Margin Composition and the IV–OLS Gap in the Return to Schooling

Abstract

Instrumental-variables estimates of the return to schooling exceed ordinary least squares, and one benign explanation is that the instrument weights schooling margins differently from a linear specification. We test this on Card's 1976 National Longitudinal Survey of Young Men extract (N = 3,010). Reweighting the estimated cross-sectional return schedule by college proximity's Angrist–Imbens weights moves the return by −0.0044 (0.0079), against a gap of 0.0568 (0.0610). Composition of that schedule explains none of the gap, though it cannot be separated from a uniform level shift in complier returns. The gap itself is indistinguishable from zero.

JEL codes: C26, I26, J24, J31. Keywords: returns to schooling, instrumental variables, local average treatment effects, causal response function, college proximity, weak identification.

I. Introduction

Instrumental-variables estimates of the return to schooling built on supply-side variation are, as a rule, larger than the ordinary-least-squares estimates they are meant to correct. Card (1993) instruments schooling with an indicator for having grown up near a four-year college and finds returns 25 to 60 percent above OLS; Card (2001) documents the same ordering across a dozen designs. Under the textbook account, in which OLS is contaminated by omitted ability, the correction should run the other way. Four resolutions compete: heterogeneous complier returns (Imbens and Angrist 1994; Card 2001), composition of the schooling margins the instrument moves (Angrist and Imbens 1995), failure of the exclusion restriction, and weak identification (Bound, Jaeger, and Baker 1995; Lee et al. 2022).

Only one is benign. Angrist and Imbens (1995) show that with an ordered treatment and a binary instrument, two-stage least squares converges to a weighted average of per-unit causal effects across adjacent schooling margins, the weights given by the instrument-induced shift in the probability of reaching each level. Because the schooling–earnings profile is sharply non-linear — Jaeger and Page (1996) document large degree-year premia — two-stage least squares can exceed a linear-in-years coefficient with homogeneous per-margin effects and a valid instrument, so that channel should be netted out before the others are invoked. Kling (2001) reads the proximity instrument through this lens and finds it bites hardest at the high-school-to-college transition, but characterises the margins qualitatively and never computes the reweighted return the composition account implies. That is the arithmetic we supply.

We supply it on the 3,010-observation Card extract of the 1976 National Longitudinal Survey of Young Men, where OLS gives 0.0747 (0.0036) and just-identified two-stage least squares 0.1315 (0.0541): a ratio of 1.76 and a gap of 0.0568. Three findings follow. First, 0.725 of the instrument's weight is post-secondary but sits on entry rather than completion, the largest single weight (0.199) falling on the high-school-to-college transition and the three entry margins carrying 0.514 against 0.095 for bachelor's completion; the sheepskin premium the story needs, 0.2034 (0.0341) for the sixteenth year, is one the instrument barely touches. Second, the decomposition therefore fails: reweighting moves the return to 0.0703, a contribution of −0.0044 (0.0079), 95 percent percentile interval [−0.0219, 0.0093]. Third, the residual will not go to the exclusion restriction: the Conley, Hansen, and Rossi (2012) breakdown value of 0.0182 dwarfs the ability-implied direct effect of 0.0017.

Two qualifications belong here rather than in a footnote. What we refute is that composition of the estimated cross-sectional schedule reproduces two-stage least squares; the decomposition cannot separate that channel from complier returns exceeding the cross-section by a common amount at every margin. And the gap itself is fragile: at a first-stage $F$ of 14.14, Durbin–Wu–Hausman gives $t = -1.10$ ($p = 0.271$), the bootstrap interval for the gap is [−0.0471, 0.1975], and the Anderson–Rubin set [0.0285, 0.2810] contains the OLS coefficient. Section II sets out the decomposition, Section III the data, Section IV the results, Section V robustness and limitations, and Section VI concludes.

