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Instrumental variable (IV) analysis estimates a causal effect when the regressor of interest is endogenous — correlated with the structural error term because of omitted confounders, reverse causation, or measurement error — so ordinary least squares (OLS) is biased and inconsistent no matter how much data you collect. See endogeneity: the three sources and the remedy that matches each for how IV fits alongside fixed effects and measurement models as one of several remedies. IV works by finding a variable, the instrument, that moves the endogenous regressor without having any effect on the outcome except through that regressor. Whether that actually holds is the whole game: two of the three IV assumptions below are not verifiable from data, and the one that is verifiable — instrument relevance — has its own well-known failure mode, the weak instrument, which this guide diagnoses with the first-stage F-statistic.
The three IV assumptions
Every IV estimate rests on three conditions holding simultaneously. Two are structural claims about the world that no dataset can confirm; only the third is directly testable.
1. Relevance
The instrument z must be correlated with the endogenous regressor x, conditional on any included controls. Formally, the first-stage coefficient on z is non-zero. This is the one assumption you can actually test — run the first-stage regression of x on z (and controls) and check whether z‘s coefficient is statistically and practically distinguishable from zero. A weak first-stage relationship doesn’t just cost precision the way it would in an OLS regression; it changes the entire sampling behavior of the second-stage estimator, which is the subject of the F-statistic section below.
What violates it: an instrument chosen for its intuitive story rather than a demonstrated first-stage relationship; an instrument that shifts x only weakly, or only for a small subpopulation (Google Trends-derived measures, distance-to-facility measures with little variation, or lagged values of a slow-moving series are common culprits).
2. Exclusion restriction
The instrument affects the outcome y only through its effect on x — no direct path, and no path through some other channel correlated with y. This is a structural claim about the causal graph, not a statistical property of the sample, and it is not testable from the data you have. Overidentification tests (Sargan, Hansen J) are sometimes offered as a check, but they only test whether multiple instruments produce mutually consistent estimates conditional on at least one of them already being valid — a set of instruments that are all invalid in the same direction passes cleanly, and the test has no power to catch that. With a single instrument (the exactly-identified case), there is no overidentification test available at all.
What violates it: the instrument affects the outcome through a second channel you didn’t model. Classic example debates: rainfall as an instrument for economic growth (also affects agricultural output and conflict directly), or a policy rollout used as an instrument for program participation when the policy itself changed other things at the same time. Defending the exclusion restriction is an argument, made with domain knowledge and institutional detail, not a statistic you can report.
3. Exogeneity (instrument independence)
The instrument must be as good as randomly assigned with respect to the structural error — uncorrelated with the unobserved determinants of y other than through x. This is closely related to the exclusion restriction but distinct: exclusion is about the causal pathway, exogeneity is about whether the instrument itself is correlated with omitted confounders. Like exclusion, it is not directly testable; it is supported by the same kind of institutional argument (a policy discontinuity, a natural experiment, an administrative rule that assigns the instrument’s value for reasons unrelated to the outcome).
What violates it: an instrument that is itself a choice made by the same optimizing agents whose behavior generates y (e.g., using a firm’s own R&D history as an instrument for a firm decision, when both are driven by the same unobserved firm quality). See natural experiments: how to argue a shock is genuinely exogenous for the argument structure reviewers expect when defending this assumption for a specific instrument.
2SLS: the estimation mechanics
Two-stage least squares (2SLS) is the standard way to compute an IV estimate when you have one endogenous regressor and one or more instruments.
- First stage. Regress the endogenous regressor x on the instrument(s) z and any exogenous controls. Save the fitted values, x̂ — this is the part of x‘s variation that is explained by the instrument, which by construction is uncorrelated with the structural error (assuming the three assumptions hold).
- Second stage. Regress the outcome y on the fitted values x̂ (and the same controls). The coefficient on x̂ is the 2SLS estimate.
