is less elastic to the real rate than PIH households'.

The six AR(1) parameters governing β, z, and ν (three persistence parameters ρj and three standard deviations σj) are estimated by minimizing the sum of squared deviations between model-generated and empirical moments: the autocorrelation of output; correlations of the unemployment rate, EE rate, and inflation with output; and standard deviations of output, unemployment rate, EE rate, and inflation. Data cover 1995:Q3–2008:Q4. Estimated values are ρβ = 0.909, ρz = 0.332, ρν = 0.936 and σβ = 0.001, σz = 0.002, σν = 0.003. The variance decomposition (Table 4) assigns 43.1 percent of inflation variance to OJS efficiency shocks ν, 52.0 percent to demand shocks β, and 4.9 percent to productivity shocks z.

Q6. How is the “missing inflation” during 2016–2019 quantified, and what is the counterfactual?

The exercise simulates two economies both replicating the same unemployment path — a 15 percent decline in unemployment relative to its 5.2 percent steady state, spread linearly over 16 quarters, followed by mean reversion. The first economy uses only positive demand shocks, which generate an endogenously rising EE rate consistent with the historical unemployment-EE correlation. The second economy additionally introduces negative OJS efficiency shocks to keep the EE rate unchanged, as observed in the data during 2016–2019. Annualized inflation in the second economy is 0.23 percentage points lower at the peak (16 quarters after the shock), implying that had the EE rate risen normally, inflation would have been around 2 percent in 2019 rather than the observed 1.8 percent.

Q7. How is the inflationary role of elevated EE transitions during 2021–2022 quantified?

Using the same unemployment path as the 2016–2019 exercise, the COVID-19 recovery economy combines positive demand shocks with positive OJS efficiency shocks to replicate the observed 0.16 percentage point (8 percent above trend) increase in the EE rate. Comparing this economy to the flat-EE-rate economy from the prior exercise, the elevated EE rate generates 0.56 percentage points higher annualized inflation. Because annual inflation rose approximately 6 percentage points in the data during this episode, the model attributes roughly 10 percent of the total inflation increase to strong worker mobility.

Q8. What are the optimal Taylor rule coefficients when EE dynamics are included, and what is the welfare cost of ignoring them?

The optimal policy over the augmented Taylor rule it = i* + Φπ(πt − π*) + Φu(ut − u*) + ΦEE(EEt − EE*), with Φπ fixed at 1.5 and a dual-mandate loss function W = var(πt − π*) + 0.25·var(Yt − Y*), prescribes Φ*_u = −3.18 and Φ*_EE = 2.22. This reduces the central bank loss by 78.7 percent relative to the baseline rule (Φu = −0.25, ΦEE = 0). If the EE gap term is excluded and only the unemployment gap coefficient is re-optimized (finding Φu = −2.71), the central bank loss is 12 percent higher than under the full optimal policy.

Q9. How does the optimal policy affect macroeconomic volatility, and who gains most from it?

Table 5 shows that the optimal policy substantially reduces volatility of inflation (standard deviation falls from 0.0013 to 0.0011), output (0.0059 to 0.0020), consumption (0.0059 to 0.0020), unemployment (0.0047 to 0.0013), labor market tightness (0.0600 to 0.0175), and the real marginal cost pl (0.0203 to 0.0081), at the cost of higher real rate volatility (0.0019 to 0.0033) and share price volatility (0.1975 to 0.3051). In terms of welfare (Table 6), the unemployed gain 0.20 percent in lifetime consumption equivalents (versus 0.15 percent for the employed), workers at the bottom quintile of match quality gain 0.24 percent (versus 0.16 percent at the top), and wealth-poor individuals in the bottom share quintile gain 0.23 percent (versus 0.11 percent at the top, whose gains are eroded by larger share price fluctuations).

Q10. How does the model extend the SSJ computational method, and why is this extension necessary?

The standard SSJ method of Auclert, Bardoczy, Rognlie, and Straub (2021) handles settings where only scalar aggregates enter equilibrium conditions in sequence space. In this model, the discretized distributions of employed workers µE(h, x) and unemployed workers µU(h) at the job search stage enter directly into the expected match value EJ (because human capital and current match productivity determine output and wage levels upon new contacts), and the distribution λE(h, x, α) at the production stage enters into labor services firm profits ΓS. The authors treat worker distributions as histograms and compute Jacobians for each mass point, combining the SSJ method with Reiter (2009)-style projection. This substantially increases computation time but remains feasible, extending the SSJ method to multi-stage models with search frictions where endogenous distributions are state variables.

