Instrumental Variables Explained: Endogeneity, 2SLS and Weak Instruments

Understanding instrumental variables — simply put

A regression can confuse cause with coincidence when the explanatory variable is tangled up with something the data does not record. People who stay longer in school may earn more because of the schooling, or because the same ability and drive that kept them in school also raises their pay. An instrumental variable (IV) cuts through this. It is a third variable that pushes schooling up or down for reasons unrelated to ability, and affects earnings only through schooling. Comparing how much earnings move with the instrument to how much schooling moves with it isolates the causal effect that OLS regression cannot.

How does it actually help?

In April 1947, Britain raised the minimum school-leaving age from 14 to 15. Children born from 1933 onward had to stay an extra year; those born a year or two earlier did not. Whether a child was born in 1932 or 1933 has nothing to do with ability, yet it changed how long many of them stayed in school. That makes the reform an instrument. The model is ln w_i = β₀ + β₁S_i + u_i, where ln w_i is the log of person i's weekly earnings, S_i the age at which they left school, β₁ the percentage return to an extra year of schooling (multiplied by 100) and u_i everything else that affects pay, including ability. The instrument is Z_i, equal to 1 if person i was born in 1933 or later and 0 otherwise. If the reform raised schooling by half a year and earnings by 5%, the return to a full year is 5% divided by 0.5, or 10%.

Why does this matter?

Most questions economists care about involve variables that people, firms or governments choose, and choices are rarely random. Education and earnings, interest rates and inflation, aid and growth, police numbers and crime: in each case the explanatory variable responds to the very conditions that drive the outcome. Without a source of variation unrelated to those conditions, a regression measures association. Instrumental variables are the main tool for estimating cause and effect from observational data, and they underpin evidence used to set education policy, design taxes and evaluate public programs.

What makes an instrument reliable?

Two conditions do the work. The instrument must be relevant: it has to move the explanatory variable noticeably, which the data can check. It must also be excludable: it can affect the outcome only through that variable and must be unrelated to everything else in the error term. The data cannot check this; it rests on argument and institutional knowledge. A birth date that changed schooling by law is persuasive. A birth date that also coincided with a recession on leaving school would not be.

The takeaway

An instrument borrows the randomness of a natural experiment to estimate a causal effect when the variable of interest is chosen rather than assigned. The rest of this guide estimates the return to schooling from the 1947 reform, then sets out the assumptions and the mechanics of two-stage least squares.

A worked example: the return to schooling in Britain

The example uses 6,000 men born between 1928 and 1937, with the age at which each left school and his weekly earnings later in life. It is a teaching sample built to resemble British survey data around the 1947 reform: before the reform, a little under 60% of each cohort left school at 14. Every statistic below is computed exactly from it.

The break is sharp. Between the 1932 and 1933 cohorts, the share leaving at 14 drops from 57% to zero, average schooling jumps by more than half a year, and average earnings rise. Nothing about ability changed between children born a few months apart, so the jump in earnings can be attributed to the jump in schooling.

OLS says each year of schooling raises pay by 17.7%, and with a standard error of 0.006 it looks very precise. It is precisely wrong. The first stage shows the reform raised schooling by 0.57 years, and its F-statistic of 199 means the instrument is strong. The reduced form shows the reform cohorts earned 5.6% more. Dividing the second by the first gives 0.056 / 0.569 = 0.099: a return of 9.9% a year. That is the 2SLS estimate, and it sits close to the 10% the sample was built with. OLS overstated the return by almost eight points because the more able stayed in school longer and earned more for reasons of their own.

The price of consistency is precision. The 2SLS standard error is 0.034, more than five times the OLS one, because only the part of schooling driven by the reform is used. A Durbin–Wu–Hausman test comparing the two estimates rejects the hypothesis that schooling is exogenous (p = 0.017), so the loss of precision is worth paying. With a random subsample of 300 men, the same design gives a first-stage F of 25 and a 2SLS estimate of 0.046 with a standard error of 0.105. The estimate is still centered sensibly, but its 95% interval runs from about −16% to +25% and is uninformative. IV needs large samples.

The estimate has a specific meaning. The reform changed behavior only for boys who would otherwise have left at 14. Those who planned to stay on anyway were unaffected. The 2SLS estimate is therefore a local average treatment effect (LATE): the return to an extra year for the compliers, those whose schooling the instrument changed. It need not equal the return for someone deciding whether to complete a university degree.

