Endogeneity: The Three Sources, and the Remedy That Matches Each

Endogeneity is not one problem. It is a label for three structurally different failures that happen to break the same assumption, and the remedy that fixes one does nothing for the other two. Treating it as a single undifferentiated flaw is why so many papers reach for an instrumental variable when a fixed-effects specification or a measurement model would have answered the question — and why so many instruments turn out, on inspection, not to be instruments at all.

This guide separates the three sources — omitted-variable bias, simultaneity and reverse causation, and measurement error — and matches each to the remedies that actually address it, with the assumption each remedy buys on credit. It also names the remedies that look like they help and do not.

The condition that is actually being violated

In the linear model y = β₀ + β₁x + u, ordinary least squares recovers β₁ consistently only if the regressor is uncorrelated with the error term: Cov(x, u) = 0, or in the stronger conditional-mean form, E[u | x] = 0. A regressor is endogenous when that fails — when part of what the model treats as unexplained noise is in fact systematically related to the variable whose effect you are trying to measure. “Endogenous” is a statement about where the variable is determined: inside the system you are modelling, rather than outside it.

Two consequences follow, and both are routinely understated:

• The estimator is inconsistent, not merely imprecise. The bias does not shrink as the sample grows. A larger dataset converges on the wrong number with a narrower confidence interval around it, which is strictly worse than a small biased sample, because it looks more convincing.
• Robust or clustered standard errors do not help. They correct inference about a quantity the estimator is not consistently estimating. This is a different failure class from the assumption checks most researchers run — see the assumptions behind regression analysis and reading a residual plot. Heteroscedasticity, non-normal residuals and endogeneity are three unrelated diagnoses; passing the first two tells you nothing about the third.

The practical question is never “is there endogeneity?” in the abstract. It is which of the three sources is generating it, because that is the only thing that determines what you should do next.

Source 1: omitted-variable bias

Suppose the true relationship is y = β₀ + β₁x + β₂w + ε, and you estimate a regression that leaves out w. Then w is absorbed into the error term, and if x and w are correlated, the regressor is now correlated with the error. The probability limit of the short-regression coefficient is:

plim(beta1_hat) = beta1 + beta2 * Cov(x, w) / Var(x)

The second term is the bias. Its sign is the product of two signs: the effect of the confounder on the outcome, and the correlation between the confounder and your regressor.

Effect of omitted w on y	Correlation of w with x	Direction of bias in β1
Positive	Positive	Upward — overstates a positive effect
Positive	Negative	Downward
Negative	Positive	Downward
Negative	Negative	Upward

This table is the most useful thing in this section, because you can very often sign the bias even when you cannot remove it. If your estimate is positive and you can argue the bias is upward, your estimate is an upper bound and the qualitative finding is not safe. If you can argue the bias is downward, your positive estimate is a conservative lower bound and the finding survives. That reasoning belongs in the limitations section, stated explicitly, rather than in a generic sentence about unobserved confounding.

What the bias actually looks like

Prose understates how large this gets. The following simulation was run in R 4.6.1 with set.seed(20260826); the true effect of x on y is exactly 1.0 in every part.

set.seed(20260826)
n <- 5000
u <- rnorm(n)                    # confounder, never observed
x <- 0.6 * u + rnorm(n)          # x is correlated with u
y <- 1.0 * x + 2.0 * u + rnorm(n)

coef(lm(y ~ x))[["x"]]           # u omitted
coef(lm(y ~ x + u))[["x"]]       # u controlled (infeasible in practice)
1.0 + 2.0 * (cov(x, u) / var(x)) # the formula above

A. OMITTED-VARIABLE BIAS
   OLS omitting u        : 1.908
   predicted by formula  : 1.894
   OLS controlling for u : 1.026

The estimate is not off by a few percent. It is nearly double the truth, and it is not noise — the algebraic prediction (1.894) lands almost exactly on the simulated result (1.908). Nothing in the regression output flags this. R-squared is fine, residuals are well behaved, the coefficient is significant at any conventional level. Endogeneity is silent by construction: the diagnostic that would reveal it requires the variable you do not have.

Distinguishing this from a spurious relationship

When the omitted variable drives both x and y and x has no effect at all, you have a spurious correlation rather than a biased estimate of a real effect — the same mechanism, at the limiting case β₁ = 0. The broader framing of what it takes to move from association to effect is covered in causal analysis and in correlation versus causation.