Q11. What are the three sources of wage growth in the HANK model, and what is their relevance for inflation dynamics?

First, human capital h stochastically appreciates during employment (at rate πE = 0.018 per quarter, calibrated to annual job-stayer wage growth of approximately 2 percent), raising wages through a higher piece-rate base. Second, job switches to higher-productivity matches yield wage increases as the worker extracts the full surplus from the new firm (the new piece rate equals x/x’, the ratio of old to new match productivity). Third, outside offers with productivity x’ satisfying αx < x’ < x — not good enough to trigger a switch but better than the current bargaining threat — cause the incumbent firm to raise the piece rate to x’/x via rebargaining, increasing wages without a job change. The second and third channels are the ones directly affected by OJS efficiency shocks and are inflationary: they raise labor costs beyond productivity gains.

Q12. Why do OJS shocks have a shorter match duration channel even without wage increases?

When OJS efficiency ν rises, each employed worker faces a higher probability νtf(θt) of contacting another firm each period. Even if wages do not change upon contact (as in the α = 0.95 robustness exercise), a labor services firm posting a vacancy expects that any match it forms will be shorter-lived: the worker is more likely to be poached in the future. This shortens the expected present discounted value of the match for the firm, reducing EJ. To satisfy the free-entry condition (expected profit = vacancy cost κ), the price of labor services pl must rise, increasing the real marginal cost and inflation. Figure 3 confirms a nearly identical inflationary response under α = 0.95 as under the baseline, isolating this match-duration mechanism.

Key Concepts

OJS efficiency shock (νt shock). A time-varying shift in the relative job search efficiency of employed workers compared with unemployed workers. Modeled as an AR(1) process for νt (estimated persistence ρν = 0.936). An increase in νt raises the probability that employed workers contact outside firms each period, boosting the EE rate. In the model, this acts as a cost-push shock: it raises inflation and unemployment simultaneously, breaking divine coincidence and creating a policy trade-off for a dual-mandate central bank.

Expected match value (EJt). The ex-ante expected value to a labor services firm of a filled vacancy, conditional on contacting a worker, defined as a weighted average of match values J across the pool of job seekers (unemployed and employed). The free-entry condition Vt = κ/q(θt) = EJt pins down the real price of labor services pl: when EJt declines (due to shorter match durations or compositional shifts toward high-surplus-extracting workers), pl must rise to maintain zero expected profit for vacancy posters.

Composition channel. The mechanism by which a rise in OJS efficiency shifts the composition of the job-seeker pool toward employed workers, who (under Bertrand competition) extract the entire flow surplus of a new match and receive wage equal to plF(h,x). Since firms receive zero rent from poached workers, an increase in the fraction of employed in the applicant pool lowers EJt and requires a compensatory increase in pl.

Match duration channel. When OJS efficiency ν rises, each existing match faces a higher probability of dissolution because the worker is more likely to be poached. The reduced expected match duration lowers the present discounted value of a match for the firm (even holding wages fixed), reducing EJt and raising pl. Demonstrated as the primary driver of inflation in the α = 0.95 robustness exercise where wage increases upon job switches are near zero.

Piece-rate α (endogenous). The share of match output F(h,x) that the worker receives as wage, determined through Bertrand competition on flow output following Postel-Vinay and Robin (2002). A worker hired from unemployment starts at α = x̄/x’ (where x̄ is the lowest match productivity). Job switches to higher-x’ firms reset α = x/x’. Rebargaining upon a credible outside offer from a firm with αx < x̃ < x raises α to x̃/x. The piece rate endogenizes wage dynamics for switchers, stayers, and job losers, allowing the model to discipline these moments in the data.

Divine coincidence (and its breakdown under OJS shocks). In standard New Keynesian models, demand and productivity shocks move inflation and unemployment gaps in opposite directions, so stabilizing inflation also stabilizes the output gap. OJS efficiency shocks break this property: they generate simultaneous increases in inflation and unemployment, introducing a genuine trade-off between the two mandates and making EE-augmented Taylor rules welfare-improving relative to rules that respond only to unemployment.