A frequent implementation trap: running these two OLS regressions manually, by hand, in two separate steps, produces the correct point estimate but the wrong standard error — the second-stage regression doesn’t know that x̂ is itself an estimated quantity, so its reported SE understates the true sampling uncertainty. Dedicated IV routines (ivreg2 in Stata, ivreg/AER::ivreg in R, linearmodels.IV2SLS in Python) compute the correct SE directly; manual two-step 2SLS should be treated as a teaching device, not a production estimator.
With exactly one instrument for one endogenous regressor (the exactly-identified case), 2SLS is numerically identical to the simpler ratio estimator: the reduced-form coefficient of y on z, divided by the first-stage coefficient of x on z. That ratio structure is exactly why a first-stage coefficient near zero causes trouble — you are dividing by a number that is itself imprecisely estimated and close to zero.
The first-stage F-statistic and the weak-instrument problem
Because 2SLS is a ratio estimator, its sampling behavior degrades sharply as the first-stage relationship weakens — not gracefully, the way OLS precision degrades with a noisy regressor, but qualitatively: bias, and a sampling distribution that stops looking normal. The standard diagnostic is the first-stage F-statistic, the F-test on the instrument(s)’ coefficient(s) in the first-stage regression.
The familiar F > 10 rule of thumb traces to Staiger and Stock (1997, Econometrica 65(3)) and was formalized into instrument-count- and tolerance-specific critical values by Stock and Yogo (2005, in Identification and Inference for Econometric Models, Cambridge University Press). It is a rule of thumb, not a hard threshold, and it has aged less well than its ubiquity suggests: Lee, McCrary, Moreira and Porter, “Valid t-Ratio Inference for IV” (American Economic Review 112(10), October 2022, pp. 3260–90), show that treating F > 10 as sufficient for standard 2SLS inference is anti-conservative — a genuinely valid 5% test requires F > 104.7, not 10, and holding onto 10 as a threshold means replacing the conventional critical value of 1.96 with 3.43. Auditing published work, they found 61 papers in top-tier AER issues where the corrected standard errors were at least 49% larger (at the 5% level) and 136% larger (at the 1% level) than the conventional 2SLS SEs for a quarter of specifications. F > 10 is a useful screening heuristic for spotting an obviously weak instrument; it is not a license to trust the usual t-ratio once you clear it.
Why a weak instrument biases toward OLS
As the first-stage relationship weakens, the 2SLS estimate’s finite-sample distribution shifts toward the OLS estimate — the very estimate IV exists to correct. Intuitively: with a near-zero first-stage coefficient, the fitted values x̂ used in the second stage are dominated by first-stage estimation noise rather than genuine instrument-driven variation in x, so 2SLS starts behaving like a regression of y on a noisy proxy for x — which is closer to what OLS is already doing. In the limit of a completely irrelevant instrument, 2SLS is not defined (you’d be dividing by a first-stage coefficient of exactly zero); just short of that limit, its distribution becomes erratic, non-normal, and can have no finite mean at all in the simplest single-instrument case — which is exactly what the simulation below shows.
A reproducible simulation: strong, borderline, and weak instruments
To make the F-statistic/bias relationship concrete rather than asserted, here is a small Monte Carlo simulation, run with a fixed seed so the numbers are exactly reproducible (deterministic PRNG, no external packages, n = 500, 4,000 replications per scenario). The data-generating process: x = πz + v, y = 2.0·x + u, where u and v share a correlation of 0.6 — the source of x‘s endogeneity — and the instrument’s strength is controlled by π. The true effect is fixed at 2.0 in every scenario.