II. Conceptual Framework

Let $S_i \in \{1,\dots,18\}$ be years of schooling, $Y_i$ log hourly earnings, $Z_i$ an indicator for growing up near a four-year college, and $X_i$ a covariate vector; $Y_i(s)$ is the potential wage at schooling $s$ and $S_i(z)$ potential schooling. Three assumptions organise what follows. (A1) Conditional independence: $\{Y_i(s)\}_s, S_i(1), S_i(0) \perp Z_i \mid X_i$. (A2) Exclusion: $Z_i$ enters the wage equation only through $S_i$ — the contested assumption, since proximity may proxy for urban location or family advantage. (A3) Monotonicity: $S_i(1) \ge S_i(0)$ for every $i$. Under (A1)–(A3), Angrist and Imbens (1995) show that two-stage least squares identifies

where $\pi_j = P(S_i(1) \ge j) - P(S_i(0) \ge j)$. Because $S = \sum_j \mathbf{1}\{S \ge j\}$, the shifts sum to the first stage, so under (A3) the weights are non-negative and sum to one; which margins receive weight is an empirical matter. The linear OLS coefficient is a different weighted average of the same schedule, and if the profile is non-linear the two weightings differ mechanically. Writing $\beta_j^{\text{OLS}}$ for the incremental cross-sectional return at margin $j$ and $\beta^{\text{lin}}$ for the linear coefficient, define $\beta^{\text{RW}} = \sum_j \widehat{\omega}_j \widehat{\beta}_j^{\text{OLS}}$ and decompose

Computing the composition term requires neither (A2) nor any claim that $\beta_j^{\text{OLS}}$ is causal; reading it as the contribution of margin weighting requires only (A3). It is nonetheless a decomposition of estimands, and that bounds the interpretation twice over. The per-margin returns are cross-sectional contrasts, subject to ability bias and selection into schooling levels. And if complier returns exceed $\beta_j^{\text{OLS}}$ by a common amount $c$ at every margin, the residual absorbs $c$ while the composition term is unchanged: inside (2), composition and a uniform complier level shift are observationally equivalent, and only differential complier gains concentrated at particular margins are distinguished. Blandhol et al. (2022) add that with covariates entered linearly rather than saturated, two-stage least squares need not be a positively weighted average of local average treatment effects, so (1) describes the estimand the standard specification produces. The hypothesis is that composition carries at least half the gap; it is falsified if the contribution is near zero, negative, or bounded well below half.

III. Data and Empirical Strategy

A. Data

We use the Card (1993) extract of the U.S. National Longitudinal Survey of Young Men, distributed as card.csv in the R package wooldridge and mirrored by the Rdatasets archive at https://vincentarelbundock.github.io/Rdatasets/csv/wooldridge/card.csv, retrieved 8 September 2026 (sha256 326dad817467b20d…) under GPL-3: 3,010 observations on young American men interviewed in the 1976 wave.

The outcome lwage is the log of average hourly earnings in cents; educ is completed years of schooling, ranging from 1 to 18; nearc4 and nearc2 indicate growing up near a four-year and a two-year college. The fourteen controls are potential experience and its square in years, indicators for being black and for current residence in the South and in a metropolitan area, eight 1966 region-of-residence indicators (reg661–reg668, reg669 omitted), and 1966 metropolitan residence. Balance checks additionally use the IQ and KWW test scores, parental schooling in years, family structure at 14, and holding a library card at 14. The sample filter is one listwise deletion on these outcome, treatment, instrument and control variables; none is missing, so the estimation sample is all 3,010 observations. Item non-response affects only the auxiliary variables — IQ is observed for 2,061 men — and each balance regression runs on its own complete-case sample.

Table 1—Descriptive Statistics, Card NLSYM Extract, 1976 Wave

Notes: N = 3,010, the full estimation sample; no observations are lost to the filter. Standard deviations omitted for binary indicators. Mean age is 28.1 years; 0.505 have at least 13 years of schooling and 0.271 at least 16. Data: Card (1993) NLSYM extract, Rdatasets archive, retrieved 8 September 2026.

