7 Instrumental Variables
7.1 Why Instrumental Variables?
Chapter 6 showed how causal effects can be identified when all confounders are observed and can be blocked by conditioning on \(X\). When some confounders are unobserved, back-door adjustment fails. This chapter develops instrumental variables (IV) as an alternative identification strategy: rather than blocking the confounding path \(T \leftarrow U \rightarrow Y\), IV exploits an external variable \(Z\) whose effect on \(T\) is free of confounding by \(U\). This chapter asks what IV identifies and under what assumptions; Chapter 13 asks how that estimand is computed and tested in practice.
7.1.1 The Endogeneity Problem
Chapter 6 established that the propensity score provides a powerful surrogate for randomization, but only under unconfoundedness: \[\bigl(Y(0),\, Y(1)\bigr) \indep T \;\big|\; X.\] This assumption requires \(X\) to be a sufficient adjustment set: every back-door path from \(T\) to \(Y\) must be blocked by observed covariates. In many empirical settings this is implausible:
- In labor economics, unobserved ability or motivation affects both schooling decisions and wages.
- In epidemiology, unobserved health behaviors affect both treatment uptake and outcomes.
- In survey sampling, voluntary participation is driven by factors that also affect the variables of interest.
When an unobserved confounder \(U\) creates a back-door path \(T \leftarrow U \rightarrow Y\) that no observed set blocks, the adjustment formula \[\int f(y \mid t, x)\, p(x)\, dx\] is no longer justified as an expression for \(f\!\bigl(y \mid \doop(T{=}t)\bigr)\). The two can differ, and their difference is a confounding bias that more data do not remove. (Econometricians call such a treatment endogenous.) We need a different identification strategy.
7.1.2 The IV Idea
An instrumental variable \(Z\) is an observed variable that:
- Moves treatment \(T\) (relevance).
- Does so exogenously — \(Z\) is unrelated to the unobserved confounder \(U\) (exogeneity).
- Affects \(Y\) only through \(T\) — \(Z\) has no direct path to \(Y\) (exclusion).
Under these three conditions, the variation in \(T\) induced by \(Z\) is free of confounding by \(U\), so the ratio of the \(Z\)-induced variation in \(Y\) to the \(Z\)-induced variation in \(T\) becomes a meaningful target for identification. Which familiar average effect it equals — the ATE, the ATT, or the LATE for compliers — depends on a fourth structural restriction on treatment-effect heterogeneity, taken up in Section 7.3 and Section 7.7. Note that condition 2 concerns how \(Z\) is assigned. How a unit’s treatment responds to \(Z\) may still depend on \(U\); this is why compliance types appear in Section 7.7.
Instrumental variables do not eliminate the confounding path \(T \leftarrow U \rightarrow Y\), nor do they make treatment as-if randomly assigned for the full population. Instead, IV identifies causal effects by isolating a component of treatment variation that is induced by \(Z\) and is therefore exogenous under the IV assumptions. In that sense, IV avoids confounding rather than controlling for it — a distinction that matters both for interpreting what is identified (the LATE for compliers, not the ATE) and for understanding which assumption does the heaviest lifting (exclusion, not unconfoundedness).
Example 7.1 (Returns to Schooling as Motivation) A researcher wants to estimate the causal effect of years of schooling \(T\) on log wages \(Y\). In a model in which unobserved ability \(U\) raises both schooling (after adjusting for demographics) and wages, \(\mathrm{Cov}(T, \varepsilon) > 0\) and OLS is biased upward. No set of observed covariates \(X\) fully captures ability. An instrumental variable \(Z\) that shifts schooling for reasons unrelated to ability — such as growing up near a college or the timing of birth relative to compulsory attendance laws — provides a way to isolate the causal effect of schooling on wages.
7.2 Graphical Setup and Core Assumptions
This section is the conceptual foundation of the IV chapter. We fix the causal graph for the IV design and state the three core assumptions in the three causal languages used throughout these notes: DAGs and do-calculus, structural equations, and potential outcomes. The purpose is not merely stylistic. Each language highlights a different aspect of the design: the DAG makes the causal pathways visible, the do-calculus formalizes what those pathways imply about interventional distributions, the structural model supplies the moment conditions used in the Wald derivation, and the potential-outcomes formulation prepares the ground for the LATE framework in Section 7.7. The potential-outcomes language dominates biostatistics and program evaluation, the structural language is standard in econometrics, and the do-calculus is the course’s preferred vehicle for identification proofs.
Before proceeding, it is important to separate two questions that are often conflated. The first is: when is an instrument valid? Validity requires the three core IV assumptions — relevance, exogeneity, and exclusion — which are the subject of this section. The second is: what does the Wald ratio of a valid instrument estimate? With binary \(Z\) and \(T\), the three assumptions already give the ratio a causal representation (see the remark on instrument validity below), but in general that representation is not the ATE, the ATT, or the average effect among compliers. Which familiar average effect the ratio equals depends on a fourth structural assumption. Under linearity and homogeneous treatment effects (Section 7.3), the Wald ratio identifies a single parameter \(\beta\) equal to the ATE. Under heterogeneous effects with monotonicity (Section 7.7), the same Wald ratio identifies the LATE for compliers. The three IV assumptions determine whether the design is valid; the fourth assumption determines which familiar average effect the ratio recovers.
7.2.1 The IV DAG
The causal structure for a basic IV model with covariates \(X\) is:
The three IV assumptions correspond to three distinct features of this DAG:
- Relevance: there is a directed path \(Z \to T\) (edge labeled (1) above), so the instrument shifts treatment.
- Exogeneity: given the observed covariates \(X\), every back-door path from \(Z\) to \(Y\) is blocked. In this graph the condition reads \(Z \indep U \mid X\) by d-separation. Intuitively, \(Z\) is as-if randomized with respect to the unobserved factors that confound \(T\) and \(Y\).
- Exclusion: every directed path from \(Z\) to \(Y\) in \(\Gcal\) passes through \(T\). In the simple IV DAG above this rules out the direct edge \(Z \to Y\); in richer graphs it also rules out indirect channels \(Z \to M \to Y\) that bypass \(T\) through any unmodeled mediator \(M\).
Throughout the chapter we also maintain consistency (\(T = T(Z)\) and \(Y = Y(T, Z)\)) and, for a binary instrument, instrument positivity: \(0 < P(Z = 1 \mid X = x) < 1\) for every \(x\) in the support of \(X\).
The distinction between exogeneity and exclusion is fundamental. Exogeneity says that the instrument is not confounded with the latent causes of the outcome. Exclusion says that the instrument has no causal channel to the outcome except through treatment. An instrument can satisfy one and fail the other. For example, a randomized encouragement may be exogenous by design, yet still violate exclusion if the encouragement changes outcomes through information, motivation, stigma, or administrative treatment apart from the treatment itself. The figure below displays both failure modes side by side. ::: {.content-visible when-format=“html”}
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What the DAG rules out. The absence of a direct \(Z \to Y\) arrow encodes the exclusion restriction. Any such arrow — no matter how small the coefficient — would violate exclusion and invalidate the Wald estimand. The DAG forces the researcher to commit to this assumption explicitly; the potential outcomes framework expresses it as the equality \(Y_i(t,z) = Y_i(t,z')\).
7.2.2 The Three Assumptions in Three Languages
The same three assumptions can be expressed in three causal languages. These are parallel formulations, not literally identical statements: each language highlights a different aspect of the underlying design. The graphical formulation is most useful for causal design, because it makes confounding paths and forbidden arrows explicit. The structural formulation is most useful for deriving moment restrictions such as \(\mathrm{Cov}(Z, \varepsilon \mid X) = 0\). The potential-outcomes formulation is most useful when we later introduce compliance types and the LATE theorem (Section 7.7). Across all three, the do-calculus remains the course’s preferred vehicle for identification proofs. The assumptions are ordered relevance \(\to\) exogeneity \(\to\) exclusion, reflecting the natural sequence in which a researcher assesses them: first check that the instrument actually moves treatment, then verify it is exogenously assigned, and finally — most subtly — verify it has no direct effect on the outcome.
| Assumption | Potential outcomes | Structural | Do-calculus / DAG |
|---|---|---|---|
| Relevance | \(\E\{T(1) - T(0) \mid X\} \neq 0\) | \(\pi \neq 0\) in \(T = \pi Z + \kappa^\top X + \eta\) | a directed path from \(Z\) to \(T\) in \(\Gcal\) |
| Exogeneity | for each \(z\), \(Z \indep \{T(z),\ Y(T(z), z)\} \mid X\) | \(\E(\varepsilon \mid Z, X) = \E(\varepsilon \mid X)\) | given \(X\), back-door paths from \(Z\) to \(Y\) blocked (here \(Z \indep U \mid X\)) |
| Exclusion | \(Y_i(t, z) = Y_i(t, z')\) for all \(z, z'\) | \(Z\) absent from structural equation for \(Y\) | \(f(y \mid x, \doop(t), \doop(z)) = f(y \mid x, \doop(t))\) |
The potential-outcomes entries are written for binary \(Z\) and \(T\). The structural exogeneity entry assumes no normalization of \(\E(\varepsilon \mid X)\): absorbing \(\E(\varepsilon \mid X)\) into the outcome equation need not keep that equation linear in \(X\). In a structural model that contains mediators, exclusion also rules out any path \(Z \to M \to Y\) that bypasses \(T\). The relevance entry in the potential-outcomes column is a nonzero average first stage: a positive share of units moved by \(Z\) is not enough, because units moved in opposite directions can cancel.
