Instrumental Variables
Exclusion restriction, weak instruments, 2SLS, LATE
Does education increase earnings? The confound is ability. Smart people get more education and earn more regardless of education level — so any observed correlation between education and earnings contains both the causal effect of education and a spurious component from ability. You need variation in education that is unrelated to ability. A valid instrument: distance from college. Students born close to a college are more likely to attend (the instrument predicts treatment). But distance from college affects earnings only through education — it does not directly affect a person's earnings potential except by influencing whether they went to college (exclusion restriction). This isolates variation in education driven only by geography, not ability.
An instrumental variable Z requires three conditions. Relevance: Z is correlated with the treatment T. Distance predicts college attendance — testable with the first-stage F-statistic. Exclusion restriction: Z affects the outcome Y only through T, not through any other path. Distance does not directly affect earnings except by influencing education — this is argued on subject-matter grounds, not verified statistically. Independence: Z is uncorrelated with T-Y confounders. Where you were born was not chosen based on your cognitive ability.
Two-Stage Least Squares (2SLS) operationalizes this. Stage 1: regress T on Z and controls, get fitted values T̂. Because controls are included in that first-stage regression too, T̂ captures variation in T explained by both Z and the controls — what makes T̂ usable for identifying the causal effect is not that controls are absent, but that Z's coefficient isolates the variation in T driven by the instrument rather than by confounders. Stage 2: regress Y on T̂ and the same controls used in stage 1. The first stage extracts the Z-driven variation in T net of those controls; the second stage estimates the causal effect of that variation on Y.
IV estimates the Local Average Treatment Effect (LATE): the causal effect for compliers — units whose treatment status changes in response to the instrument. Non-compliers are excluded: always-takers are units that take the treatment regardless of what the instrument assigns, and never-takers are units that never take the treatment regardless of what the instrument assigns — since neither group's behavior responds to Z, the instrument carries no information about the effect on them. The LATE is not the ATE — it is the treatment effect for a specific subpopulation defined by the instrument.
What this is not: any variable correlated with treatment is a valid instrument. The exclusion restriction is almost never testable. A weak instrument (first-stage F < 10) produces estimates with enormous variance and finite-sample bias toward OLS that defeats the purpose of the IV approach entirely. A good instrument is extremely hard to find — this is why natural experiments are so valuable in applied causal inference.
Key points
- Always report the first-stage F-statistic — F < 10 indicates a weak instrument that biases IV estimates toward OLS. The Stock-Yogo weak instrument test gives formal critical values. Weak instruments are the most common failure mode in applied IV. A weak instrument does not just widen the confidence interval — it also biases the point estimate itself back toward OLS, so a low F-stat should be treated as disqualifying, not merely noted and proceeded past.
- Trap: the exclusion restriction is untestable and can be violated in subtle ways. For distance-as-instrument: distance might directly affect earnings through local labor market access, independent of education. Always think through every possible path from Z to Y and argue why each either does not exist or is controlled for. Stating the exclusion restriction holds "by assumption" is not a defense — it is a request for the reader to accept an unverified claim. One partial check: a placebo regression — regressing the instrument on an outcome it should have no effect on — flags a suspicious pathway if it comes back significant, though passing it never proves the exclusion restriction, since it only rules out the specific alternate outcomes you thought to test.
- Diagnostic: estimate the effect using IV and compare to OLS. If IV < OLS, the OLS confounder was upward-biasing the estimate (e.g., ability bias in the education example — smarter people get more schooling and earn more regardless of schooling, so OLS overstates the causal return). If IV > OLS instead, do not reach for a downward-biasing confounder by default — check complier heterogeneity first: IV estimates the LATE, and compliers induced by the instrument can have above-average returns, which is the standard explanation for IV>OLS in the schooling literature. If the estimates have opposite signs, there is a strong confound or a violated exclusion restriction — investigate before publishing. The direction of the OLS-IV gap is a useful diagnostic, but only pins down confounding direction cleanly when treatment effects are homogeneous.
IV trades the ignorability assumption for the exclusion restriction — both untestable — and estimates LATE for compliers only; a weak instrument adds enormous variance and biases the estimate toward OLS, defeating the purpose of the approach.
Recap
- IV isolates the variation in the treatment that's unrelated to the confounder: for education↔ability, distance-to-college shifts who attends but (arguably) not their innate ability, so 2SLS uses only the geography-driven variation in education to estimate its effect on earnings.
- Three conditions a valid instrument Z must meet: relevance (Z is correlated with T — testable via the first-stage F-statistic), exclusion (Z affects Y *only* through T, no other path), and independence (Z is uncorrelated with the T–Y confounders).