Source 2: simultaneity and reverse causation

Here nothing is omitted. The problem is that y and x are determined jointly, so x is not a fixed input to the equation you wrote — it responds to the same shocks. Write the system out:

y = a1 * x + u        (the equation you care about)
x = a2 * y + v        (the feedback you ignored)

Solving for the reduced form makes the failure mechanical: x depends on u, so Cov(x, u) ≠ 0 by construction, with no unmeasured third variable anywhere in the story. Collecting more covariates cannot help, because there is no missing covariate.

Reverse causation is the limiting case where a₁ is essentially zero and the arrow runs entirely the other way. In practice the two are hard to separate and the remedy set is the same. What distinguishes simultaneity from omitted-variable bias operationally is the diagnosis: ask whether the value of x for a given unit would have been different had y come out differently. If yes, you have simultaneity, and the fix has to break the feedback loop — either with an instrument that shifts one equation and not the other, or with a design that fixes the timing so that x is determined before y can influence it.

Timing-based fixes are weaker than they look. Lagging the regressor is the most common false remedy for simultaneity. A lagged x is exogenous only if the confounding process is not serially correlated — and confounders in observational data almost always are. A lag buys the appearance of temporal precedence without the identification. Genuine design-based timing — a policy discontinuity, a staggered rollout, an explicitly emulated protocol such as target trial emulation — is a different and much stronger claim.

Source 3: measurement error

The third source is the one most often missed, because it does not feel like a confounding story at all. If you observe x_obs = x* + e where x* is the truth and e is classical error (independent of x* and of the equation error), the observed regressor carries the error into the composite error term, and OLS attenuates the coefficient toward zero by the reliability ratio:

plim(beta_hat) = beta * Var(x*) / (Var(x*) + Var(e))

From the same seeded simulation, with a true coefficient of 1.0 and measurement noise of standard deviation 0.8:

B. CLASSICAL MEASUREMENT ERROR IN x
   OLS on mismeasured x  : 0.601
   reliability ratio     : 0.609
   beta x reliability    : 0.609

A real effect of 1.0 is reported as 0.6. Note what this means for interpretation: attenuation makes a null result untrustworthy in a way that a positive result is not. If you found nothing, classical measurement error is a live explanation. If you found something despite it, the true effect is at least as large.

Four properties of measurement error are load-bearing and routinely got wrong:

• Classical measurement error in the dependent variable does not bias the coefficient. It enlarges the residual variance and widens standard errors, nothing more. Mismeasuring y is an efficiency problem; mismeasuring x is an identification problem. These are not symmetric, and treating them as equally alarming misallocates effort.
• With several regressors, mismeasuring one contaminates the others. The attenuation on the mismeasured variable spills into the coefficients of every correlated covariate, and the direction of that spillover is not generally predictable from first principles. “The variable I care about is measured well” is not sufficient.
• Measurement error in a control variable produces residual confounding. If you “control for” socioeconomic status using a noisy proxy, you have removed only part of its influence, and the remainder stays in the error term correlated with your regressor. This is one of the most common ways a paper that looks fully adjusted is not.
• Non-classical error need not attenuate. Bounded scales produce error correlated with the true value; differential misclassification of a binary regressor can bias in either direction, and can inflate rather than shrink an estimate. The clean attenuation result depends on assumptions that survey and administrative data frequently violate.

Where a construct is measured by several indicators, the honest response is to model the measurement explicitly rather than to average the indicators and pretend the average is the construct. That is what latent-variable methods are for — see exploratory factor analysis for identifying the structure and structural equation modelling fit indices for evaluating a model that estimates the measurement and structural parts jointly. A well-specified measurement model addresses attenuation at its source instead of instrumenting around it.

Matching source to remedy

This is the table the rest of the guide exists to support. Read the assumption column as the price, not the fine print — it is what you are asserting without evidence when you choose that method.