Why the do-calculus column is preferred. The exclusion restriction in the do-calculus column reads \[f\!\bigl(y \mid x,\, \doop(T{=}t),\, \doop(Z{=}z)\bigr) \;=\; f\!\bigl(y \mid x,\, \doop(T{=}t)\bigr).\] It is a statement about interventional densities: once \(T\) is set by intervention, setting \(Z\) as well leaves the distribution of \(Y\) unchanged. By Rule 3 of the do-calculus it holds when \((Y \indep Z \mid T, X)\) in \(\Gcal_{\overline{T}\,\overline{Z}}\), the graph with all arrows into \(T\) and into \(Z\) removed. In that graph only the outgoing edges of \(Z\) remain, so the condition fails exactly when a directed path from \(Z\) to \(Y\) avoids \(T\): it isolates exclusion. The related Rule 1 statement \(f(y \mid x, \doop(T{=}t), z) = f(y \mid x, \doop(T{=}t))\), checked in \(\Gcal_{\overline{T}}\), also fails when an arrow \(U \to Z\) opens \(Z \leftarrow U \rightarrow Y\); it follows from exclusion and exogeneity together, and it is the form used in the Wald derivation of Section 7.3. Neither statement should be confused with the observational independence \(f(y \mid x, T{=}t, z) = f(y \mid x, T{=}t)\), which the valid IV graph does not imply: conditioning on \(T\) opens the collider path \(Z \to T \leftarrow U \to Y\).
7.2.3 Relevance
Definition 7.1 (Relevance) The instrument \(Z\) is relevant if it has a non-zero causal effect on the treatment \(T\) within at least some stratum of covariates \(X\). Formally, \(P\bigl(T \mid \doop(Z{=}z),\, X{=}x\bigr)\) varies with \(z\) for some \(x\) in the support; in the linear first-stage model \(T = \pi Z + \kappa^\top X + \eta\), this reduces to \(\pi \neq 0\).
The graphical analogue of relevance is that \(Z\) and \(T\) are not d-separated in \(\Gcal\). Under faithfulness, a directed path \(Z \to T\) implies an observable association between \(Z\) and \(T\); without faithfulness, non-d-separation does not by itself guarantee a non-zero conditional covariance, and an exact cancellation between alternative paths is mathematically possible. Conversely, an observable association between \(Z\) and \(T\) can arise without a causal \(Z \to T\) effect when \(Z\) and \(T\) share a common cause. Graphical non-d-separation, observable association, and a non-zero causal effect are therefore three related but not identical conditions. Dependence also need not show up as a covariance: if \(Z\) is symmetric about zero and \(T = Z^2 + \eta\), then \(Z\) shifts \(T\), yet \(\mathrm{Cov}(Z, T) = 0\), so a linear first stage would miss it. The conditional covariance \(\mathrm{Cov}(Z, T \mid X)\) and the first-stage \(F\)-statistic are empirical diagnostics for the linear first-stage association; the causal claim that \(Z\) shifts \(T\) is design-based. What happens when relevance holds only weakly — or fails entirely — is analyzed in Section 7.4 and Section 7.6.
7.2.4 Exogeneity
Definition 7.2 (Exogeneity (Graphical Assumption)) The instrument \(Z\) is exogenous given covariates \(X\) if, given \(X\), every back-door path from \(Z\) to \(Y\) is blocked. In the canonical IV graph this is \(Z \indep U \mid X\) in \(\Gcal\) by d-separation.
Exogeneity means that the instrument carries no information about latent determinants of the outcome other than through treatment. In the DAG language, there is no open back-door path from \(Z\) to \(Y\) through unobserved causes \(U\): the graphical condition \(Z \indep U \mid X\) in \(\Gcal\) captures this directly. In the structural linear model, the same requirement appears as the moment orthogonality condition \(\E[\{Z - \E(Z \mid X)\}\varepsilon \mid X] = 0\), because the structural residual \(\varepsilon\) is a function of \(U\). In potential-outcomes language, \(Z\) must be independent, given \(X\), of the potential treatment \(T(z)\) and of the outcome that results when \(Z\) is set to \(z\), for each \(z\). These are related manifestations of the same identification requirement, but they live in different formal languages and are not literally the same statement.
Econometric implication. Write \(\tilde Z = Z - \E(Z \mid X)\). If \(\varepsilon\) is a function of \(U\) and of noise independent of everything else, the graphical assumption gives \(\E(\varepsilon \mid Z, X) = \E(\varepsilon \mid X)\), and hence \[\E(\tilde Z \varepsilon \mid X) = \E\{\tilde Z\, \E(\varepsilon \mid Z, X) \mid X\} = \E(\varepsilon \mid X)\, \E(\tilde Z \mid X) = 0.\] The centering matters: without it, \(\E(Z\varepsilon \mid X) = 0\) requires the further normalization \(\E(\varepsilon \mid X) = 0\). The moment condition is a consequence of the graphical assumption, not a definition of exogeneity. This distinction matters: a researcher who adopts the moment condition as a primitive has no guarantee that \(Z\) is free of back-door paths to the outcome, only that a particular linear projection is zero. The condition enters the Wald derivation in Section 7.3 specifically because it follows from the graphical assumption.
Potential-outcomes analogue. For binary \(Z\) and \(T\), let \(T(z)\) be the treatment a unit would take if \(Z\) were set to \(z\), and let \(Y(t, z)\) be its outcome when \(T = t\) and \(Z = z\); consistency gives \(T = T(Z)\) and \(Y = Y(T, Z)\). Then \(Y(T(z), z)\) is the outcome when only \(Z\) is set to \(z\). The graphical assumption implies, for each \(z\), \[Z \indep \bigl\{T(z),\, Y(T(z), z)\bigr\} \;\big|\; X. \tag{7.1}\] The argument is that of Proposition 4.3, with \(Z\) in the role of the treatment. In the single-world intervention graph \(\Gcal(z)\), the random half of \(Z\) has no children, so every path from \(Z\) to \(T(z)\) or \(Y(T(z), z)\) is a back-door path of \(\Gcal\). A back-door path from \(Z\) to \(T\) extends through \(T \to Y\) to a back-door path from \(Z\) to \(Y\), and \(T\) is not in \(X\) because \(X\) contains no descendants of \(Z\). So \(X\) blocks every such path, and Equation 7.1 follows. Statement Equation 7.1 does not use exclusion, and it covers the potential treatment \(T(z)\) as well as the outcome; the LATE proof in Section 7.7 uses both.
The stronger joint statement \[Z \indep \bigl(T(0),\, T(1),\, Y(0,0),\, Y(1,0),\, Y(0,1),\, Y(1,1)\bigr) \;\big|\; X,\] the random-assignment assumption of Angrist et al. (1996), follows from the graphical assumption only if the structural errors are also mutually independent (Chapter 4). It holds by design when \(Z\) is randomized. The IV arguments of this chapter need only the single-world form Equation 7.1.
Example 7.2 (Quarter of Birth as an Instrument) Angrist and Krueger (1991) used quarter of birth as an instrument for schooling to estimate the return to education. In graphical terms, exogeneity requires no open back-door path from quarter of birth to wages through unobserved variables such as ability or family background; in potential-outcomes terms, it requires that birth timing is independent of what wages a student would earn under any schooling level. Both are plausible because birth timing is largely outside parental control, although season of birth is associated with family background (Buckles and Hungerman 2013), so even this instrument needs a defense. Bound et al. (1995) later raised concerns about weak first stages in some specifications, illustrating that even a well-motivated instrument can fail the relevance requirement in certain samples.
Key point. No version of exogeneity can be tested on its own: the unobserved confounder \(U\) is, by definition, unobserved, and counterfactual potential outcomes are never jointly observed. The assumption must be justified by institutional knowledge or the design of the study. Together with exclusion, however, it restricts the observed distribution, so the data can sometimes reject the IV model, but never confirm it (Pearl 1995; Kitagawa 2015). With binary \(Z\), \(T\), and \(Y\) and no covariates, for example, exogeneity and exclusion imply the instrumental inequality \[P(Y{=}0, T{=}t \mid Z{=}1) + P(Y{=}1, T{=}t \mid Z{=}0) \le 1, \qquad t = 0, 1,\] and the same with \(Z{=}0\) and \(Z{=}1\) exchanged; monotonicity is not needed. Data that violate it reject the model, but many ways the assumptions can fail leave it satisfied. See Section 7.6 for the limited consistency check that overidentification provides.
7.2.5 Exclusion
Definition 7.3 (Exclusion Restriction) The instrument \(Z\) satisfies the exclusion restriction if it affects the outcome \(Y\) only through its effect on the treatment \(T\): every directed path from \(Z\) to \(Y\) passes through \(T\). Exclusion implies the do-calculus statement \[f\!\bigl(y \mid x,\, \doop(T{=}t),\, \doop(Z{=}z)\bigr) \;=\; f\!\bigl(y \mid x,\, \doop(T{=}t)\bigr) \quad \text{for all } z.\] In potential-outcomes terms, exclusion is the unit-level restriction \(Y_i(t, z) = Y_i(t, z')\) for all \(z \neq z'\). The unit-level restriction implies the equality above; the equality, a statement about distributions, does not imply it.
Exclusion is a causal restriction, not a conditional-correlation restriction. It is emphatically not the observational statement \(Y \indep Z \mid T, X\). That statement can hold in the data even when \(Z\) has a direct structural effect on \(Y\) (through a cancellation), and it is not implied when exclusion holds: conditioning on \(T\) opens the collider path \(Z \to T \leftarrow U \to Y\), so \(Z\) and \(Y\) can be associated given \(T, X\) in a valid design. What exclusion requires is that changing \(Z\) while holding treatment fixed — that is, intervening to set \(T = t\) — would leave \(Y\) unchanged. In graphical terms, every directed path from \(Z\) to \(Y\) must pass through \(T\): exclusion rules out a direct edge \(Z \to Y\) and any indirect channel \(Z \to M \to Y\) that bypasses \(T\). In the structural linear model, this means no \(Z\) term appears in the outcome equation for \(Y\), and no mediator other than \(T\) carries an effect of \(Z\).