Sequence-Space Jacobian (SSJ) method with distributed worker states. An extension of the Auclert, Bardoczy, Rognlie, and Straub (2021) computational method to settings where discretized distributions of workers (µE(h,x) and µU(h)) enter directly into equilibrium conditions — specifically into the free-entry condition via EJt and into firm profits. The authors treat distributions as histograms and compute Jacobians for each mass point, combining SSJ with Reiter (2009)-style projection to efficiently solve for transitional dynamics under aggregate uncertainty.

The Effect of Education Policy on Crime: An Intergenerational Perspective

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

This paper studies the intergenerational effects of education policy on crime, asking whether a compulsory schooling reform that reduced crime among those directly exposed also reduced crime among their children. The authors exploit the staggered municipal rollout of Sweden’s comprehensive school reform, implemented gradually between 1949 and 1962 across more than 1,000 municipalities, which increased compulsory schooling by one to two years, abolished tracking into academic and vocational streams after 6th grade, and introduced a uniform national curriculum. The parent generation consists of all individuals born in Sweden between 1945 and 1955 (approximately 447,000 men and 450,000 women), and their children form the child generation (426,721 sons observed from age 15 to 29). Crime is measured by administrative conviction records from the Swedish National Council for Crime Prevention covering 1973–2010.

The empirical strategy is difference-in-differences, comparing changes in conviction rates across cohorts in municipalities that implemented the reform at different times, with treatment assigned based on the parent’s birth municipality to avoid endogenous sorting bias. Standard errors are clustered at the municipality level. Parallel trends validity is supported by three tests: results are unchanged when municipality-specific linear trends are included, placebo tests using incorrect reform dates yield effects indistinguishable from zero, and residuals from crime regressions show no correlation with municipality-specific trends.

The main finding is a significant 0.79 percentage point (pp) decline in conviction rates among sons of fathers exposed to the reform (p-value < 0.002), representing a 3.4 percent reduction relative to baseline. The decline spans multiple crime types: violent crime fell by 0.27 pp, traffic-related crime by 0.45 pp, fraud by 0.22 pp, and other offenses by 0.41 pp — percentage reductions of three to six percent across categories. Multiple convictions fell by 0.43 pp (5.8 percent). These second-generation effects are driven entirely by paternal exposure: the impact of maternal reform exposure is an order of magnitude smaller and statistically insignificant, and the difference between paternal and maternal effects is itself significant (p-value 0.048 for any conviction, 0.009 for multiple convictions). Effects on daughters in the child generation are much smaller, with only the residual “other crime” category showing a significant 0.129 pp (15.5 percent) decline.

The asymmetry between paternal and maternal transmission is explained by the first-generation effects of the reform. For men, the reform increased schooling by 0.32 years, earnings by approximately 1 percent, the probability of white-collar employment by 1.2 percent, cognitive skills by 0.14 standard deviations, noncognitive skills by 0.17 standard deviations, spousal earnings by 1,022 SEK per year, and overall household income by approximately 1 percent. For women, the reform increased education by 0.21 years but did not raise earnings, household income, or white-collar employment, and did not reduce their already low crime rates. Only 13 percent of women in the 1945–55 cohorts were at or below the compulsory schooling threshold, versus 20 percent of men, substantially limiting the reform’s bite for women.

A mediation analysis decomposes the intergenerational transmission through three channels: fathers’ education accounts for 64.8 percent of the indirect effect, the decline in paternal crime accounts for 18.5 percent, and the increase in household disposable income accounts for 16.7 percent. The direct effect (unexplained by these mediators) accounts for 48 percent of the total effect. The paper also documents that children of treated fathers attended schools with lower peer crime rates and lived in neighborhoods with lower youth crime rates, supporting a neighborhood and peer effects channel alongside human capital and role-model channels.

Scope conditions: the study covers male children observed to age 29 in Sweden; results apply to a context of near-universal administrative records, a specific postwar schooling reform, and cohorts born 1945–1955 in a Nordic welfare state.

Q: What is the magnitude of the intergenerational crime reduction caused by the reform?

A: Sons of fathers exposed to the reform experienced a 0.79 pp decline in conviction rates (p-value < 0.002), corresponding to a 3.4 percent reduction relative to the baseline conviction rate of approximately 24 percent for the child generation by age 29. Multiple convictions fell by 0.43 pp, a 5.8 percent reduction. These magnitudes are similar in percentage terms to the direct crime reduction the reform caused among fathers themselves.