Source	Remedies that address it	What you are assuming
Omitted confounder, measured — you have the variable	Include it as a covariate; regression adjustment; propensity score matching; inverse probability weighting	Conditional ignorability: no unmeasured confounding remains, and the covariate is measured well
Omitted confounder, time-invariant — unit-level and constant	Fixed effects / within estimator; first differences; sibling or twin fixed effects	The confounder really is constant over the observation window, and x varies within unit
Omitted confounder, time-varying	Instrumental variables; difference-in-differences; regression discontinuity; interrupted time series	Design-specific: instrument validity, parallel trends, no manipulation of the running variable
Simultaneity / reverse causation	Instrumental variables; structural simultaneous-equation systems; design-based timing	The instrument shifts one equation only; the system is correctly specified
Selection into the sample	Heckman selection model; inverse probability weighting; bounds analysis	An exclusion restriction in the selection equation — a variable driving selection but not the outcome
Classical measurement error in x	A second independent measurement used as an instrument; latent-variable / SEM measurement models; SIMEX; correction using a known reliability coefficient	The second measure’s error is independent of the first’s, or the reliability is genuinely known
Classical measurement error in y	Nothing is required for the coefficient	The error is classical; you accept wider standard errors
Nonlinear model with an endogenous regressor	Control function approach	Instrument validity, plus a correctly specified first stage

Note that no row lists “add more control variables” as a general remedy, and only one row lists propensity scores.

Instrumental variables, and what they actually cost

An instrument z must satisfy two conditions, and the asymmetry between them is the single most important thing to understand about IV:

1. Relevance — z is correlated with x after conditioning on the other covariates. This is testable, from the first-stage regression.
2. Exclusion (validity) — z is uncorrelated with the structural error, meaning it affects y only through x. This is not testable. In the just-identified case there is no test at all; it is defended with an argument, never with a statistic.

An overidentification test (Sargan, or Hansen’s J under heteroscedasticity) is frequently mistaken for a test of validity. It is not. It tests the joint null that the instruments are valid conditional on at least as many as are needed being valid, it has low power, and passing it is not evidence that your instruments are exogenous — a set of uniformly invalid instruments that are invalid in the same direction passes comfortably. If a paper’s defence of its exclusion restriction is “the overidentification test does not reject”, it has no defence.

A third condition, monotonicity (no defiers), matters for what the estimate means. With heterogeneous treatment effects, IV recovers a local average treatment effect — the effect among compliers, the units whose x actually moved because of the instrument — not the average effect in the population. A LATE that is precisely estimated for an unrepresentative subgroup is not automatically the number a policy question needs.

Weak instruments: the worst of both estimators

When the first stage is weak, two things happen at once, and they compound:

• 2SLS is biased toward OLS. As the instrument’s explanatory power goes to zero, the IV estimator collapses back onto the very estimate it was supposed to correct. You have not removed the bias; you have paid for it.
• Conventional standard errors are understated, so t-ratios over-reject and confidence intervals are too narrow. The estimate is both wrong and overconfident, and it carries the rhetorical authority of a causal method.

The familiar convention is a first-stage F statistic above 10, from Staiger and Stock (1997), later formalised by Stock and Yogo (2005) into critical values that depend on the number of instruments and on how much bias or size distortion you are willing to tolerate. Ten is a rule of thumb, not a threshold — it corresponds to a particular case (a single endogenous regressor, a specific tolerance for size distortion), and it was never intended as a pass/fail line.

How far it is from a real threshold was quantified by Lee, McCrary, Moreira and Porter, Valid t-Ratio Inference for IV, American Economic Review 112(10), October 2022, 3260–90. In the single-IV model, their result is blunt: current practice “yields an anti-conservative test”, and a true 5 percent test requires an F greater than 104.7. If you want to keep 10 as your threshold, you must replace the critical value 1.96 with 3.43. Their tF adjustment scales the standard error smoothly with the first-stage F rather than applying a cliff; re-examining 61 published AER papers, they found that for a quarter of specifications the corrected standard errors were at least 49 percent larger at the 5 percent level and 136 percent larger at the 1 percent level than conventional 2SLS standard errors.

The practical implications for anyone reporting IV results:

• Always report the first-stage F, and the first-stage coefficients. A paper that reports only the second stage is not reporting enough to be assessed.
• Report OLS alongside IV. If they are close and the instrument is weak, that convergence is expected mechanically and is not corroboration.
• Use weak-instrument-robust inference when F is low. Anderson–Rubin confidence intervals remain valid regardless of instrument strength; the tF adjustment above is a second option.
• Do not compute 2SLS by hand as two OLS regressions. The coefficients come out right; the second-stage standard errors do not, because they ignore that the fitted values were estimated. Use a 2SLS routine.
• Defend the exclusion restriction in prose, naming the specific alternative pathways from z to y and why each is implausible. That paragraph is the actual evidence. There is no substitute statistic.