B. Estimating Equations

The Mincer benchmark, first stage and reduced form are, respectively,

with $\widehat{\beta}^{\text{2SLS}} = \widehat{\rho}/\widehat{\pi}$. Margin shifts come from linear probability models,

so $\sum_j \widehat{\pi}_j = \widehat{\pi}$ holds exactly by linearity. The return schedule comes from a wage equation saturated in schooling increments,

in which each $\beta_j$ is the incremental return to crossing margin $j$. Margins at nine years and below are pooled because those cells are thin; they carry 5.2 percent of the weight, and Section V varies the pooling point.

Standard errors are heteroskedasticity-robust (HC1); the data are an individual cross-section with no natural clustering dimension, so no clustering is applied. Inference on the decomposition uses a pairs bootstrap over individuals, 2,000 replications, seed 20260908. Because Lee et al. (2022) show conventional $t$-ratio inference on a single instrument to be unreliable at this first-stage strength, the primary interval for $\beta$ is the Anderson–Rubin 95 percent set, from inverting the reduced-form test on a grid of width 0.0005 over $[-1,1]$; the Wald interval is reported only for comparison.

IV. Results

A. Benchmarks and Whether the Gap Is Real

Table 2 reproduces the canonical result. OLS gives 0.0747 (0.0036): a year of schooling raises hourly earnings by 7.8 percent ($e^{0.0747}-1$), about 45 cents at the sample mean of 577.3 cents, and a one-standard-deviation increase of 2.68 years raises them by 22 percent. The first stage is 0.3199 (0.0851) — about a third of a year — with robust $F$ = 14.14, and the reduced form is 0.0421 (0.0175), so two-stage least squares is 0.1315 (0.0541): 14.1 percent a year, some 81 cents an hour, and 1.76 times OLS, inside the 25–60 percent excess Card (1993) reported. The two estimates differ by 36 cents an hour per year of schooling.

Table 2—Benchmark Estimates of the Return to Schooling

Notes: HC1 standard errors in parentheses; no clustering (individual cross-section). All columns control for experience and its square, black, residence in the South and in an SMSA, eight 1966 region indicators and 1966 SMSA residence. Column 4 is just-identified 2SLS; its Anderson–Rubin set is contiguous, is the primary interval given $F$ = 14.14 (Lee et al. 2022), and contains the OLS coefficient. *, **, *** denote 10, 5 and 1 percent significance.

Before explaining the gap it is worth testing it. The Durbin–Wu–Hausman control-function statistic on the first-stage residual is $t = -1.10$ ($p = 0.271$): exogeneity of schooling, hence equality of the two estimands, is not rejected, and the bootstrap puts the gap at 0.0568 (0.0610), percentile interval [−0.0471, 0.1975]. The puzzle is a difference of point estimates the sample cannot resolve, and everything below should be read in that light.

B. Which Margins the Instrument Moves

Table 3 reports the shifts, the implied weights and the cross-sectional return at each margin. The shifts sum to 0.31990, numerically identical to the first stage.

Table 3—Angrist–Imbens Margin Weights and Cross-Sectional Returns

Notes: N = 3,010; Table 2 controls throughout. Column 2 is the coefficient on four-year-college proximity in a linear probability model for reaching each level, equation (4); column 3 normalises the shifts to one. Column 4 is the incremental return from the saturated wage equation (5), ten schooling parameters, R² = 0.309, HC1 standard errors in parentheses. Margins at nine years and below are pooled. No standard errors were computed for columns 2 and 3, which are point estimates; the pairs bootstrap of Table 4 re-estimates the weights in every replication, so their sampling variation enters the composition term but is not reported for the weights. *, **, *** denote 10, 5 and 1 percent significance.

The weight profile is post-secondary but front-loaded: 0.725 lies at thirteen years and above, the largest single weight (0.199) is on the high-school-to-college transition, and the three entry margins carry 0.514 against 0.095 for bachelor's completion — sharpening Kling's (2001) qualitative reading. These aggregates decompose a first stage of 0.3199 (0.0851) and carry no inference of their own, so they are a point-estimated profile rather than precisely located weight.