The do-calculus makes the violation visible. Adding a direct arrow \(Z \to Y\) to the DAG is exactly the formal counterpart of exclusion failing. In \(\Gcal_{\overline{T}\,\overline{Z}}\), where all arrows into \(T\) and into \(Z\) have been removed, the edge \(Z \to Y\) survives, so Rule 3 no longer removes \(\doop(Z{=}z)\) from the interventional density of \(Y\). An arrow \(U \to Z\), by contrast, is deleted in \(\Gcal_{\overline{T}\,\overline{Z}}\): exclusion is a statement about the paths out of \(Z\), exogeneity about the paths into \(Z\).
7.3 Identification in the Linear Homogeneous-Effect Model
7.3.1 The Linear Structural Model
We begin with the homogeneous-effect linear SEM because it makes the IV logic transparent; Section 7.7 then relaxes homogeneity and reinterprets the same Wald ratio as a LATE.
Consider the linear structural model: \[Y = \alpha + \beta T + \gamma^\top X + \varepsilon, \tag{7.2}\] \[T = \pi Z + \kappa^\top X + \eta, \tag{7.3}\] where \(\varepsilon\) and \(\eta\) are structural errors with standard deviations \(\sigma_\varepsilon\) and \(\sigma_\eta\). We assume \(\mathrm{Cov}(Z, \varepsilon \mid X) = \mathrm{Cov}(Z, \eta \mid X) = 0\), which exogeneity implies when both errors are functions of \(U\) and of independent noise, and \(\mathrm{Cov}(\varepsilon, \eta) = \rho\sigma_\varepsilon\sigma_\eta \neq 0\). A shared latent cause makes \(\rho \neq 0\) typical but does not force it, so \(\rho \neq 0\) is an assumption. The nonzero covariance is the source of endogeneity: OLS applied to Equation 7.2 gives a biased estimator of \(\beta\).
Equation Equation 7.2 is the potential outcome \(Y(t) = \alpha + \beta t + \gamma^\top X + \varepsilon\) evaluated at \(t = T\); the error \(\varepsilon\) collects everything else that determines \(Y\), including \(U\). It looks like a regression equation but is not one: a regression of \(Y\) on \((T, X)\) would carry \(\E(\varepsilon \mid T, X) = 0\), whereas here \(\mathrm{Cov}(T, \varepsilon \mid X) = \mathrm{Cov}(\eta, \varepsilon) \neq 0\), so \(\beta\) is not the regression slope of \(Y\) on \(T\). The reduced form below, by contrast, is a regression: \(Z\) is uncorrelated with its error \(\beta\eta + \varepsilon\) given \(X\).
The parameter of interest is \(\beta\), the causal effect of \(T\) on \(Y\): \[\beta = \E\!\bigl[Y \mid \doop(T{=}t+1)\bigr] - \E\!\bigl[Y \mid \doop(T{=}t)\bigr].\] Equation Equation 7.2 is the outcome equation (or second stage); Equation 7.3 is the first-stage equation. The reduced form is obtained by substituting Equation 7.3 into Equation 7.2: \[Y = \alpha + \beta(\pi Z + \kappa^\top X + \eta) + \gamma^\top X + \varepsilon = \alpha + \beta\pi Z + (\beta\kappa + \gamma)^\top X + (\beta\eta + \varepsilon).\] The reduced-form coefficient on \(Z\) is \(\beta\pi\): the total effect of the instrument on the outcome. Dividing by the first-stage coefficient \(\pi\) recovers \(\beta\), provided \(\pi \neq 0\).
7.3.2 The OLS Bias
To see why OLS fails, take the case without covariates and apply OLS to Equation 7.2. Since \(\mathrm{Cov}(Z, \varepsilon) = \mathrm{Cov}(Z, \eta) = 0\), the probability limit of the OLS estimator is \[\mathrm{plim}\; \hat\beta_{\mathrm{OLS}} = \beta + \frac{\mathrm{Cov}(T, \varepsilon)}{\mathrm{Var}(T)} = \beta + \frac{\rho\sigma_\varepsilon\sigma_\eta}{\pi^2 \mathrm{Var}(Z) + \sigma_\eta^2}. \tag{7.4}\] The second term is the endogeneity bias. It is zero only if \(\rho = 0\) (the two errors are uncorrelated) or if \(\sigma_\eta = 0\) (the instrument determines \(T\), infeasible in practice). The direction of the bias depends on the sign of \(\rho\). The bias shrinks as \(|\pi|\) grows, but it does not shrink with the sample size.
The point of IV is not that OLS is always wrong, but that when \(T\) is endogenous, IV can recover a causal parameter from the exogenous variation in \(T\) that \(Z\) induces — variation that OLS mixes indiscriminately with the confounded component.
7.3.3 Derivation of the Wald Estimand
The derivation has three ingredients:
- the first stage, which measures how much the instrument moves treatment;
- the reduced form, which measures how much the instrument moves the outcome;
- the exclusion restriction, which implies that any effect of \(Z\) on \(Y\) must operate through \(T\).
Under the homogeneous-effect linear model, these three ingredients imply that the reduced-form effect of \(Z\) on \(Y\) is exactly \(\beta\) times the first-stage effect of \(Z\) on \(T\). Dividing the reduced form by the first stage therefore recovers \(\beta\).
We derive the identification of \(\beta\) step by step, using the structural model as the vehicle and the do-calculus to interpret the exclusion step. Write \(\tilde Z = Z - \E(Z \mid X)\), and note that \(\E\{\tilde Z\, g(X)\} = 0\) for every function \(g\).
Exogeneity (given \(X\), no open back-door path from \(Z\) to \(Y\); in the IV graph, \(Z \indep U \mid X\)) implies, for the structural residual \(\varepsilon\), \[\E[\varepsilon \mid Z, X] = \E[\varepsilon \mid X].\] No normalization of \(\E[\varepsilon \mid X]\) is needed. (An arbitrary function of \(X\) could not, in general, be absorbed into the linear term \(\gamma^\top X\) anyway.)
Exclusion (\(Z\) absent from the structural equation for \(Y\)) is what permits writing the outcome equation Equation 7.2 without a \(Z\) term in the first place: under exclusion, the structural residual \(\varepsilon\) depends on \(U\) but does not absorb a direct effect of \(Z\) on \(Y\). Combined with step 1, \[\E(\tilde Z \varepsilon \mid X) = \E\{\tilde Z\, \E(\varepsilon \mid Z, X) \mid X\} = \E(\varepsilon \mid X)\, \E(\tilde Z \mid X) = 0 .\] The graphical counterpart uses both assumptions: with exogeneity and exclusion, \(Y \indep Z \mid T, X\) holds in \(\Gcal_{\overline{T}}\), and Rule 1 of the do-calculus removes \(Z\) from \(f(y \mid x, \doop(T{=}t), z)\).
Multiply Equation 7.2 by \(\tilde Z\) and take expectations. The terms \(\alpha\) and \(\gamma^\top X\) drop out, and step 2 removes the error term: \[\E(\tilde Z Y) = \beta\, \E(\tilde Z T) + \E(\tilde Z \varepsilon) = \beta\, \E(\tilde Z T).\] In the simpler case with no covariates \(X\), this is the reduced-form decomposition \[\mathrm{Cov}(Y, Z) = \beta\, \mathrm{Cov}(T, Z),\] which shows that the \(Z\)–\(Y\) covariance is entirely attributable to the causal path \(Z \to T \to Y\) (by exclusion), and equals \(\beta\) times the first-stage covariance. Constant effects enter at this step: a single \(\beta\) multiplies every unit’s \(T\).
Relevance, \(\E(\tilde Z T) = \E\{\mathrm{Cov}(Z, T \mid X)\} \neq 0\), allows the division: \[\beta = \frac{\E(\tilde Z Y)}{\E(\tilde Z T)} = \frac{\E\{\mathrm{Cov}(Y,\, Z \mid X)\}}{\E\{\mathrm{Cov}(T,\, Z \mid X)\}}. \tag{7.5}\] Taking expectations given \(X = x\) in step 3 instead gives the pointwise version \(\beta = \mathrm{Cov}(Y, Z \mid X{=}x)/\mathrm{Cov}(T, Z \mid X{=}x)\) at every \(x\) with a nonzero denominator. Under the linear model every such ratio, and every average of numerator and denominator, equals \(\beta\).
The key lesson is that the Wald ratio identifies \(\beta\) in this section only because treatment effects are assumed to be constant across units. The observed formula \[\frac{\E\{\mathrm{Cov}(Z, Y \mid X)\}}{\E\{\mathrm{Cov}(Z, T \mid X)\}}\] is a statistical estimand, a feature of the observed distribution. Which causal estimand it equals depends on the structural assumptions maintained around it. In Section 7.7, the same ratio will survive, but its interpretation will change from a common causal effect to a complier-specific average effect.
Example 7.3 (Returns to Schooling) In the Mincer earnings equation \(\log W = \alpha + \beta S + \gamma^\top X + \varepsilon\), where \(S\) is years of schooling, \(W\) is wages, and \(X\) are demographics, the OLS estimator of \(\beta\) is biased upward because unobserved ability \(U\) raises both \(S\) and \(W\) (\(\rho > 0\)). Angrist and Krueger (1991) use quarter of birth. In the simplest contrast, \(Z = 1\) for men born in the first quarter and \(Z = 0\) for men born in the other three quarters. Because compulsory attendance laws bind by birth date, first-quarter births can leave school at an earlier grade: the contrast lowers completed schooling by about a tenth of a year, and lowers log wages slightly, so the Wald ratio is a ratio of two negative numbers. Using all four quarters, or their interactions with other variables, is a case of multiple instruments (Section 7.6). The IV estimate of the return to schooling is approximately \(0.08\)–\(0.10\) per year, similar to the OLS estimate in this case, suggesting the ability bias is modest.
