Instrumental Variables

When the Confounder Cannot Be Measured

Matching and propensity methods rest on unconfoundedness — that after conditioning on observed covariates, treatment is as good as random. Their fatal blind spot is the confounder you cannot measure. The textbook case is the return to schooling: people who choose more education differ in unobserved ability, motivation and family background, all of which also raise earnings. Ability sits in the error term, correlated with schooling, so an ordinary regression of wages on education is biased — and no amount of matching on observed covariates fixes it, because the problem is unobserved.

Instrumental variables attack exactly that. An instrument $Z$ is a source of variation in the treatment $D$ that is itself as good as randomly assigned, and it must satisfy two conditions: relevance, that $Z$ actually shifts the treatment, which is testable; and exclusion, that $Z$ affects the outcome only through $D$, which is not. That asymmetry is the whole character of IV work — the credible half is checkable and the load-bearing half is an argument.

Card (1995) studies 3,010 men from the U.S. National Longitudinal Survey of Young Men. The outcome is log hourly wage in 1976, the treatment is years of education, and the instrument is nearc4 — whether the respondent grew up near a four-year college. The logic is that proximity lowers the cost of attending, since you can live at home. Relevance holds and is easy to see: 13.53 years of schooling for those who grew up near a college against 12.70 for those who did not, a gap of 0.83 years.

Two-Stage Least Squares

Two-stage least squares regresses the endogenous treatment on the instrument and controls, keeps the fitted values — the part of schooling predicted by proximity, purged of the ability confounder — and regresses the outcome on those. In matrix form, with instrument matrix $Z$ and regressor matrix $X$:

The result is the famous Card finding, and it runs the wrong way for the textbook intuition: the IV return of 13.2% exceeds the OLS return of 7.5%. If unobserved ability inflated OLS, IV should have come in below it.

The notebook also reports the Wald ratio without controls at 0.188, against the controlled 2SLS estimate of 0.132. The gap is not rounding. Dropping experience, race, region and urban status moves the estimate by more than four percentage points, because proximity to a college is itself correlated with living somewhere urban where wages are higher. The exclusion restriction is doing conditional work — nearc4 is only plausibly excludable given those controls — and the distance between these two numbers measures how much rests on that conditioning.

What IV Actually Estimates

The resolution is the single most important idea in modern IV. With heterogeneous effects, 2SLS does not estimate the average treatment effect. Imbens & Angrist (1994) classify units by how they respond to the instrument: compliers take more schooling because a college was nearby, always-takers get it regardless, never-takers do not regardless, and defiers would do the opposite — assumed away by monotonicity. Under relevance, exclusion and monotonicity, IV identifies the Local Average Treatment Effect: the average effect for compliers alone.

That reframes the headline, and the size of the complier group is worth stating precisely because it is easy to overstate. At the binary margin the decomposition uses — crossing into college, $\text{educ} \ge 13$ — proximity raises the probability from 0.422 to 0.544. The compliers are 12.2% of the sample: roughly one man in eight.

At the college margin, proximity raises P(educ ≥ 13) from 0.422 to 0.544. The separate 0.83-year figure is the first stage measured on years of schooling — a different quantity, not a share.

So the 13% return is the average effect for one-eighth of this sample — the men whose college decision turned on how far away the campus was. It says nothing directly about the 42% who went regardless or the 46% who did not go either way. And it explains the puzzle: proximity mainly moves students who would otherwise stop early, plausibly the liquidity-constrained, whose return to education is high. The complier-weighted local effect exceeds the population average because the compliers are not a random slice of the population. Always ask whom the instrument moves.

Weak Instruments

IV's power is also its danger. If the instrument is only weakly relevant, 2SLS becomes badly biased toward OLS and its standard errors mislead — the cure becomes worse than the disease. The Bound, Jaeger & Baker (1995) critique of Angrist & Krueger's quarter-of-birth instrument is the cautionary tale: the first stage was so weak that estimates were driven by bias rather than signal, and comparable numbers could be produced from randomly generated instruments.

The first-stage $F$-statistic is the standard guard, with the Staiger–Stock rule of thumb demanding $F > 10$. Card's instrument clears it at 13.26 — adequate, but not comfortable. To make the pathology unmistakable the notebook runs a controlled simulation against a known effect of 0.5: as the instrument weakens and $F$ falls below roughly 10, the 2SLS estimate collapses from the truth back toward the confounded OLS value, with exploding variance.

Which is the sharpest practical warning in the subsection. A weak instrument is worse than no instrument, because it does not fail loudly — it returns a number, with a standard error, that looks like an answer.

Where this sits

IV picks up exactly where Potential Outcomes & Matching stops: matching adjusts for observed confounders, IV for unobserved ones, at the price of an untestable exclusion restriction and a local estimand. The complier and never-taker types are the same latent classes modelled explicitly in principal stratification, where the vitamin A trial's compliance types are estimated rather than assumed. The ratio-of-reduced-forms logic returns in regression discontinuity, where the instrument is landing just above a threshold.

Notebooks

Downloads

References

• Imbens, G. W. & Angrist, J. D. (1994). Identification and estimation of local average treatment effects. Econometrica. — the LATE theorem, and the compliers it is defined on
• Angrist, J. D. & Krueger, A. B. (1991). Does compulsory school attendance affect schooling and earnings?. Quarterly Journal of Economics. — the quarter-of-birth instrument
• Bound, J., Jaeger, D. A. & Baker, R. M. (1995). Problems with instrumental variables estimation when the correlation between the instruments and the endogenous explanatory variable is weak. Journal of the American Statistical Association. — the weak-instrument critique of that design
• Card, D. (1995). Using geographic variation in college proximity to estimate the return to schooling. Aspects of Labour Market Behaviour (eds. Christofides, Grant & Swidinsky). — the proximity instrument used here
• Staiger, D. & Stock, J. H. (1997). Instrumental variables regression with weak instruments. Econometrica. — where the first-stage F > 10 rule of thumb comes from
• Anderson, T. W. & Rubin, H. (1949). Estimation of the parameters of a single equation in a complete system of stochastic equations. Annals of Mathematical Statistics. — the AR confidence set, which stays valid however weak the instrument