The return schedule is as the sheepskin literature predicts: large premia at high-school completion (0.1574) and at the bachelor's year (0.2034, a 22.6 percent premium for the sixteenth year), consistent with Jaeger and Page (1996), but little in between — 0.0363 at 13→14 and −0.0217 at 14→15, neither distinguishable from zero. The two patterns are misaligned. Averaged with the instrument's weights, the entry margins are worth 0.0384 a year and the post-secondary margins 0.0673, both below the 0.0780 those weights imply for the pre-secondary margins and below the 0.0747 linear coefficient. College proximity moves men into college rather than through it, and the cross-section does not price entry.

C. The Decomposition

Table 4 executes equation (2). The reweighted estimate is 0.0703 (0.0088), so composition contributes −0.0044 (0.0079), 95 percent percentile interval [−0.0219, 0.0093]. That is the paper's primary statistic: reweighting is worth under three cents an hour per year of schooling against a gap worth about 36 cents, and even the most favourable end of the interval, 0.0093, is a sixth of the gap. The hypothesis that composition carries at least half of it is refuted with precision — the standard error on the composition term is an eighth of the one on the gap, because it is built from well-identified reduced-form objects rather than a ratio with a noisy denominator.

Table 4—Decomposing the 2SLS–OLS Gap

Notes: N = 3,010. Rows 1 and 3 reproduce Table 2, columns 1 and 4, with analytic HC1 standard errors; row 3's interval is the Anderson–Rubin set. Row 2 applies the Table 3 weights to the Table 3 returns. Rows 2 and 4–6 use a pairs bootstrap, 2,000 replications, seed 20260908, re-estimating every component in each replication. The memorandum row divides the composition term and its interval endpoints by the point estimate of the gap; that denominator is not significantly different from zero, so this is not a valid interval for the ratio and none is reported. Row 2 under alternatives: weights without covariate adjustment, 0.0721; low margins pooled at eleven years, 0.0728; at seven, 0.0693.

Inverting the decomposition shows how far the story is from working. Reconciling 0.1315 with the schedule needs complier returns exceeding the cross-section by 0.0845 at every post-secondary margin — 0.152 log points a year rather than the 0.067 priced — or, loading it all on the bachelor's year, that year worth 0.851 log points against 0.2034. Neither is credible as margin composition, though a uniform complier premium of that size would sit undetected in the residual.

V. Robustness and Heterogeneity

Monotonicity. (A3) requires every margin-specific shift to be weakly positive. Of the seventeen margins only two are negative, the most negative −0.0026, largest absolute $t$-statistic 0.51, so the Table 3 weights are a proper averaging.

Specification. The decomposition's two discretionary choices matter little: weights without covariate adjustment give 0.0721, pooling the low margins at eleven years 0.0728, at seven 0.0693 — all at or below the 0.0747 linear coefficient, so the composition term is not an artefact of how the bottom of the schooling distribution is handled.

Threats to identification. Table 5 collects the checks on (A2). Conditional on the controls, proximity is unrelated to IQ, parental schooling and family structure at fourteen; the joint test on six predetermined characteristics gives $F(6) = 1.14$ ($p = 0.336$) on the 1,616 men for whom all six are observed, and a library card at fourteen is marginal ($p = 0.056$). The one clearly significant imbalance is KWW, but it is administered at the 1976 interview and is plausibly a consequence of schooling, so it is not a valid balance test — nor, by the same token, evidence against a channel from proximity to labour-market knowledge outside schooling.

Table 5—Threats to the Exclusion Restriction

Notes: HC1 standard errors; no clustering; Table 2 controls throughout. Panel A regresses each characteristic on four-year-college proximity on its complete-case sample. The joint test instead regresses proximity on six predetermined characteristics — IQ, father's and mother's schooling, living with both parents at 14, living with a single mother at 14, and a library card at 14 — and tests them jointly; it excludes both KWW, which post-dates schooling, and living with a step-parent at 14. Panel B follows Conley, Hansen, and Rossi (2012): with a direct effect $\delta$ of proximity on log wages, $\beta(\delta) = (\widehat{\rho}-\delta)/\widehat{\pi}$, so the breakdown values solve $\beta(\delta) = 0.0747$ and $\beta(\delta) = 0$. The implied $\delta$ multiplies the Panel A IQ imbalance by the log-wage return per IQ point. *, **, *** denote 10, 5 and 1 percent significance.

