The Causal Effect of Parents' Schooling on Children's Schooling: A Comparison of Estimation Methods

Review of the prior causal literature plus an original application of all three designs to Swedish register data — twin parents, adoptees (foreign-born, Korean, and Swedish-born), and a compulsory schooling reform instrument

Swedish parents born in a common period and their children, plus the international twin/adoption/IV literature on intergenerational schooling.

Journal of Economic Literature 49(3), 615-651. The decisive paper on this question because it removes the usual excuse: the twin, adoption and IV literatures disagree, and the standing explanation was that they use different countries, cohorts and data. Holmlund et al. apply all three identification strategies to ONE Swedish register dataset covering parents born in the same period, and reproduce every discrepancy in the literature — which localizes the disagreement in the identification strategy, not the data. Numbers below are read from the working-paper version (IZA DP 3630 / CESifo 3234); the published JEL article should be checked against them before this source is marked verified. Their twin sample mixes MZ and DZ pairs, so the headline twin estimates are corrected for the mixture and for measurement error (register reliability ratios 0.95-0.96, falling to 0.88 within twin pairs).

All three causal designs come in below OLS, and the causal effect of parental schooling on child schooling is small. Swedish OLS baseline: 0.28 years per maternal year and 0.23 per paternal year, falling to 0.20 and 0.15 once spousal education is controlled (assortative mating). Twin-parent fixed effects: fathers positive and significant, mothers near zero; corrected for the DZ/MZ mixture and measurement error, mothers -0.001 (SE 0.065) and fathers 0.120 (SE 0.069). Adoptees: foreign-born 0.03-0.04, Korean adoptees 0.01-0.03 and never significant, Swedish-born adoptees 0.07-0.11 for mothers and 0.03-0.08 for fathers. IV (compulsory schooling reform): only mothers matter, 0.06 in the sample restricted like Black-Devereux-Salvanes, larger when the restriction is relaxed, and fathers never transmit. The three methods disagree about WHICH parent matters — twins and adoption point to fathers, IV points to mothers — and the authors do not resolve it. What they do resolve is the magnitude: "intergenerational schooling associations are largely driven by selection. Parental schooling constitutes a large part of the parental nurture effect, but as a whole does not play a large role." That last clause is the finding an evidence archive should carry: parental schooling is most of what "parental nurture" turns out to be, and parental nurture is not much.

This is a paper about the genetic confound. Each design attacks it differently: twin-parent differencing removes shared genes and rearing endowments but assumes twins differ ONLY in schooling (Griliches; Bound & Solon show twin-FE bias can exceed OLS bias); adoption removes transmitted genes but is exposed to selective placement; IV removes both in principle but estimates a LATE for compliers at the bottom of the education distribution. The authors note that only the IV fully accounts for inherited abilities and child-rearing endowments in theory. The consistent answer across three different confound-removal strategies — estimates fall to between a fifth and a half of OLS — is stronger than any one of them.

This IS the replication study — it reproduces the twin literature (father-positive, mother-null, as in Behrman & Rosenzweig 2002), the adoption literature (small positive effects, as in Plug 2004 and Sacerdote 2007), and the IV literature (mother-positive, father-null, as in Black, Devereux & Salvanes 2005) on one dataset, and shows the choice of identification strategy is what generates the disagreement. It also does the external-validity work: applying the twin design to low-skilled twins to see whether the IV's complier population explains the divergence, which it does only partly.