Q: Does the reform’s intergenerational effect on crime differ by the sex of the treated parent?

A: Yes. The intergenerational effect is driven entirely by paternal exposure to the reform: the effect of maternal exposure is an order of magnitude smaller and insignificant at any conventional significance level. The difference between paternal and maternal effects is statistically significant, with p-values of 0.048 for any conviction and 0.009 for multiple convictions. The paper attributes this asymmetry to the much weaker first-generation effects of the reform on women’s earnings, household income, crime rates, and neighborhood sorting.

Q: Which crime types declined significantly among sons of treated fathers?

A: Significant declines were found in violent crime (−0.27 pp, Romano-Wolf p-value 0.09), traffic-related crime (−0.45 pp, RW p-value 0.057), fraud (−0.22 pp, RW p-value 0.09), and other offenses (−0.41 pp, RW p-value 0.047), each representing a three-to-six percent reduction relative to the mean incidence of that crime type. Property crime and drug-related crime did not show significant declines.

Q: What were the direct effects of the reform on the parent generation’s human capital?

A: For men, the reform increased schooling by 0.32 years, earnings by approximately 1 percent, the probability of white-collar employment by 1.2 percent, cognitive skills by 0.14 standard deviations, and noncognitive skills by 0.17 standard deviations, all measured at military enlistment. Spousal earnings increased by 1,022 SEK per year and overall household income rose by approximately 1 percent. For women, education increased by 0.21 years and marriage market matches improved, but earnings, household income, and white-collar employment probability did not increase significantly.

Q: Why did the reform have stronger first-generation effects on men than on women?

A: The average share of individuals at or below the compulsory schooling threshold — the margin at which the reform was binding — was 20 percent for men but only 13 percent for women in the 1945–55 cohorts. Because fewer women were constrained by the old compulsory schooling limit, the reform increased their education by less and produced smaller downstream effects on earnings and labor market outcomes.

Q: What are the three channels through which the reform reduces child crime, and what is the relative contribution of each?

A: The paper identifies three channels: (1) the human capital channel, whereby increased parental education raises household income and child human capital; (2) the role model channel, whereby reduced paternal crime participation directly reduces son’s crime; and (3) the neighborhood and peer effects channel, whereby higher income enables sorting into lower-crime neighborhoods and better schools. The mediation analysis attributes 64.8 percent of the indirect effect to fathers’ increased education, 18.5 percent to the decline in paternal crime, and 16.7 percent to the increase in household disposable income. The direct effect unexplained by these three mediators accounts for 48 percent of the total effect.

Q: What is the role model effect, and how strong is it in the parent generation?

A: The role model channel operates through the strong intergenerational persistence in crime participation: sons are 2.06 times more likely to participate in crime if their fathers have been convicted (Hjalmarsson and Lindquist, 2012). The reform reduced the incidence of any conviction among treated men by 1.5 pp and repeat convictions by 1.5 pp — the latter representing an approximately 8 percent decline from a lower base. For women, the reform produced no reduction in crime, providing no analogous role model improvement through the maternal channel.

Q: How does neighborhood and school peer quality change for children of treated fathers versus treated mothers?

A: Sons of fathers exposed to the reform moved to neighborhoods with lower youth crime rates (−0.087 pp) and attended schools with lower peer crime rates (−0.077 pp). In contrast, sons of mothers exposed to the reform experienced higher neighborhood crime rates (p-value 0.06) and higher school peer crime rates (p-value 0.01), the opposite direction. This asymmetry helps explain why only paternal treatment generates significant second-generation crime reductions.

Q: What happens to other outcomes for children of treated fathers beyond crime?

A: Sons experienced a 1.2 percentile increase in school GPA (RW p-value 0.05), a 2.3 pp increase in employment (RW p-value 0.04), a matching 2.3 pp decline in unemployment benefit receipt, a reduction in hospitalization of 2.4 days (17 percent, RW p-value 0.02), and a decline in prescribed drugs of 31 doses (2.8 percent, RW p-value 0.09). The decline in prescribed drugs for sons is driven by nervous system drugs and painkillers, pointing to improved mental health. Daughters of treated fathers show a significant reduction in welfare dependency but no other significant improvements.