Real data on this reform tell a less tidy story than the teaching sample. Philip Oreopoulos (2006), using British survey data, estimated returns of around 10% or more from this reform, close to or above the OLS estimate, and a later re-analysis by Devereux and Hart (2010) found smaller returns. The size of the true return remains debated. The method itself is not in question; the debate is about data, controls and which cohorts to compare.

The assumptions

• Relevance. The instrument must be correlated with the endogenous variable, Cov(Z, X) ≠ 0. The IV estimator divides by this covariance. When it is small, any small correlation between Z and the error is magnified, and the estimate is biased toward OLS and badly approximated by its usual standard error. A first-stage F-statistic well above 10 is the conventional minimum.
• Independence. The instrument must be as good as randomly assigned, unrelated to the unobserved factors in u. The numerator of the IV estimator, Cov(Z, Y), then reflects only the effect running through X. If Z is correlated with ability, for example because families timed births around the reform, that correlation leaks into the estimate. Controlling for a smooth birth-year trend guards against slow cohort differences.
• Exclusion. The instrument must affect the outcome only through the endogenous variable. If the reform also changed earnings in other ways, for instance because the extra year delayed entry into the labor market during a boom, the reduced form would mix that effect with the effect of schooling, and dividing by the first stage would attribute all of it to schooling. Exclusion cannot be tested with a single instrument; it has to be argued.
• Monotonicity. The instrument must push everyone in the same direction, or not at all. No one may leave school earlier because of the reform. Without monotonicity, people moved in opposite directions can cancel out, and the IV estimate no longer equals an average effect for any well-defined group.

The formula

This section sets out the estimators formally. Readers who need only the intuition can skip to the limitations. Start with the structural equation and the source of the problem:

With a single instrument, the IV estimator replaces the variance of X with its covariance with Z:

When Z is binary, this reduces to the Wald estimator: the difference in average outcomes between the two instrument groups divided by the difference in average treatment.

With control variables W and possibly several instruments, two-stage least squares (2SLS) runs the two stages in sequence. The first stage regresses X on all instruments and controls; the second regresses Y on the fitted values X̂ and the controls:

In matrix form, with X the n × k matrix of regressors (endogenous and exogenous) and Z the n × m matrix of instruments and exogenous controls, m ≥ k:

Instrument strength is judged by the first-stage F-statistic on the excluded instruments. The long-standing rule of thumb from Staiger and Stock requires F > 10. More recent work by Lee, McCrary, Moreira and Porter (2022) shows that a conventional 5% t-test on the 2SLS estimate is only reliable with F above about 104, or with adjusted critical values, so an F of 199 as in the example clears both bars. The Durbin–Wu–Hausman test compares OLS and 2SLS; a significant difference indicates that X is endogenous and OLS should not be used.

When instrumental variables aren't the right tool

• No credible instrument. IV is only as good as the exclusion argument. A weak or invalid instrument can give an answer further from the truth than OLS, with wider error bands that make it look cautious. If no variable plausibly satisfies exclusion, a different design is safer.
• Confounders that do not change over time. When the same units are observed repeatedly and the confounder is fixed, such as innate ability across a worker's career, panel data with fixed effects removes it without an instrument.
• A policy that reached some groups and not others. When the question is the effect of the policy itself rather than of the variable it shifts, difference-in-differences compares treated and untreated groups before and after, and its parallel-trends assumption is easier to inspect.
• Effects for the whole population. IV identifies the effect for compliers only. If policy needs the average effect for everyone, or for a group the instrument never moved, the IV estimate has to be combined with other evidence or a model of who responds.

The takeaway

Report the first stage, the reduced form and the 2SLS estimate together, and show the first-stage F. Argue exclusion with institutional detail, because no test will do it for you. Read the result as the effect for the people the instrument moved, and expect wider standard errors than OLS: that is the cost of an answer that can be trusted.

Further reading

• Understanding OLS Regression — internal
• Panel Data Explained — internal
• Difference-in-Differences Explained — internal
• UK legislation: Education Act 1944 (raised the leaving age to 15 from 1947) — external reference
• Office for National Statistics: earnings and working hours — external reference

Data note: the worked example is a teaching sample constructed by EconoLens to resemble British survey data around the 1947 school-leaving-age reform introduced under the Education Act 1944. The figures are illustrative, not survey records; the published studies cited above use real British survey data. All estimates were computed by EconoLens.