7.4 Why the IV Assumptions Matter
The three IV assumptions are not merely technical conditions: each one is load-bearing, and each failure mode produces a distinct, quantifiable distortion of the Wald estimand. Violating exogeneity or exclusion contaminates the reduced form, and dividing by a weak first stage magnifies that contamination. A weak instrument is therefore not merely inefficient; it makes any small violation of the identifying assumptions more consequential.
When relevance fails. If \(\pi = 0\), the Wald estimand is undefined: its denominator is zero and there is no exogenous variation to exploit. When \(\pi\) is small but nonzero, the instrument is weak. The Wald ratio still identifies \(\beta\), but its sample analog becomes unstable: the estimated first stage is often close to zero, and the estimator has very heavy tails. In the Gaussian design of Section 7.5, the just-identified IV estimator has no finite mean, so mean bias is undefined. Its distribution is nevertheless pulled toward the OLS probability limit (median bias), and at \(\pi = 0\) it is exactly a Cauchy distribution centered there (Bound et al. 1995; Andrews and Armstrong 2017).
When exclusion fails. If the outcome equation contains a direct effect \(Y = \alpha + \beta T + \delta Z + \gamma^\top X + \varepsilon\) with \(\delta \neq 0\), the reduced form picks up both the indirect path \(\beta\pi\) and the direct path \(\delta\), so the Wald ratio equals \(\beta + \delta/\pi\). The bias \(\delta/\pi\) is amplified by a weak first stage: a small direct effect combined with a weak instrument can produce large bias. This is why a weak instrument with a plausible exclusion violation is not “nearly valid” — it may be severely misleading. In the reminder-letter example of Example 7.4, the first stage is \(0.20\) and the reduced form \(-0.02\); if the letter itself lowered hospitalization risk by one percentage point, say by prompting hand-washing, the reduced form would become \(-0.03\) and the ratio would move from \(-0.10\) to \(-0.15\). A one-point side effect shifts the estimate by five points.
When exogeneity fails. If \(\mathrm{Cov}(Z, \varepsilon \mid X) \neq 0\), the IV moment condition fails and the Wald ratio equals \(\beta + \mathrm{Cov}(\varepsilon, Z)/\mathrm{Cov}(T, Z)\). This is the IV analogue of OLS omitted-variable bias: IV fails when the instrument itself is endogenous, just as OLS fails when the treatment is endogenous. Again the bias is amplified when the first stage is weak.
Table 7.1 summarizes the testability status of the three assumptions. The key asymmetry is that the hardest work in defending an IV design — the institutional arguments for exogeneity and exclusion — is precisely the work that the data cannot do for the researcher.
| Assumption | Directly testable? | Basis for assessment |
|---|---|---|
| Relevance | Association testable; causal claim design-based | First-stage \(F\)-statistic and \(\mathrm{Cov}(Z,T \mid X)\) test the observable association; the causal \(Z \to T\) link rests on the design |
| Exogeneity | Not separately | Institutional knowledge; randomization (if available); placebo regressions on pre-determined outcomes |
| Exclusion | Not separately | Institutional argument. With several instruments the \(J\)-test (Chapter 13) checks the joint moment restrictions, not exclusion by itself, and cannot confirm that all instruments are valid; with binary variables the instrumental inequality of Section 7.2 is a further check |
7.5 Lab: OLS vs. IV Across Instrument Strengths
The analytic results of Section 7.3 and Section 7.4 established two facts: OLS is biased by a precise, computable amount whenever \(\rho \neq 0\); and IV is consistent for every fixed \(\pi \neq 0\), but its sampling distribution spreads out and acquires heavy tails as \(\pi \to 0\). What the analytics do not immediately reveal is the finite-sample consequence: with a weak instrument the IV estimate is usually close and occasionally far off, to the point that the biased OLS estimator can have a lower Monte Carlo root mean squared error. This lab verifies the bias formulas numerically and traces the behavior of both estimators across the full range of instrument strength, from \(\pi = 0\) (no instrument) to \(\pi = 2\) (very strong instrument). This simulation studies estimator behavior conditional on the IV assumptions being true; it does not address the separate and fundamentally substantive question of whether a proposed instrument is valid in an applied study.
Estimators. Two estimators of \(\beta\) are compared at each value of \(\pi\).
OLS regresses \(Y\) on \(T\): \(\hat\beta_{\mathrm{OLS}} = \mathrm{Cov}(Y, T)/\mathrm{Var}(T)\). From Section 7.3, this converges in probability to \(\beta + \rho/(\pi^2 + 1) = 1 + 0.8/(\pi^2 + 1)\). The bias is always positive (since \(\rho > 0\)), decreasing in \(|\pi|\), but never zero for finite \(\pi\).
IV (Wald estimator) uses \(Z\) as the instrument: \(\hat\beta_{\mathrm{IV}} = \mathrm{Cov}(Y, Z)/\mathrm{Cov}(T, Z)\). This estimator is consistent for \(\beta\) for any fixed \(\pi \neq 0\), and for a strong instrument its distribution is approximately normal with variance \(\sigma_\varepsilon^2/(n\pi^2)\) in this design, a variance that grows without bound as \(\pi \to 0\). This is the variance of the normal approximation, not of the estimator: in finite samples the just-identified IV estimator has no finite moments in this Gaussian design, whatever the value of \(\pi\), so its mean, variance, and mean squared error do not exist at any \(n\).
Results. Table 7.2 reports Monte Carlo mean, bias, standard deviation, and RMSE across \(B = 2{,}000\) replications at \(n = 500\), seed 2024, alongside the theoretical OLS bias from Section 7.3 and the mean first-stage \(F\)-statistic. For OLS these columns estimate population quantities. For IV they do not: because the IV estimator has no finite moments in this design, the IV mean, SD, and RMSE summarize these 2,000 draws only and change from seed to seed. Table 7.3 therefore adds quantile-based summaries, which do have population counterparts.
2024. RMSE is reported as \(\sqrt{\text{bias}^2 + \text{sd}^2}\). At \(\pi = 0\) the Wald estimand is undefined, but the sample ratio is still computable and its row is reported. IV mean and SD at \(\pi \le 0.15\) are set by a few extreme replications; the IV median is \(\approx 1.01\) at \(\pi = 0.10\) and \(0.15\).
| \(\pi\) | \(F\) | Theory bias | OLS mean | OLS bias | OLS SD | OLS RMSE | IV mean | IV bias | IV SD | IV RMSE |
|---|---|---|---|---|---|---|---|---|---|---|
| 0.00 | 1 | \(+0.800\) | 1.801 | \(+0.801\) | 0.026 | 0.802 | 0.756 | \(-0.244\) | 32.2 | 32.2 |
| 0.10 | 6 | \(+0.792\) | 1.791 | \(+0.791\) | 0.027 | 0.792 | 0.872 | \(-0.128\) | 4.391 | 4.393 |
| 0.15 | 13 | \(+0.782\) | 1.782 | \(+0.782\) | 0.027 | 0.783 | 0.764 | \(-0.236\) | 6.487 | 6.491 |
| 0.20 | 21 | \(+0.769\) | 1.769 | \(+0.769\) | 0.027 | 0.770 | 0.940 | \(-0.060\) | 0.380 | 0.385 |
| 0.30 | 46 | \(+0.734\) | 1.735 | \(+0.735\) | 0.028 | 0.735 | 0.975 | \(-0.025\) | 0.163 | 0.165 |
| 0.50 | 127 | \(+0.640\) | 1.639 | \(+0.639\) | 0.028 | 0.640 | 0.996 | \(-0.004\) | 0.091 | 0.091 |
| 1.00 | 500 | \(+0.400\) | 1.401 | \(+0.401\) | 0.027 | 0.402 | 0.999 | \(-0.001\) | 0.045 | 0.045 |
| 2.00 | 2006 | \(+0.160\) | 1.160 | \(+0.160\) | 0.019 | 0.161 | 1.000 | \(0.000\) | 0.022 | 0.022 |
2024).
| \(\pi\) | \(F\) | OLS limit | OLS median | OLS MdAE | IV median | IV 5% | IV 95% | IV MdAE | Far off |
|---|---|---|---|---|---|---|---|---|---|
| 0.00 | 1 | 1.800 | 1.801 | 0.801 | 1.796 | \(-1.670\) | 5.676 | 0.987 | 49.4% |
| 0.10 | 6 | 1.792 | 1.791 | 0.791 | 1.013 | \(-0.720\) | 1.537 | 0.295 | 11.5% |
| 0.15 | 13 | 1.782 | 1.782 | 0.782 | 1.011 | 0.131 | 1.370 | 0.200 | 3.8% |
| 0.20 | 21 | 1.769 | 1.769 | 0.769 | 0.995 | 0.415 | 1.293 | 0.154 | 1.1% |
| 0.30 | 46 | 1.734 | 1.734 | 0.734 | 0.993 | 0.677 | 1.199 | 0.106 | 0.0% |
| 0.50 | 127 | 1.640 | 1.639 | 0.639 | 1.001 | 0.839 | 1.131 | 0.061 | 0.0% |
| 1.00 | 500 | 1.400 | 1.401 | 0.401 | 1.000 | 0.923 | 1.069 | 0.031 | 0.0% |
| 2.00 | 2006 | 1.160 | 1.161 | 0.161 | 1.000 | 0.962 | 1.036 | 0.015 | 0.0% |
Four lessons stand out.