The control function approach

In a linear model, the control function estimator is numerically identical to 2SLS — it is not an alternative identification strategy, just a different computation. Regress the endogenous regressor on the instruments and exogenous covariates, retain the residuals, and include those residuals as an additional regressor in the structural equation.

Its value appears where 2SLS is not consistent: nonlinear models. If your outcome equation is a probit or a logit model, or if the endogenous regressor interacts with other covariates, plugging first-stage fitted values into the nonlinear second stage is not valid, and the control function is. Two cautions: the standard errors must account for the residual being a generated regressor (bootstrap, or an analytic correction), and the approach imposes stronger distributional assumptions than 2SLS does in the linear case. If you are fitting such a model in R, the diagnostics and reporting conventions in logistic regression in R apply to the second stage as usual.

A useful by-product: the t-test on the residual’s coefficient is a test of the null that the regressor is exogenous. It is the same test as Durbin–Wu–Hausman, obtained more directly.

Fixed effects: only time-invariant confounders

The within transformation subtracts each unit’s own mean from every variable, which removes anything constant within that unit over the observation window — ability, founding-era institutional culture, genotype, a firm’s location. This is a genuinely powerful remedy and it requires no instrument. It is also narrower than it is usually described.

Fixed effects removes time-invariant confounders and nothing else. A confounder that moves — a manager’s changing strategy, a patient’s evolving disease severity, a local economic shock — survives the transformation untouched. From the same seeded simulation, with a panel of 1,000 units observed over 4 periods, one time-invariant confounder and one time-varying confounder, and a true effect of 1.0:

N <- 1000; TT <- 4
id <- rep(1:N, each = TT)
a  <- rep(rnorm(N, sd = 2), each = TT)   # TIME-INVARIANT confounder
s  <- rnorm(N * TT)                      # TIME-VARYING confounder
x3 <- 0.7 * a + 0.7 * s + rnorm(N * TT)
y3 <- 1.0 * x3 + 1.5 * a + 1.5 * s + rnorm(N * TT)

demean <- function(v, g) v - ave(v, g)
coef(lm(y3 ~ x3))[["x3"]]                             # pooled OLS
coef(lm(demean(y3, id) ~ demean(x3, id)))[[2]]        # unit fixed effects

C. FIXED EFFECTS AGAINST TWO CONFOUNDERS AT ONCE
   pooled OLS            : 2.510
   unit fixed effects    : 1.727

Fixed effects cut the bias substantially — 2.510 down to 1.727 — and the remaining estimate is still 73 percent above the truth. This is the specific failure the guide is arguing against: a specification that has visibly improved, that a reviewer will accept as “controlling for unobserved heterogeneity”, and that is still badly wrong because the remedy addressed only one of the two confounders present.

Three further costs, all real:

• You cannot estimate the effect of anything time-invariant. Sex, birth cohort, country of incorporation — the transformation removes them along with the confounders. If a time-invariant regressor is your research question, fixed effects is not available to you.
• Fixed effects makes measurement-error attenuation worse. True regressors are typically persistent, so most of their variance is between units and is removed by demeaning; classical measurement error is typically not persistent, so nearly all of its variance survives. The signal-to-noise ratio of the transformed regressor falls, and attenuation rises. This is the central result of Griliches and Hausman, Errors in variables in panel data, Journal of Econometrics 31(1), 1986, 93–118, and it means that fixing omitted-variable bias can amplify measurement-error bias in the same regression — an argument for diagnosing the source before choosing the remedy, not after.
• Identification comes only from within-unit variation. If x barely moves within units, the estimate is driven by a small and possibly unrepresentative slice of the data, with correspondingly wide standard errors.

On the related choice between treating unit effects as fixed or as random draws, and what the random-effects assumption additionally requires, see mixed-effects models: random versus fixed effects.

Selection, and why it is a distinct case

Sample selection is endogeneity generated by who is in the data rather than by what is in the equation. If the probability of appearing in the sample depends on unobservables that also affect the outcome, conditioning on inclusion induces a correlation between regressor and error — the mechanism of selection bias, and, in panel and trial settings, of attrition bias.

