Instrumental Variable Estimation

Instrumental Variable Estimation is a family of statistical methods for estimating the causal effect of an exposure on an outcome when the exposure is correlated with unmeasured determinants of the outcome. The approach uses a third variable, the instrument, that influences the exposure, is unrelated to the confounders, and has no path to the outcome except through the exposure. The method originated in econometrics in the 1920s, in work on estimating supply and demand curves, and entered epidemiology later as researchers sought alternatives to adjustment for measured covariates, which cannot address confounders no one recorded. Its appeal is that a valid instrument acts as a natural randomization device. Its difficulty is that validity cannot be verified from data alone.

Let Z denote the instrument, A the exposure, Y the outcome, and U the set of unmeasured confounders. A valid instrument satisfies three conditions.

1. Relevance. Z is associated with A. This is testable, and its strength is usually quantified by the F-statistic from the regression of A on Z.
2. Independence (exchangeability). Z shares no common causes with Y, so Z is as good as randomly assigned with respect to U. This is untestable but can be probed by checking balance of measured covariates across levels of Z.
3. Exclusion restriction. Z affects Y only through A. Any direct effect of Z on Y, or any path through a third variable, violates this condition.

These conditions identify a causal effect only when supplemented by a fourth, parametric or structural assumption. The commonly used choices are constant treatment effects, which let the instrument identify the average effect for everyone, and monotonicity, which identifies a local effect described below. A randomized controlled trial with imperfect compliance is the cleanest example: random assignment is the instrument, treatment actually received is the exposure, and assignment is independent of confounders by design, though the exclusion restriction may still fail when assignment alters behavior through channels other than treatment, such as unblinded participants changing lifestyle.

With a binary instrument, the simplest estimator is the Wald ratio: the difference in mean outcome between instrument groups divided by the difference in mean exposure between the groups,

β_IV = (E[Y | Z = 1] − E[Y | Z = 0]) / (E[A | Z = 1] − E[A | Z = 0]).

The numerator is the effect of the instrument on the outcome, often called the reduced form, and the denominator is the effect of the instrument on the exposure, the first stage. The ratio rescales the effect of Z on Y to the effect of one unit of A on Y, under the assumption that all of Z's influence travels through A.

When there are several instruments or covariates, two-stage least squares (2SLS) generalizes the ratio. In the first stage, the exposure is regressed on the instruments and covariates, giving fitted values Â. In the second stage, the outcome is regressed on  and the same covariates. The coefficient on  is the 2SLS estimate. With one instrument and no covariates, 2SLS equals the Wald ratio. Standard errors must come from the 2SLS formula rather than from the second-stage regression output, since the latter ignores the uncertainty in the fitted values. With more instruments than exposures, the model is overidentified, and the Sargan or Hansen J statistic tests whether the instruments give consistent estimates, which detects some, but not all, exclusion violations, since a test of agreement cannot flag a defect shared by all instruments.

Imbens and Angrist in 1994 clarified what an instrument estimates when treatment effects vary across people. They divided the population into four latent groups defined by how the exposure responds to the instrument: compliers, who take the exposure only when Z = 1; always-takers, who take it regardless; never-takers, who never take it; and defiers, who take it only when Z = 0. Under independence, exclusion, relevance, and monotonicity, which rules out defiers, the Wald ratio equals the average causal effect among compliers, termed the local average treatment effect (LATE).

This result reframes the interpretation. The IV estimate is not the population average effect and may differ from the effect in always-takers or never-takers. Compliers cannot be identified individually, and different instruments define different complier groups, so two valid instruments can give different answers without either being wrong. For policy, LATE is relevant when the policy resembles the instrument, for instance a subsidy that changes uptake for marginal participants.