1. The OLS bias formula is exact. The “Theory bias” column of Table 7.2 (\(0.8/(\pi^2 + 1)\)) matches the simulated OLS bias to within Monte Carlo error at all eight values of \(\pi\). OLS is biased in the direction of \(\rho\) at every value of \(\pi\), including \(\pi = 0\). The bias decreases as \(\pi\) grows, because more of \(T\)’s variance then comes from the exogenous source \(Z\), but it never vanishes: at \(\pi = 2\) the OLS estimates still sit near \(1.16\), and the OLS 5%–95% range never comes within \(0.1\) of \(\beta\), while 90% of the IV estimates lie in \([0.962, 1.036]\). OLS is precise around the wrong value.
2. IV is consistent, but a weak instrument makes it unstable and can bias its median. At \(\pi = 0.10\) (mean \(F \approx 6\)) and \(\pi = 0.15\) (mean \(F \approx 13\)) the IV means in Table 7.2 are \(0.87\) and \(0.76\), while the IV medians in Table 7.3 are \(1.013\) and \(1.011\). The middle 90% of the estimates runs from \(-0.72\) to \(1.54\) at \(\pi = 0.10\), and \(11.5\%\) of the estimates miss \(\beta\) by more than 1. Since the estimator has no finite moments, the mean and SD entries have no population counterparts: they are set by a few replications whose estimated first stage is near zero, and they vary across seeds. Mean bias is undefined here. For the nonzero values of \(\pi\) in the tables the IV median is close to \(\beta = 1\), but weaker instruments also produce substantial median bias toward the OLS limit: with the same design and \(20{,}000\) draws, the IV median is about \(1.23\) at \(\pi = 0.05\) and \(1.49\) at \(\pi = 0.03\), and at \(\pi = 0\) it is \(1.8\) (Andrews and Armstrong 2017). The weak-instrument problem is not inconsistency: IV is consistent for each fixed \(\pi \neq 0\), but weak instruments produce unstable and median-biased estimates in finite samples.
3. Monte Carlo RMSE and median error disagree. By the Monte Carlo RMSE of these draws, OLS looks better than IV in the rows with \(\pi \le 0.15\) (for example \(4.39\) against \(0.79\) at \(\pi = 0.10\)); this is a fact about these draws, not a population crossover, since the population RMSE of IV is infinite in every row. By the median absolute error, IV is closer to \(\beta\) than OLS in every row with \(\pi \neq 0\) (for example \(0.295\) against \(0.791\) at \(\pi = 0.10\)). The two criteria disagree because of the tails: a weak instrument is usually close and occasionally far off. Even a design with mean \(F \approx 13\) produced \(3.8\%\) of estimates off by more than 1. This describes the design, not what to expect in one data set with an observed \(F\) of 13 (see the remark on the \(F\)-statistic below).
4. A strong instrument removes the dilemma. At \(\pi = 1.00\) (mean \(F \approx 500\)) the middle 90% of the IV estimates lies in \([0.923, 1.069]\) and none is far off, while OLS concentrates near \(1.40\). With a strong instrument, IV is accurate by every criterion in Table 7.3.
7.6 Multiple Instruments and Overidentification
This section gives only the identification-level intuition for using more than one instrument. The computational details of 2SLS with multiple instruments, GMM weighting, and the Sargan–Hansen \(J\)-test are deferred to Chapter 13.
When there are exactly as many instruments as endogenous variables (\(q = p\)), the model is just-identified: the IV assumptions pin down the causal parameter exactly, leaving no surplus identifying variation. When \(q > p\), the model is overidentified: the extra instruments impose additional moment restrictions beyond those needed for identification. Under the homogeneous-effect linear model of Section 7.3, every valid instrument must imply the same structural coefficient \(\beta\), so those extra restrictions are testable. Under heterogeneous treatment effects (Section 7.7), valid instruments can legitimately identify different LATEs because they shift treatment for different complier populations; the overidentification test then targets equality of probability limits across instruments, and a rejection admits more interpretations than instrument invalidity. In both cases, the Sargan–Hansen \(J\)-test (Sargan 1958; Hansen 1982) formalizes the mutual-consistency check; rejection indicates that at least one of the instruments either violates exogeneity or exclusion or identifies a different LATE, but does not localize which. The test statistic and its asymptotic distribution are derived in Chapter 13.
The terminology distinguishes the order condition — a counting requirement that \(q \geq p\) — from the rank condition, \(\operatorname{rank}\{\E(\tilde Z \tilde T^\top)\} = p\), where \(\tilde Z\) and \(\tilde T\) are the excluded instruments and the endogenous treatments after adjusting for \(X\). In words, the instruments must move the treatments in \(p\) linearly independent directions. Both conditions are necessary for identification, and counting alone is not enough: \(q\) irrelevant instruments satisfy the order condition. The order condition is checked by inspection; the rank condition can be assessed from the first-stage coefficient matrix. Both notions are developed formally in Chapter 13.
7.7 Heterogeneous Treatment Effects and the LATE Framework
7.7.1 Compliance Types
In the binary-instrument, binary-treatment setting, each unit’s response to the instrument is fully described by the pair of potential treatment decisions \((T_i(0), T_i(1))\): the treatment the unit would take under each value of \(Z\). This pair defines the unit’s compliance type — a latent causal classification, because \((T_i(0), T_i(1))\) is never jointly observed in data.
Definition 7.4 (Compliance Types (Angrist et al. 1996)) For binary \(Z, T \in \{0,1\}\), define the potential treatment \(T_i(z)\) as the treatment unit \(i\) would take under instrument value \(z\). The four compliance types are:
| Compliance type | \(T_i(0)\) | \(T_i(1)\) |
|---|---|---|
| Complier | 0 | 1 |
| Always-taker | 1 | 1 |
| Never-taker | 0 | 0 |
| Defier | 1 | 0 |
A complier takes treatment if and only if the instrument is switched on. An always-taker takes treatment regardless of \(Z\). A never-taker never takes treatment regardless of \(Z\). A defier does the opposite of what the instrument suggests.
The instrument \(Z\) shifts treatment only for compliers and defiers: always-takers and never-takers have the same treatment status regardless of \(Z\), so they contribute nothing to the denominator \(\E[T \mid Z{=}1] - \E[T \mid Z{=}0]\). This is the first indication that the Wald ratio will be driven by the units the instrument moves rather than by the full population.
7.7.2 The Monotonicity Assumption
The three core IV assumptions alone do not yield a clean causal interpretation for the Wald ratio when effects are heterogeneous. The difficulty is that the instrument may push some units toward treatment and others away from it: in the presence of defiers, the numerator and denominator of the Wald ratio conflate effects in opposite directions. A fourth assumption rules out this ambiguity.
Definition 7.5 (Monotonicity (Imbens and Angrist 1994)) The treatment assignment is monotone in \(Z\) if \[T_i(1) \;\geq\; T_i(0) \quad \text{for all } i.\] Equivalently: there are no defiers in the population.
Interpretation. Monotonicity is not a generic law of causal inference. It is a design-specific claim about how this particular instrument changes treatment behavior. Switching the instrument from \(0\) to \(1\) may induce some units to take treatment (compliers) and leave others unaffected (always-takers or never-takers), but it should not reverse anyone’s treatment decision. This is most plausible when the instrument is a randomized encouragement, access rule, or administrative assignment mechanism. In many observational IV settings the no-defiers assumption is substantively harder to defend and requires explicit justification. Because it compares \(T_i(1)\) and \(T_i(0)\) for the same unit, no data set can confirm it; it can be contradicted, however. Under exogeneity the first stage equals \(P(\text{complier}) - P(\text{defier})\), so monotonicity implies \(P(T{=}1 \mid Z{=}1) \ge P(T{=}1 \mid Z{=}0)\), and a negative first stage rules it out. Example 7.4 gives a sharper check.
7.7.3 The LATE Theorem
Under the three core IV assumptions, heterogeneous treatment effects, and monotonicity, the Wald ratio derived in Section 7.3 no longer identifies the ATE. Instead it recovers the average treatment effect for the units whose treatment status is actually changed by the instrument — the compliers. This is the Local Average Treatment Effect (LATE).
The effect is local not because it is estimated with nearby observations, but because it pertains to a local margin of behavioral response defined by the instrument itself: it is the average effect precisely for the subpopulation that the instrument moves.
Theorem 7.1 (LATE Theorem (Imbens and Angrist 1994)) Let \(Z\) and \(T\) be binary, with \(0 < P(Z = 1) < 1\), and suppose the following hold:
- Consistency: \(T = T(Z)\) and \(Y = Y(T, Z)\);
- Exogeneity (PO form): \(Z \indep \{T(z),\, Y(T(z), z)\}\) for each \(z\), that is, Equation 7.1 without \(X\);
- Exclusion: \(Y_i(t, z) = Y_i(t)\) for all \(z\) (i.e., \(Z\) enters \(Y\) only through \(T\));
- Relevance: \(\E[T(1) - T(0)] \neq 0\);
- Monotonicity: \(T_i(1) \geq T_i(0)\) for all \(i\).
Then the Wald estimand identifies the Local Average Treatment Effect (LATE): \[\frac{\E[Y \mid Z{=}1] - \E[Y \mid Z{=}0]}{\E[T \mid Z{=}1] - \E[T \mid Z{=}0]} \;=\; \E\!\bigl[Y(1) - Y(0) \;\big|\; T_i(1) > T_i(0)\bigr] \;\equiv\; \tau_{\mathrm{LATE}}. \tag{7.8}\]
That is, the Wald estimand identifies the average causal effect for compliers only. When covariates are present, the same result holds at each value \(x\), with all assumptions and the Wald formula stated conditionally on \(X = x\). Combining the conditional effects into a single estimand requires weights; how estimators such as 2SLS weight them is taken up in Chapter 13.