Q: How does the paper validate the parallel trends assumption?

A: Three tests are reported. First, including municipality-specific linear trends leaves the main coefficient unchanged (p-value 0.85 for the trend terms themselves). Second, placebo contrasts using incorrect reform implementation dates produce effects indistinguishable from zero for all tested dates. Third, graphical inspection of regression residuals shows no correlation with municipality-specific trends. Together these provide strong support for the identifying assumption.

Q: Are the results sensitive to using a linear probability model instead of a nonlinear model?

A: A Monte Carlo experiment was conducted replicating observed crime rates across municipalities and imposing the estimated average treatment effect. Assuming the true data-generating process is a probit model, the linear probability model biases the estimated average effect upward by only 5 percent — a difference that is statistically indistinguishable from zero in the actual data — validating the OLS approach.

Q: What is the broader policy implication of the findings?

A: The results show that well-designed education policies can reduce crime not only among the directly treated generation but also among their children, amplifying the social benefits of reform across generations. The authors interpret this as consistent with the theoretical framework of Becker and Tomes (1979) on intergenerational transmission of human capital, and suggest that education policy evaluations that focus only on the treated generation substantially understate total social returns.

Intergenerational transmission of education reform effects: the phenomenon whereby an education policy that raises parental human capital produces improvements in children’s outcomes — including crime — through multiple channels including resource increases, parental role modeling, and neighborhood sorting, beyond any direct policy exposure of the child generation.

Comprehensive school reform (Sweden, 1949–1962): a nationally mandated restructuring of compulsory schooling that extended required attendance by one to two years, abolished selection into academic and vocational tracks after 6th grade, and introduced a uniform national curriculum, rolled out staggered across 1,055 Swedish municipalities.

Human capital channel: the mechanism by which increased parental education raises earnings and household income, enabling greater investments in children’s development and exploiting complementarity between parental and child human capital in the skill production function, thereby raising children’s opportunity cost of crime.

Role model channel: the mechanism by which reduced parental crime participation directly reduces children’s crime, operating through the transmission of norms and information across generations; identified empirically by the strong intergenerational correlation in convictions (sons with convicted fathers are 2.06 times more likely to be convicted themselves).

Neighborhood and peer effects channel: the mechanism by which increased parental income from the reform enables sorting into residential neighborhoods and schools with lower youth crime rates, exposing children to peers less involved in illegal activities and thereby reducing their own crime participation.

Mediation analysis: a decomposition method following Heckman, Pinto, and Savelyev (2013) that quantifies the share of a total treatment effect accounted for by specific intermediate variables (here: fathers’ education, fathers’ crime participation, and household disposable income) versus the direct unexplained effect.

Conviction rate: the proportion of individuals in a given generation and observation window who received at least one criminal conviction in Swedish administrative records; used as the primary outcome measure because it captures offenses that led to a court appearance, excluding minor infractions resolved by direct fine.

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.

J62 | Macro Paper Warehouse

Diversifying Society's Leaders? Determinants and Causal Effects of Admission

Labor Market Shocks and Monetary Policy

Overview

In depth

Q1. What is the OJS efficiency shock, and how does it differ from a standard demand or supply shock?

Q2. What are the three mechanisms through which higher OJS efficiency raises the real price of labor services, and what is the quantitative contribution of each?

Q3. Does the positive relationship between EE rates and inflation require wage increases upon job switches?

Q4. How does household heterogeneity change the quantitative effects of OJS shocks relative to the RANK benchmark?

Q5. How are aggregate shock processes estimated, and what share of inflation variance do OJS shocks explain?

Q6. How is the “missing inflation” during 2016–2019 quantified, and what is the counterfactual?

Q7. How is the inflationary role of elevated EE transitions during 2021–2022 quantified?

Q8. What are the optimal Taylor rule coefficients when EE dynamics are included, and what is the welfare cost of ignoring them?

Q9. How does the optimal policy affect macroeconomic volatility, and who gains most from it?

Q10. How does the model extend the SSJ computational method, and why is this extension necessary?

Q11. What are the three sources of wage growth in the HANK model, and what is their relevance for inflation dynamics?

Q12. Why do OJS shocks have a shorter match duration channel even without wage increases?

Key Concepts

The Effect of Education Policy on Crime: An Intergenerational Perspective

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