Economists have exploited circumstances that assign exposure through administrative rules or accidents of timing. Angrist and Krueger in 1991 used quarter of birth as an instrument for years of schooling. Compulsory attendance laws require students to stay in school until a given birthday, so children born early in the year can leave after completing slightly less schooling than children born late in the year. Quarter of birth is plausibly unrelated to ability or family background, so it shifts education while, the authors argued, leaving earnings otherwise unaffected. The study became the standard teaching example, and it also became the standard cautionary one: later analyses showed that when the instruments explain little of the variation in schooling, estimates are biased toward ordinary least squares and are sensitive to specification. Other natural-experiment instruments include draft lottery numbers, distance to a hospital or college, judge assignment, and physician prescribing preference, the last widely used in pharmacoepidemiology as a response to confounding by indication.

An instrument is weak when its association with the exposure is small. Three problems follow. First, the variance of the IV estimator increases sharply as the first-stage association approaches zero. Second, even a minor violation of the exclusion or independence condition is amplified by dividing by a small denominator, so bias from a tiny direct effect can exceed the confounding bias that IV set out to remove. Third, in finite samples the 2SLS estimator is biased toward the confounded ordinary estimate, and this bias grows with the number of instruments. Staiger and Stock in 1997 formalized asymptotics under weak instruments and showed that standard confidence intervals can have poor coverage. The conventional rule of thumb is a first-stage F-statistic above 10, and more robust approaches include limited-information maximum likelihood, Anderson–Rubin confidence sets, and conditional likelihood ratio tests, which maintain coverage regardless of instrument strength.

Hernán and Robins in 2006 reviewed the use of instruments in epidemiology and stressed that the three core conditions are not enough to point-identify the average causal effect without a further assumption, that IV bounds can be wide, and that investigators should state which additional assumption they are making. They also noted that a valid instrument can be drawn as a node in a causal diagram, which exposes violations: a path from Z to Y through a variable other than A breaks the exclusion restriction, and conditioning on a common effect of Z and U opens a path through collider bias. Related approaches in epidemiology that tackle unmeasured confounding by other routes include proximal causal inference and the g-computation formula, which require measured confounders, and propensity score matching, which does not address unmeasured ones.

Mendelian randomization uses genetic variants as instruments. Alleles are assigned at conception by random segregation, so they are plausibly independent of later-life behaviors and social circumstances, and they cannot be changed by the outcome, which removes reverse causation. A variant associated with a biomarker such as circulating lipids serves as an instrument for the effect of the biomarker on disease. The Wald ratio becomes the ratio of the variant–outcome and variant–exposure associations, usually taken from separate genome-wide association studies, and multiple variants are combined by inverse-variance weighting. The central threat is horizontal pleiotropy, in which a variant influences the outcome through a pathway other than the exposure, violating exclusion. Methods such as MR-Egger regression and median-based estimators relax this assumption under specified patterns of pleiotropy. Population stratification and linkage disequilibrium with causal variants for other traits threaten independence, so analyses control for ancestry and prefer variants with biological justification.

Applied IV work should report the first-stage F-statistic, the reduced-form estimate, and the 2SLS or Wald estimate with weak-instrument-robust intervals. It should argue the exclusion restriction on substantive grounds, since no test establishes it, and state the target of inference, either a constant effect or a complier effect. Comparing the IV estimate with the ordinary regression estimate is informative only when the difference is judged against the much larger IV variance. Sensitivity analyses that quantify how large a direct effect of Z on Y would be needed to overturn conclusions help readers judge credibility.

1. Imbens GW, Angrist JD. Identification and estimation of local average treatment effects. Econometrica. 1994;62(2):467–475. https://doi.org/10.2307/2951620
2. Angrist JD, Krueger AB. Does compulsory school attendance affect schooling and earnings? Quarterly Journal of Economics. 1991;106(4):979–1014. https://doi.org/10.2307/2937954
3. Staiger D, Stock JH. Instrumental variables regression with weak instruments. Econometrica. 1997;65(3):557–586. https://doi.org/10.2307/2171753
4. Hernán MA, Robins JM. Instruments for causal inference: an epidemiologist's dream? Epidemiology. 2006;17(4):360–372. https://pubmed.ncbi.nlm.nih.gov/16755261/