The Heckman selection model handles this in two steps: a probit for the selection decision, from which an inverse Mills ratio is constructed and entered into the outcome equation. The coefficient on that term is a test for selection on unobservables. The critical detail, widely ignored: identification should come from an exclusion restriction — a variable that affects selection but not the outcome — not from the nonlinearity of the Mills ratio alone. Identification off functional form is fragile and collinear, and produces unstable estimates that shift with arbitrary specification choices. That exclusion restriction is exactly as untestable as an instrument’s, and deserves the same explicit defence. In trial settings, the parallel discipline is analysing as randomised rather than as treated — see intention-to-treat analysis.

Remedies that do not remedy this

Propensity scores

This is the most consequential confusion in the list, because propensity score methods are widely and wrongly described as a solution to endogeneity. Propensity score matching balances measured covariates. It assumes conditional ignorability — that treatment assignment is as good as random given the observed covariates. That assumption is precisely what endogeneity from an unobserved cause violates.

Worse, the method’s own diagnostics are reassuring in exactly the wrong way: after matching, standardised mean differences on the measured covariates improve, balance tables look excellent, and the bias from the unmeasured confounder is entirely unchanged. Good balance on what you measured is not evidence about what you did not. Propensity scores are a legitimate and useful tool for the first row of the remedy table — measured confounding — and no help at all for the rest. Propensity score matching: how it works and what it cannot fix sets out the mechanics and the boundary in detail.

Adding more control variables

Adding covariates helps only when the confounder is measured. When it is not, adding controls can actively make things worse. Two bad-control cases are common: conditioning on a mediator removes the part of the effect that travels through it, so you estimate a direct effect while reporting a total one; conditioning on a collider — a variable caused by both the regressor and the outcome — creates an association where none existed. “Throw everything into the model” is not the conservative choice it feels like.

Multicollinearity diagnostics

High correlation among regressors and endogeneity are unrelated diagnoses. Multicollinearity inflates variance; the estimator remains unbiased and consistent, so it is an efficiency problem. Endogeneity is an identification problem and no amount of precision cures it. A clean set of variance inflation factors says nothing about whether your regressor is exogenous — see multicollinearity and VIF in regression for what VIF does and does not diagnose.

Distributional fixes

Switching to a non-parametric test, or transforming variables until the residuals behave, addresses a different assumption entirely. If the normality assumption fails you may need a different test; the Wilcoxon signed-rank test is the right response to a distributional problem and no response at all to a confounded one. A rank-based test of a confounded comparison returns a valid p-value for a biased contrast.

A larger sample

Restated because it is the most common instinct: endogeneity is inconsistency. More data narrows the interval around the wrong value.

Improved model fit or discrimination

A specification that predicts better is not thereby better identified. Metrics that quantify whether adding a variable improves classification — such as net reclassification improvement — answer a prediction question. Prediction and causal identification are different objectives with different requirements, and a model can be excellent at one while being useless for the other.

Can you test for endogeneity?

Not without already assuming a solution. The Durbin–Wu–Hausman test compares the OLS and IV estimates and rejects when they differ by more than sampling variation would explain. It is a genuinely useful test, but note what it requires: a valid instrument, which is the untestable part. The test tells you whether OLS and a maintained-valid IV disagree. If your instrument is invalid, a rejection tells you the two estimators differ and nothing about which is closer to the truth; a failure to reject may simply reflect a weak instrument’s lack of power.

There is no diagnostic that reads endogeneity off the data alone, and there cannot be — the correlation in question involves an error term you never observe. The identification of the source is a substantive argument about how the data were generated, made from subject knowledge and an explicit causal diagram, before any estimation. That is why the source-first framing of this guide is not merely tidy: the data cannot make the choice for you.

A working procedure

1. Draw the causal diagram for the process that generated your data, including variables you cannot observe. Endogeneity is a property of that diagram, not of your dataset.
2. Identify which source applies. Is there a common cause you lack (omitted variable)? Does the outcome feed back into the regressor (simultaneity)? Is the regressor a noisy proxy (measurement error)? More than one can apply at once, and each needs its own answer.
3. Check whether the confounder is measured. If it is, the answer is regression adjustment or a propensity-score method, and no instrument is needed.
4. Check whether it is time-invariant and you have panel data. If so, fixed effects, with the measurement-error caveat above in mind.
5. Look for a design before looking for an instrument. A discontinuity, a staggered policy rollout, or a natural experiment carries assumptions that can be argued from institutional facts. A clever instrument usually carries one that cannot.
6. If you use IV, budget for the defence. First-stage F, first-stage coefficients, OLS side by side, weak-instrument-robust intervals when F is low, and a real paragraph on the exclusion restriction.
7. If none of these is available, sign the bias and say so. Use the direction table, report the estimate as a bound, and consider a formal sensitivity analysis — coefficient-stability bounds, or an E-value expressing how strong an unmeasured confounder would have to be to explain the result away. A bounded honest estimate is worth more than an unbounded implausible one.