Example 7.4 (Recovering Complier Means: A Reminder Letter) A clinic mails a reminder letter (\(Z = 1\)) to a randomly chosen half of its patients; \(T = 1\) if a patient is vaccinated against influenza, and \(Y = 1\) if the patient is hospitalized during the winter. The table gives illustrative population frequencies per 1,000 patients in each assignment group; sampling variability is ignored.
| Letter (\(Z=1\)): vaccinated | Letter (\(Z=1\)): not vaccinated | No letter (\(Z=0\)): vaccinated | No letter (\(Z=0\)): not vaccinated | |
|---|---|---|---|---|
| patients | 600 | 400 | 400 | 600 |
| hospitalized | 26 | 74 | 16 | 104 |
The Wald ratio is \((0.100 - 0.120)/(0.60 - 0.40) = -0.10\). Under the assumptions of Theorem 7.1, the types can be recovered by counting. The 400 patients vaccinated without a letter are always-takers, and the 400 unvaccinated patients with a letter are never-takers, so each arm contains 200 compliers. By randomization, the always-takers in the letter arm resemble those in the other arm, of whom 16 were hospitalized. Hence \(26 - 16 = 10\) of the 200 compliers are hospitalized when vaccinated, a rate of \(0.05\). Likewise, never-takers account for 74 of the 104 hospitalizations among unvaccinated patients without a letter, so 30 compliers are hospitalized when not vaccinated, a rate of \(0.15\). Thus \(\tau_{\mathrm{LATE}} = 0.05 - 0.15 = -0.10\), as the theorem states (Imbens and Rubin 1997).
Three further lessons follow. First, the naive comparison of vaccinated and unvaccinated patients, \(42/1000 - 178/1000 = -0.136\), pools different compliance types under different treatment states. The table gives \(\E\{Y(1) \mid \mathrm{at}\} = 16/400 = 0.04\) and \(\E\{Y(0) \mid \mathrm{nt}\} = 74/400 = 0.185\), but not the untreated risk of always-takers. The difference between the naive comparison and the LATE can reflect both selection and treatment-effect heterogeneity, and the table does not separate the two. Second, the recovered counts are a check on the model: in population frequencies, a negative complier count, or one larger than the number of compliers, would contradict the IV assumptions with monotonicity. In a sample, a negative estimate can arise by chance; formal tests account for sampling variability (Kitagawa 2015). Third, the data never show \(Y(0)\) for always-takers or \(Y(1)\) for never-takers. With \(a = \E\{Y(0) \mid \mathrm{at}\}\) and \(n = \E\{Y(1) \mid \mathrm{nt}\}\) unrestricted in \([0, 1]\), \[\mathrm{ATE} = 0.2\,(-0.10) + 0.4\,(0.04 - a) + 0.4\,(n - 0.185)\] can be anywhere in \([-0.478,\ 0.322]\). The LATE is identified; the ATE is not (Chapter 9 develops such bounds). Because hospitalization is binary, a common individual effect of \(-0.10\) is impossible, so the constant-effect reading of Framework 1 is not available and \(-0.10\) is best read as a 10-percentage-point reduction in hospitalization risk among compliers.
7.8 Interpreting IV Estimands
The two frameworks — linear homogeneous effects (Section 7.3) and the LATE framework (Section 7.7) — give the Wald estimand different interpretations. This section synthesizes those interpretations and clarifies when they agree, when they disagree, and what the difference means for applied work.
7.8.1 What the Two Frameworks Say
| Framework 1 (linear, homogeneous) | Framework 2 (heterogeneous effects) | |
|---|---|---|
| Key assumption | \(\tau_i = \beta\) for all \(i\) | Monotonicity; no defiers |
| What IV identifies | \(\beta = \mathrm{ATE} = \mathrm{ATT} = \mathrm{LATE}\) | \(\tau_{\mathrm{LATE}} = \E[\tau_i \mid \text{complier}]\) |
| Estimand depends on instrument? | No (same \(\beta\) regardless of \(Z\)) | Yes (different \(Z\) \(\Rightarrow\) different compliers \(\Rightarrow\) different LATE) |
| Equals the ATE? | Yes | Not in general; yes if the three types have equal mean effects, or if everyone is a complier (Section 7.8.2) |
The two frameworks overlap rather than nest: constant effects do not imply monotonicity, and monotonicity does not imply constant effects. When both hold, the Wald ratio equals both the ATE and the LATE, and the instrument affects only identification, not the estimand. Framework 2 is the more realistic setting for a binary treatment. In applied work, the default interpretation of the Wald estimand is the LATE; the ATE interpretation requires the additional homogeneity argument of Framework 1.
7.8.2 When Does LATE Equal ATE?
LATE equals ATE only under additional structure, most notably treatment-effect homogeneity or special forms of heterogeneity that make complier effects representative of the full population. Neither condition should be assumed without argument.
In general, \(\tau_{\mathrm{LATE}} \neq \mathrm{ATE}\) when treatment effects are heterogeneous and some units are not compliers. To see this, decompose the ATE by compliance type: \[\mathrm{ATE} = P(\mathrm{co})\,\E[\tau_i \mid \mathrm{co}] + P(\mathrm{at})\,\E[\tau_i \mid \mathrm{at}] + P(\mathrm{nt})\,\E[\tau_i \mid \mathrm{nt}],\] where \(\mathrm{co}\), \(\mathrm{at}\), and \(\mathrm{nt}\) abbreviate complier, always-taker, and never-taker. The LATE equals only the first term divided by its probability weight. Since \(P(\mathrm{co}) + P(\mathrm{at}) + P(\mathrm{nt}) = 1\), \[\mathrm{ATE} - \tau_{\mathrm{LATE}} = P(\mathrm{at})\bigl(\E[\tau_i \mid \mathrm{at}] - \tau_{\mathrm{LATE}}\bigr) + P(\mathrm{nt})\bigl(\E[\tau_i \mid \mathrm{nt}] - \tau_{\mathrm{LATE}}\bigr),\] so the two coincide exactly when this weighted sum is zero. Two sufficient conditions are:
- Mean treatment effects are equal across compliance types (\(\E[\tau_i \mid \mathrm{co}] = \E[\tau_i \mid \mathrm{at}] = \E[\tau_i \mid \mathrm{nt}]\)) — a strict weakening of the constant-effect assumption of Section 7.3, but still a nontrivial restriction on heterogeneity; or
- Everyone is a complier (\(P(\mathrm{at}) = P(\mathrm{nt}) = 0\)), which would require \(Z\) to perfectly determine \(T\).
Otherwise, equality holds only if the deviations of always-takers and never-takers happen to cancel, an untestable coincidence. In practice, none of these conditions is likely to hold exactly. The LATE is a well-defined, identifiable parameter, but it is not the ATE.
Example 7.5 (Same Observables, Different ATEs) The following construction makes the remark “Instrument Validity Does Not Fix the Interpretation” in Section 7.2 and the nonidentification remark above concrete. Two distinct data-generating processes satisfy all three IV assumptions and produce identical observable statistics, yet imply different ATEs. No amount of data can distinguish them without a fourth structural assumption.
Observable statistics. Let \(Z, T \in \{0,1\}\) and let \(Y\) be a continuous outcome. Suppose the joint distribution of \((Y, T, Z)\) satisfies \[\begin{aligned} \E[T \mid Z{=}1] - \E[T \mid Z{=}0] &= 0.2 \quad \text{(first stage)}, \\ \E[Y \mid Z{=}1] - \E[Y \mid Z{=}0] &= 0.1 \quad \text{(reduced form)}, \end{aligned}\] giving a Wald ratio of \(0.1/0.2 = 0.5\). Both DGPs share the same compliance structure — under monotonicity (no defiers), \(P(\mathrm{co}) = 0.2\), \(P(\mathrm{at}) = 0.4\), \(P(\mathrm{nt}) = 0.4\) — though under DGP A the compliance types are simply a convenient labeling; what drives identification there is the constant-effect restriction, not monotonicity.
DGP A: Constant treatment effects. Every unit has the same effect \(\tau_i = 0.5\). Then \[\text{reduced form} = P(\mathrm{co}) \cdot \tau_{\mathrm{co}} = 0.2 \times 0.5 = 0.1 \;\checkmark, \qquad \mathrm{ATE} = 0.5.\]
DGP B: Heterogeneous treatment effects with monotonicity. Effects differ by compliance type: \(\tau_{\mathrm{co}} = 0.5\), \(\tau_{\mathrm{at}} = 0\), \(\tau_{\mathrm{nt}} = 0\). Then \[\text{reduced form} = P(\mathrm{co}) \cdot \tau_{\mathrm{co}} = 0.2 \times 0.5 = 0.1 \;\checkmark, \qquad \mathrm{ATE} = 0.2 \times 0.5 + 0.4 \times 0 + 0.4 \times 0 = 0.1.\]
What this shows. Both DGPs produce the same first stage, the same reduced form, and therefore the same Wald ratio of \(0.5\). Yet the ATE is \(0.5\) under DGP A and \(0.1\) under DGP B — a fivefold difference. The three IV assumptions do not distinguish between them. The fourth assumption is what resolves the ambiguity: under DGP A, the constant effects assumption makes the Wald ratio equal to the ATE; under DGP B, the monotonicity assumption makes the Wald ratio equal to the LATE (\(= 0.5\)) for compliers, which is a different quantity from the ATE (\(= 0.1\)). Committing to one fourth assumption or the other changes not the estimator but what it estimates.
Only means are displayed, but the full observed distributions can be made identical as well. Under monotonicity the data never reveal \(Y(0)\) for always-takers or \(Y(1)\) for never-takers (Example 7.4), and these are exactly the quantities on which the two DGPs differ.
7.8.3 Different Instruments, Different Estimands
Because the LATE is specific to the complier population, and different instruments select different complier populations, two valid instruments for the same treatment can legitimately identify different LATEs. This is a precise, substantive fact — not a contradiction. Different instruments can legitimately identify different causal effects because they shift treatment for different margins of the population; the diversity of LATEs is informative about treatment effect heterogeneity, not a symptom of model failure.