Because the weak-instrument sampling distribution is heavy-tailed (as the theory above predicts), the simulation’s mean is itself unstable and misleading in the weak case — the table reports the median 2SLS estimate across replications, which is the well-behaved summary statistic here.
| Scenario | π (instrument strength) | Median first-stage F | Median 2SLS estimate | 2SLS bias | OLS bias (same data) |
|---|---|---|---|---|---|
| Strong instrument | 0.80 | 319.5 | 2.001 | +0.001 | +0.366 |
| Near the F > 10 threshold | 0.135 | 8.8 | 1.978 | −0.022 | +0.589 |
| Weak instrument | 0.05 | 1.3 | 2.195 | +0.195 | +0.599 |
Read across the rows: OLS is biased by roughly the same amount throughout (around +0.37 to +0.60, since the underlying endogeneity in the data doesn’t change) — that bias is what IV exists to remove. With a strong instrument (F ≈ 320), 2SLS removes essentially all of it. Right around the F > 10 rule of thumb, 2SLS is still close to unbiased at the median (−0.022). Once the instrument is genuinely weak (F ≈ 1.3), the median 2SLS bias climbs to +0.195 — about a third of the distance from the true effect toward the OLS estimate, confirming the bias-toward-OLS direction predicted by the theory, even though the F-statistic here would clearly fail the F > 10 screen and no one should be reporting this estimate as reliable in the first place.
What to do about a weak instrument
- Report the first-stage F, always — not just the second-stage results. A 2SLS table with no first-stage diagnostics is incomplete regardless of how clean the second-stage coefficient looks.
- Use Anderson-Rubin confidence intervals instead of the conventional 2SLS t-ratio when the first-stage F is low or borderline. Anderson-Rubin inference stays valid under weak identification because it doesn’t rely on the same asymptotic normality that breaks down in the simulation above; the conventional t-ratio does not have that property.
- Don’t “fix” a weak instrument by adding more instruments. Each additional weak instrument adds estimation noise to the first stage without adding much genuine explanatory power, and can worsen finite-sample bias (the many-weak-instruments problem) rather than improve it.
- Reconsider whether IV is the right tool at all. If no instrument in hand clears a reasonable relevance bar, a design-based alternative — regression discontinuity, difference-in-differences, or a fixed-effects specification (see the Hausman test for choosing between fixed and random effects) — may identify a credible, if narrower, causal quantity without leaning on a shaky instrument.
Frequently asked questions
What makes an instrument “weak” rather than just imprecise?
Weakness is about the strength of the first-stage relationship between the instrument and the endogenous regressor, not about sample size or the precision of the second-stage estimate directly. A weak instrument can occur in a very large sample; it just means the instrument barely moves the regressor it’s supposed to instrument for, so the ratio structure underlying 2SLS becomes unstable regardless of how much data you have.
Can I test the exclusion restriction statistically?
Not directly. With a single instrument there is no statistical test at all — it has to be argued from institutional knowledge of how the instrument could plausibly affect the outcome. With multiple instruments, overidentification tests (Sargan, Hansen J) can flag mutual inconsistency among the instruments, but they assume at least one instrument is already valid and have no power against instruments that are all invalid in a correlated direction.
Is a higher first-stage F always better?
Directionally yes, but F > 10 is a screening heuristic, not a guarantee of valid inference at conventional confidence levels — recent work shows a true 5% test requires F well above 100 if you insist on using the conventional critical value. Report the F-statistic, and prefer weak-instrument-robust inference (Anderson-Rubin) over the conventional t-ratio whenever F is anywhere near the borderline.
Does 2SLS require the outcome and the endogenous regressor to be continuous?
2SLS itself is a linear estimator and works with continuous, binary, or count outcomes as a linear probability-style approximation, but a binary endogenous regressor or nonlinear second stage (e.g., IV-probit) usually calls for a control-function approach instead — numerically identical to 2SLS in a fully linear model, but the more general tool when either stage is nonlinear.
For background on when endogeneity arises in the first place and which remedy fits which source, see endogeneity: the three sources and the remedy that matches each. IV sits alongside regression discontinuity design, difference-in-differences, and propensity score matching as one of several strategies for approximating a causal comparison without full randomization — see the causal analysis overview for how these fit together.