The recurring failure this guide is written against is step 5 being skipped: an analyst who has diagnosed unobserved confounding, correctly, reaches straight for an instrument because that is what endogeneity is supposed to require — when the confounder was time-invariant and a panel was available, or measured and simply not included, or the whole problem was attenuation in a construct that a measurement model would have handled. The source determines the fix. Naming it first is most of the work.

This guide sits in the research methods cluster alongside related material on regression analysis and causal inference.

Frequently asked questions

Is endogeneity the same thing as omitted-variable bias?

No. Omitted-variable bias is one of three sources of endogeneity, alongside simultaneity/reverse causation and measurement error in the regressor. They break the same assumption — correlation between regressor and error — through different mechanisms, and they have different remedies. Conflating them is what leads analysts to instrument when a fixed-effects or measurement-model answer was available.

Does a larger sample fix endogeneity?

No. Endogeneity makes the estimator inconsistent, not merely imprecise, so the bias does not shrink with sample size. A larger sample produces a tighter confidence interval around the wrong number, which is more misleading than a small biased sample rather than less.

Does propensity score matching fix endogeneity?

Only for measured confounding. Propensity score methods assume conditional ignorability given the observed covariates, which is exactly the assumption that unmeasured confounding violates. The balance diagnostics after matching improve on the covariates you measured and say nothing about the ones you did not, which makes the method look more reassuring than it is in this specific case.

What first-stage F statistic do I need for an instrument to be strong enough?

The conventional figure is 10, from Staiger and Stock (1997), formalised by Stock and Yogo (2005) into critical values that vary with the number of instruments and the tolerated distortion. It is a rule of thumb, not a threshold. Lee, McCrary, Moreira and Porter (AER 2022) show that a true 5 percent test in the single-IV model requires an F greater than 104.7, and that retaining 10 as a threshold means replacing the 1.96 critical value with 3.43. When F is low, use weak-instrument-robust inference such as Anderson–Rubin intervals rather than conventional t-ratios.

Can I test whether my instrument is valid?

You can test relevance, from the first stage. You cannot test the exclusion restriction — in the just-identified case there is no test at all. An overidentification test (Sargan or Hansen J) tests a joint null conditional on enough instruments already being valid, has low power, and does not validate a set of instruments that are invalid in the same direction. The exclusion restriction is defended with an argument about mechanism, not with a statistic.

Do fixed effects solve endogeneity?

They remove confounders that are constant within a unit over the observation window, and nothing else. Time-varying confounders survive the within transformation. Fixed effects also cannot identify effects of time-invariant regressors, and they worsen attenuation when the regressor is measured with error, because demeaning removes more signal than noise.

Does measurement error in my outcome variable bias my coefficient?

Classical measurement error in the dependent variable does not bias the coefficient; it inflates residual variance and widens standard errors. Classical measurement error in a regressor attenuates its coefficient toward zero by the reliability ratio and contaminates correlated covariates. Mismeasuring y is an efficiency problem; mismeasuring x is an identification problem.

Is multicollinearity a form of endogeneity?

No. Multicollinearity inflates the variance of estimates while leaving them unbiased and consistent — an efficiency problem, diagnosed by variance inflation factors. Endogeneity is an identification problem that no amount of precision addresses. A model can have perfectly acceptable VIFs and a badly endogenous regressor.

Sources

• Lee, D. S., McCrary, J., Moreira, M. J., and Porter, J. (2022). “Valid t-Ratio Inference for IV.” American Economic Review 112(10), 3260–90.
• Griliches, Z., and Hausman, J. A. (1986). “Errors in variables in panel data.” Journal of Econometrics 31(1), 93–118.
• Staiger, D., and Stock, J. H. (1997). “Instrumental Variables Regression with Weak Instruments.” Econometrica 65(3).
• Stock, J. H., and Yogo, M. (2005). “Testing for Weak Instruments in Linear IV Regression.” In Identification and Inference for Econometric Models, Cambridge University Press.
• Simulation output above was generated in R 4.6.1 with set.seed(20260826); the code shown reproduces the printed figures exactly.