Example 7.6 (Compulsory Schooling Laws vs. Distance to College) Two classic instruments for years of schooling are (i) compulsory schooling laws (Angrist and Krueger 1991) and (ii) distance to the nearest college (Card 1995). The compliers for instrument (i) are individuals at the margin of dropping out before the compulsory leaving age — typically lower-income students. The compliers for instrument (ii) are students deterred from college by geographic distance — again, disproportionately lower-income. Both instruments identify the return to schooling for their respective complier populations, and the LATEs can legitimately differ even if both instruments are valid.
The dependence of the LATE on the instrument is sometimes described as a limitation of IV. It is better understood as a precise statement about what question is being answered. A researcher using compulsory schooling laws is estimating the return to schooling for students at the compulsory leaving margin; a researcher using distance to college is estimating the return for students deterred by geography. These are different causal questions, and it is informative — not troubling — that they can yield different answers.
7.8.4 The Policy Relevance of LATE
Two numbers answer different policy questions. For an encouragement policy such as the reminder letter of Example 7.4, the reduced form measures the effect per person encouraged: there, \(p_{\mathrm{C}}\,\tau_{\mathrm{C}} = 0.20 \times (-0.10) = -0.02\), a reduction of 2 percentage points per patient sent a letter. The LATE measures the effect of treatment among the people whose take-up the encouragement changes: a reduction of 10 percentage points among patients vaccinated because of the letter. Applying either number to a new population requires comparable responses and effects. The LATE is most informative when the contemplated intervention changes treatment for the same kind of people as the instrument did.
Evaluating universal treatment requires effects for the groups whose treatment the instrument does not change. The ATE compares treating everyone with treating no one; a mandate compared with the current pattern of take-up is a different contrast. When such quantities are required, IV alone is insufficient under heterogeneous effects. Additional assumptions — such as an explicit model of treatment effect heterogeneity, or a second instrument that identifies effects for a different subpopulation — are needed to extrapolate from the LATE to the ATE.
7.8.5 IV versus Back-Door Adjustment
The two identification strategies of Chapters 6 and 7 differ in what they require, what they identify, and how they fail; Table 7.5 collects the comparison. Back-door adjustment requires an observed set \(X\) that blocks every back-door path from \(T\) to \(Y\), and fails when a path through an unobserved \(U\) is left open. IV tolerates unobserved confounding but requires an exogenous source of variation in \(T\) with no other causal route to \(Y\), and fails when the instrument is confounded or has a side channel, with the error \(\delta/\pi\) of Section 7.4 magnified by a weak first stage. Which assumption is more plausible in a given study decides the choice.
| Dimension | Back-door / propensity score | Instrumental variables |
|---|---|---|
| Core assumption | \(X\) is a valid back-door adjustment set, so \(Y(t) \indep T \mid X\) for each \(t\) | Valid instrument: relevance, exogeneity, exclusion |
| Residual confounding | Ruled out after adjusting for \(X\) | Permitted: IV routes around \(U\) |
| Estimand | ATE, ATT, or ATC depending on design and overlap; all coincide under homogeneity | LATE (compliers only); reduces to a common \(\beta\) under homogeneous effects |
| Testability | Unconfoundedness is untestable; overlap is testable | First stage testable; exogeneity and exclusion not separately testable |
| Main threat | A back-door path left open by \(X\) | Exclusion restriction violation |
| Identifies ATE? | Yes, under strong ignorability | Not in general; yes under constant effects or equal mean effects across compliance types |
| Typical setting | Rich administrative or survey data | Natural experiment; RCT with noncompliance; policy change |
When a valid instrument and a sufficient adjustment set \(X\) are both available, comparing the two estimates can be informative, but disagreement does not by itself say which method is wrong: the two strategies typically target different estimands (the ATE or ATT for back-door adjustment, the LATE for IV) and rest on different assumptions. Agreement is reassuring under treatment-effect homogeneity, and neither required nor sufficient otherwise.
The Hausman (1978) endogeneity test operationalizes this comparison: under the null hypothesis that \(T\) is exogenous given \(X\), and with constant effects, both the OLS and IV estimators are consistent for the same \(\beta\), and a large discrepancy is evidence of endogeneity. Under the null and standard regularity conditions, an appropriately scaled quadratic form in the discrepancy \(\hat\beta_{\mathrm{IV}} - \hat\beta_{\mathrm{OLS}}\) is asymptotically \(\chi^2_p\)-distributed, where \(p\) is the number of components of \(T\) tested for endogeneity; the formal construction is given in Chapter 13. Under constant effects, rejection means at least one strategy is inconsistent; it does not identify which.
7.9 Practical Guidance on Defending an IV Design
There is no algorithm for finding a valid instrument; credible instruments arise from institutional knowledge and careful reasoning about the data-generating process. A strong IV design is defended primarily by institutional knowledge, design logic, and causal structure; statistical diagnostics are supportive but secondary.
A researcher proposing an instrument should be able to answer five questions explicitly.
- What exactly is the instrument? Specify \(Z\) precisely: its source of variation, the level at which it varies, and the population to which it applies.
- Why does it shift treatment? Articulate the causal mechanism by which \(Z\) moves \(T\). Relevance can be verified empirically with the first-stage \(F\)-statistic, but the \(F\)-statistic is a diagnostic for instrument strength, not a substitute for a causal account of the \(Z \to T\) link.
- Why is it as-if random relative to latent outcome determinants? Argue why \(Z\) is unrelated to the unobserved causes of \(Y\). The most credible sources are designed randomization (lotteries, randomized encouragement), natural experiments with institutional quasi-randomness (policy discontinuities, geographic boundaries, biological quirks), and shift-share designs (Bartik 1991; Goldsmith-Pinkham et al. 2020). Placebo regressions on pre-determined outcomes provide partial — but not definitive — evidence.
- Why can it affect the outcome only through treatment? The exclusion restriction cannot be tested on its own, so it must rest on a structural argument that no direct path \(Z \to Y\) exists. A useful diagnostic is to ask: how large would the direct effect \(\delta\) have to be, relative to the first-stage coefficient \(\pi\), to overturn the estimated causal effect? When the first stage is weak, the answer is: not very large at all.
- What population margin does it shift? Identify the complier population — the units whose treatment status changes with \(Z\). This determines the LATE that is being identified and governs the external validity of the estimates for other populations or policy margins.
7.10 Applied Example: Charter School Lotteries and the KIPP Lynn Study
This example illustrates a canonical randomized-encouragement IV design. The key distinction is that the lottery randomizes offer status, not actual treatment. Winning the lottery does not mechanically force a student to attend KIPP, and losing the lottery does not make later attendance impossible in all cases. Thus the lottery offer is the instrument \(Z\), while actual years of KIPP attendance is the endogenous treatment \(S\). Here \(S\) plays the role of the generic treatment variable \(T\) used throughout the rest of this chapter; the paper’s notation is retained to keep the empirical discussion close to the source.
This distinction is exactly what makes the design an IV design rather than a randomized controlled trial on treatment itself. The lottery generates exogenous variation in access to KIPP, and the IV analysis uses only the portion of attendance variation induced by that randomized offer to identify a causal effect.
7.10.1 Setting and Instrument
KIPP (Knowledge Is Power Program) schools follow a “No Excuses” model: extended school days, a longer academic year, selective teacher hiring, and strict behavioral norms. KIPP Academy Lynn was substantially oversubscribed beginning in 2005. Massachusetts law requires oversubscribed charter schools to select students by lottery, so the school conducted randomized admissions lotteries from 2005 through 2008. The treatment is years of KIPP attendance \(S\); in the panel structure of the data this is denoted \(s_{igt}\), the number of calendar years student \(i\) has spent at KIPP by the time of test \((g, t)\), with partial years counted as full years — a multivalued, endogenous variable, because families self-select into applying and attending. The outcome \(Y_{igt}\) is the student’s standardized score on the Massachusetts Comprehensive Assessment System (MCAS), normalized to mean zero and standard deviation one within each subject–grade–year cell statewide. ::: {.content-visible when-format=“html”}
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7.10.2 Mapping the Three Assumptions to the KIPP Context
The figure above displays the causal structure. The KIPP lottery design makes the logic of the three IV assumptions unusually transparent; the three paragraphs below trace each assumption to a specific feature of the design.
One point deserves emphasis before proceeding. Relevance and exogeneity are especially natural in a lottery-based design: because lottery sequence numbers are randomly assigned within cohort, offer status is independent of the latent determinants of achievement by construction. Exclusion, however, still requires institutional argument. Random assignment of the instrument does not, by itself, imply that the instrument has no direct effect on the outcome — it only guarantees that the instrument is exogenous.
Relevance. The lottery offer must shift years of KIPP attendance. Lottery winners were offered a seat and about 80 percent accepted; few lottery losers attended KIPP. The first-stage regression of \(s_{igt}\) on \(Z_i\) (with year and grade controls) yields a coefficient of approximately \(1.2\): at the time of each MCAS exam, lottery winners had spent about 1.2 more years at KIPP than lottery losers. The first-stage \(F\)-statistic is far above conventional thresholds. The first stage is less than the theoretical maximum because compliance is partial (some winners do not attend; some losers find entry through later cohorts or attrition slots) and the follow-up window captures students at different points in their KIPP tenure.
Exogeneity. The lottery offer must be independent of all potential outcomes and potential treatments within each application cohort, which gives the single-world form Equation 7.1 there. Because offer status was determined by randomly drawn lottery-sequence numbers, this independence holds by design — an especially strong basis for exogeneity compared to most observational IV applications. The authors check for evidence against it: a joint test of covariate balance across lottery winners and losers yields a \(p\)-value of \(0.615\) for demographic characteristics and baseline test scores, consistent with the null of no pre-lottery differences (Table 1 of Angrist et al. (2012)). Such a test can contradict exogeneity; it cannot verify it. Pre-lottery variables are used for the balance check precisely because post-lottery variables such as LEP or SPED classification may themselves be affected by school attended.