- 2SLS operationalises it in two stages: stage 1 regress T on Z and controls to get fitted T̂ (T̂'s useful part is the exogenous, instrument-driven variation, isolated via Z's coefficient — not the absence of controls); stage 2 regress Y on T̂ and those same controls — the effect of that clean variation on the outcome.
- IV estimates the LATE, not the ATE: it recovers the effect only for *compliers* — units whose treatment status actually flips in response to the instrument — excluding always-takers and never-takers, so it's a specific subpopulation's effect.
- A weak instrument (first-stage F < 10) defeats the whole method: it gives enormous variance *and* finite-sample bias back toward the OLS estimate you were trying to escape — the most common failure mode in applied IV (Stock-Yogo gives formal critical values).
- The exclusion restriction is almost never testable: you must reason through *every* path from Z to Y and argue each away on subject-matter grounds (e.g. distance affecting earnings via local labour markets) — "holds by assumption" is not a defence.
- Diagnostic — compare IV to OLS: IV < OLS points to an upward-biasing confounder (e.g. ability bias in the education example); IV > OLS is more often complier heterogeneity — IV estimates the LATE, and compliers can have above-average returns, not necessarily a downward-biasing confound; opposite signs ⇒ strong confound or a violated exclusion restriction — investigate before publishing.
Check your understanding
Q1. You want to estimate the causal effect of price increases on demand. Propose a valid instrument and explain how you would test its validity.
- A) Use lagged price as the instrument — the temporal ordering alone is treated as sufficient to guarantee the exclusion restriction, since a past price cannot literally be caused by current demand, only correlated with it
- B) Use input cost shocks, e.g. oil prices for airlines — they move prices, but consumers respond only to the ticket price. Test relevance via first-stage F>10 and exclusion via a mechanism argument plus a placebo regression
- C) Use competitor prices as the instrument — they move with own prices (relevance) and can't affect own-firm demand directly, since consumers are assumed to respond only to the firm's own posted price, never a rival's
- D) Use random price variation from an A/B pricing experiment as the instrument — experimental assignment is independent of demand by construction, so exclusion is guaranteed and no further testing is ever required
Q2. Your IV estimate of effect of education on earnings is 15% per year of schooling, but OLS estimate is 8%. Hausman test rejects exogeneity. Why might IV be higher than OLS?
- A) IV is higher because the instrument, college proximity, actually violates the exclusion restriction by directly raising earnings through better local labor market access, which inflates the 2SLS estimate above the truth
- B) IV is higher purely because of weak-instrument bias — a low first-stage F causes 2SLS to systematically overestimate the effect, and the Hausman rejection is itself read as confirmation of this upward bias
- C) IV and OLS should always converge as the sample grows arbitrarily large, so a persistent 15% vs 8% gap on its own is proof the instrument is invalid and the plain OLS estimate should be trusted instead
- D) IV estimates LATE for compliers — marginal students induced to attend by proximity, who may have higher returns than the always/never-takers OLS averages over, so IV>OLS suggests returns are higher at the margin
Q3. An economist uses distance to nearest abortion clinic as instrument for abortion rates, studying effect on child outcomes. What are the threats to the exclusion restriction?
- A) Distance must affect outcomes ONLY through abortion rates. Threats: geographic sorting on income/religion, rural healthcare access, urbanicity predicting outcomes via schools/labor markets — test with outcomes it shouldn't touch
- B) The dominant threat here is simply a weak first stage — distance may only weakly predict abortion rates, pushing the first-stage F below 10 and biasing the resulting IV estimate back toward the plain OLS estimate
- C) The exclusion restriction holds automatically as long as distance is measured at the time of pregnancy rather than during childhood, since that timing choice alone removes any direct channel to child outcomes
- D) The only real threat to the exclusion restriction here is reverse causality — families may relocate closer to a clinic after having children, generating a spurious correlation between distance and the outcome
Q4. What is the difference between LATE and ATE, and why does it matter for policy? Select the two true statements.
- A) ATE = E[Y(1)−Y(0)] over the full population, while LATE is the effect only for compliers — the subset whose treatment status actually changes in response to the instrument — so LATE ≠ ATE unless the treatment effect is homogeneous
- B) Citing a lottery-instrument LATE to justify a universal training mandate is an error, since the effect on never-takers (who wouldn't attend even if required) could be zero or negative even when LATE for lottery-induced compliers is positive
- C) LATE and ATE are numerically equivalent whenever the instrument is strong, i.e. first-stage F>10; the distinction between the two estimands only becomes relevant once the instrument is weak
- D) LATE should always be preferred over ATE for policy decisions, because it specifically captures the effect for the people most likely to respond to whatever intervention is ultimately rolled out
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