Adding two-year-college proximity as a second instrument gives an over-identified estimate of 0.1571 (0.0526) and a Sargan statistic of 1.25 ($p = 0.264$), which does not reject. We do not read that as support for (A2): the added instrument is weak — first stage 0.1230 (0.0776), joint $F$ of 8.32, below the 14.14 from four-year proximity alone — so the test has little power and its non-rejection is close to uninformative. The sensitivity analysis carries more weight. A direct wage effect of 0.0182 would erase the gap; the only channel we can price, proximity's association with measured ability, implies 0.0017, nine percent of that, or 0.0049 at the upper end of the imbalance interval. A violation large enough to explain the gap would run almost entirely through channels the survey does not measure.

Heterogeneity. We estimated no subgroup returns: splitting a sample whose first-stage $F$ is 14.14 by parental education would leave first stages too weak to interpret, and father's schooling is missing for 690 men in a way unlikely to be random. Whether compliers are the credit-constrained men of Card's (2001) model or the positively selected entrants of Carneiro, Heckman, and Vytlacil (2011) remains open.

Limitations. Five restrictions bound what this study establishes. First, the per-margin returns in Table 3 are cross-sectional contrasts, not causal effects; the decomposition holds that schedule fixed and cannot distinguish composition from a uniform level shift in complier returns. Second, following Blandhol et al. (2022), linear covariate adjustment does not guarantee that 2SLS is a positively weighted average of local average treatment effects. Third, no inference was computed for the margin shifts or the aggregates 0.725, 0.514, 0.199 and 0.095, so the weight profile — the paper's mechanism — is a point estimate. Fourth, the balance evidence is weak evidence of validity, not proof: the joint test rests on 1,616 observations because IQ is missing for 949 men, IQ is measured in high school and so is only partly predetermined relative to the college decision, and the calibrated direct effect bounds one channel of violation rather than all. Fifth, this is a single cross-section of 3,010 young American men interviewed in 1976, with earnings observed only for those reporting them and no modelling of selection into the wage sample; nothing here speaks to women, later cohorts, other countries, or other instruments.

VI. Conclusion

The excess of instrumental-variables over ordinary-least-squares returns to schooling has three troubling explanations and one benign one. We have measured the benign one, over the estimands it is defined on, and found it empty. Reweighting the estimated cross-sectional schedule by the instrument's own Angrist–Imbens weights moves the return by −0.0044 (0.0079) against a gap of 0.0568, because the instrument concentrates on college-entry margins the cross-section prices at 0.0384 a year rather than on the bachelor's year it prices at 0.2034. That is silent on a complier premium spread evenly across margins; what it rules out is the mechanical, no-heterogeneity account.

The rest the data cannot settle. A measurable exclusion violation through ability is an order of magnitude too small, but the gap itself is not distinguishable from zero by any of our three tests. For a literature that has spent three decades theorising about why IV exceeds OLS here, the more disciplined reading is that the ordering is a property of two point estimates whose difference 3,010 men cannot resolve. Progress will come from stronger first stages, not from further explanations of a gap that may not be there.

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Data: Card, David. 1995. "Using Geographic Variation in College Proximity to Estimate the Return to Schooling." In Aspects of Labour Market Behaviour: Essays in Honour of John Vanderkamp, edited by Louis N. Christofides, E. Kenneth Grant, and Robert Swidinsky, 201–222. Toronto: University of Toronto Press. Extract distributed with Wooldridge, Jeffrey M., Introductory Econometrics: A Modern Approach, via the Rdatasets archive, https://vincentarelbundock.github.io/Rdatasets/csv/wooldridge/card.csv, retrieved 8 September 2026.