Why the Apple Doesn’t Fall Far: Understanding Intergenerational Transmission of Human Capital

Norwegian register data — 286,137 mother-child pairs and 228,060 father-child pairs in the full sample; 63,269 and 43,407 in the low-education restricted sample

Norwegian children aged 20-35 matched to parents via the 1960 census, with parental education instrumented by the staggered municipality-level rollout of the 1960s compulsory schooling reform (7 to 9 mandatory years).

American Economic Review 95(1), 437-449. The canonical instrumental-variables answer to "does educating the parent educate the child". Identification comes from Norwegian municipalities adopting the 9-year compulsory schooling reform in different years, which is exogenous to family ability. Education data are administrative register records, so measurement error — the usual reason IV exceeds OLS — is close to zero here, which the authors use to explain why their IV estimates come in BELOW OLS rather than above. NUMBERS BELOW ARE READ FROM NBER WORKING PAPER 10066 (October 2003), not the published AER text; Holmlund, Lindahl & Plug 2011 summarize the published restricted-sample maternal effect as ~0.12 years, close to but not identical with the working paper's mother-son coefficient. The instrument only has bite at the bottom of the education distribution (7 to 9 years), which is the estimate's main external-validity limit.

The correlation between parents' and children's education is almost entirely selection. OLS says an extra year of parental education is worth about 0.15 extra years for the child, consistently across all four parent-child sex pairings. In the full sample every 2SLS estimate is statistically insignificant, and the standard errors are wide enough to be uninformative. In the low-education sample where the instrument actually bites, the 2SLS estimates are precise and universally smaller than OLS: fathers are close to zero and insignificant across the board, and the only surviving effect is mothers on sons (0.1051, SE 0.0388) and mothers overall (0.0786, SE 0.0316) — mothers on daughters is null (0.0480, SE 0.0444). The authors' summary is that "the true causal effect of parental education on child education appears to be weak" and that the high correlations are "due primarily to family characteristics and inherited ability and not education spillovers". For an archive premised on heritability, this is the load-bearing result on parental education as an input: the observational gradient shrinks by roughly half to nothing when the parent's schooling is moved exogenously.

This paper is the instrument for measuring the genetic confound, not a victim of it. The reform shifts parental schooling without shifting parental genotype, so the gap between the OLS 0.15 and the IV 0.00-0.10 IS an estimate of how much of the observed intergenerational education gradient is selection and inherited ability. The residual caveat is LATE: the compliers are people at the very bottom of the Norwegian education distribution in the 1960s, so the estimate need not generalize to marginal changes higher up.

Replicated on Swedish register data by Holmlund, Lindahl & Plug 2011, who apply twin, adoption and IV designs to the same population and reproduce this paper's pattern almost exactly with their IV strategy (maternal effect ~0.06 in the comparable restricted sample, paternal effect zero) — and who state that of all the IV studies they review they "are inclined to take the results of BDS most seriously". The direction also converges with the twin literature (Behrman & Rosenzweig 2002) and the adoption literature (Sacerdote 2007, already in this archive), although the three methods disagree about WHICH parent matters.