Exclusion. The lottery offer must affect test scores only through KIPP attendance, not through any direct channel. Because the offer merely provides access to a school — it does not itself deliver instruction — this restriction is institutionally plausible. One potential violation is a discouragement effect: losing the lottery might demoralize students, suppressing their achievement regardless of where they enroll. The authors address this by noting that the scores of lottery losers are typical of demographically comparable students in Lynn, which is inconsistent with large discouragement effects.
7.10.3 First Stage, Reduced Form, and the 2SLS Estimand
The equations below are used here only to illustrate the components of the Wald/2SLS logic — first stage, reduced form, and their ratio. Formal estimation theory for 2SLS, including asymptotic variance and cluster-robust inference, is deferred to Chapter 13.
The structural equation for test scores is \[y_{igt} = \alpha_t + \beta_g + \sum_j \delta_j d_{ij} + \gamma' X_i + \theta\, s_{igt} + \varepsilon_{igt}, \tag{7.9}\] where \(\alpha_t\) and \(\beta_g\) are year-of-test and grade-of-test fixed effects, \(d_{ij}\) are application-cohort dummies (cohort membership determines the probability of winning, so cohort is an essential control), \(X_i\) is a vector of baseline demographics, and \(\theta\) is the causal effect of interest per year at KIPP. We write \(\theta\) here rather than \(\rho\) (as in Angrist et al. (2012)) to avoid clashing with the endogeneity correlation parameter of the same name in Section 7.3 through Section 7.5. The first-stage equation is \[s_{igt} = \lambda_t + \kappa_g + \sum_j \mu_j d_{ij} + \Gamma' X_i + \pi Z_i + \eta_{igt}. \tag{7.10}\] The model is just-identified (one excluded instrument per endogenous variable) with the same controls in both stages, so the 2SLS estimator of \(\theta\) equals the ratio of the reduced-form coefficient on \(Z_i\) to the first-stage coefficient \(\pi\), as the remark “From the Estimand to an Estimator” in Section 7.3 explains.
Estimates from Angrist et al. (2012) (their Table 4, the specification with demographic and baseline-score controls) are summarized in Table 7.6.
| Subject | First stage | Reduced form | 2SLS |
|---|---|---|---|
| Math | \(1.221\) | \(0.430\) | \(0.352\) |
| \((0.068)\) | \((0.067)\) | \((0.053)\) | |
| ELA | \(1.228\) | \(0.164\) | \(0.133\) |
| \((0.068)\) | \((0.073)\) | \((0.059)\) |
The 2SLS estimates are weighted average gains per additional year at KIPP induced by the offer: about \(0.35\) standard deviations in math and \(0.13\) in ELA. The reduced-form estimate for math (\(0.43\sigma\)) is larger than the 2SLS estimate (\(0.35\sigma\)) because the first stage exceeds \(1\): by the test dates, lottery winners had accumulated about 1.2 more years at KIPP than losers. The reduced form regression, the 2SLS estimator, and its asymptotic theory are all developed in Chapter 13.
7.10.4 LATE Interpretation
The lottery design identifies the causal effect of KIPP attendance only for the students whose attendance is changed by the lottery offer. Because the treatment is years at KIPP rather than a binary enrollment indicator, “changed” means that the offer alters the number of years accumulated; under the IV assumptions and monotonicity in years of attendance, \(\theta\) is a weighted average of the effects of additional years induced by the offer (the remark above). In the binary language of Section 7.7, compliance is partial in both directions: some lottery winners do not enroll (never-takers) and some losers find entry later through attrition slots (always-takers at the extensive margin), and with years as the treatment both margins reappear in the number of years a student stays.
This is the key interpretive point of the example. The 2SLS estimand \(\theta\) is not the effect of KIPP on all students in Lynn, nor on all applicants — it is the average per-year treatment effect for the lottery compliers, the specific margin of students whose enrollment decision is altered by randomized access to the school.
An important feature of this LATE is that it may differ from the effect the school would have on a randomly selected Lynn student who was not part of the applicant pool. KIPP applicants already had parents motivated enough to apply. The authors find that KIPP applicants have baseline test scores slightly lower than the LPS average (Table 1 of Angrist et al. (2012)), so the applicant pool is not positively selected on prior achievement, but it may still be selected on parental engagement in ways that affect how students respond to the KIPP environment.
The design is therefore strongest not because it identifies a universally generalizable effect, but because it identifies a clearly interpretable causal effect for a well-defined subpopulation under highly credible exogeneity.
7.10.5 Treatment Effect Heterogeneity
Subgroup analysis reveals that the LATE varies substantially across observable student characteristics. Reading gains (\(\approx 0.13\sigma\) overall) are driven almost entirely by students classified as having limited English proficiency (LEP, \(\approx 0.43\sigma\)) and special education needs (SPED, \(\approx 0.27\sigma\)); non-LEP, non-SPED students show negligible ELA gains. Math effects are large and positive across all subgroups but are largest for LEP and lower-achieving students. An interaction model that adds the product of baseline score with years at KIPP — identified by including \(Z_i \times \text{baseline score}\) as a second instrument — yields a significantly negative interaction term in both subjects, about \(-0.11\) in math and \(-0.17\) in reading: a baseline score one standard deviation lower is associated with an additional gain per year at KIPP of about \(0.11\sigma\) in math and \(0.17\sigma\) in reading.
These findings connect directly to Section 7.8.3: were we to define separate subgroup-specific instruments (LEP-lottery and non-LEP-lottery), each would identify a distinct subpopulation LATE. Pooled, the 2SLS estimate is a weighted average of these subgroup effects, with weights that depend on each subgroup’s share of the sample and on how many additional years the offer induces there; with covariates entering linearly and lottery odds differing across cohorts, the exact weights are those of Chapter 13. This heterogeneity is not a nuisance detail; it is exactly why IV estimates must be interpreted together with the margin of compliance they capture.
The KIPP example ties together the main lessons of this chapter. All three IV assumptions are visible in the design: relevance is confirmed by a strong, precisely estimated first stage; exogeneity within the applicant sample (conditional on application cohort) follows from the randomization protocol; and exclusion rests on an institutional argument that the lottery offer affects achievement only through attendance. Because compliance is partial — the lottery shifts actual attendance but does not fully determine it — the resulting estimate is a LATE for lottery compliers, not an ATE for all applicants or all students in Lynn. A lottery-based IV design is strongest not because it answers every causal question, but because it answers a clearly defined causal question for a clearly defined subpopulation.
7.11 Summary
IV identifies effects from exogenous treatment variation. When back-door adjustment fails because an unobserved \(U\) creates a path \(T \leftarrow U \rightarrow Y\), a valid instrument \(Z\) identifies the causal effect by exploiting only the component of treatment variation that \(Z\) induces. IV does not block the confounding path — it avoids it by isolating exogenous variation and ignoring the rest.
Three assumptions, ordered by testability. Relevance — that \(Z\) causally shifts \(T\) — can be assessed with the first-stage \(F\)-statistic, though the \(F\)-statistic is a sample diagnostic, not the assumption itself. Exogeneity and exclusion are primarily substantive: exogeneity requires that \(Z\) carries no information about latent outcome determinants other than through \(T\); exclusion requires that \(Z\) has no direct effect on \(Y\). Both must be defended by institutional knowledge, design logic, and causal structure — statistical diagnostics are supportive but secondary. Each violated assumption produces a distinct, quantifiable bias in the Wald estimand, amplified by weak instruments (Section 7.4).
Framework 1: homogeneous-effect SEM \(\Rightarrow\) Wald identifies \(\beta\). Under constant treatment effects and the linear structural model, the Wald estimand identifies the single causal parameter \(\beta\), which equals the ATE, ATT, and LATE simultaneously. The identification follows from a four-step argument (exogeneity, exclusion, the moment equation, relevance) using the reduced form and first stage (Section 7.3).
Framework 2: heterogeneity + monotonicity \(\Rightarrow\) Wald identifies LATE. Under heterogeneous treatment effects and the monotonicity assumption, the Wald estimand identifies the average treatment effect for compliers only — those whose treatment status changes with the instrument, a latent subgroup defined by potential treatment statuses \((T(0), T(1))\), not by observable characteristics (Section 7.7 and Section 7.8).
Different instruments identify different effects. The LATE depends on the instrument through the complier population it selects. Different instruments can legitimately identify different causal effects because they shift treatment for different margins of the population. This is informative about treatment effect heterogeneity, not a contradiction. LATE equals ATE only under additional structure, most notably treatment-effect homogeneity (Section 7.8).
IV versus back-door adjustment. The two strategies have complementary failure modes: back-door adjustment fails when confounders are unobserved; IV fails when the exclusion restriction is violated or the instrument is not truly exogenous. IV identifies the LATE (not the ATE) under heterogeneous effects; back-door adjustment identifies the ATE or ATT. They are tools for different identification problems, not competitors (Section 7.8.5).
Applied example: the KIPP Lynn lottery. Angrist et al. (2012) use a randomized admissions lottery as a canonical randomized-encouragement instrument for years of charter school attendance. Within the applicant sample, conditional on application cohort, random assignment of the offer supports exogeneity; exclusion is defended institutionally; relevance is confirmed by a first-stage coefficient of \(1.2\). The estimates identify the LATE for lottery compliers — \(0.35\sigma\) per year in math, \(0.13\sigma\) in ELA — with the largest gains for LEP, SPED, and low-baseline-score students, illustrating that the margin of compliance shapes which LATE is recovered (Section 7.10).
Estimation deferred to Chapter 13. This chapter establishes what IV identifies and under what assumptions. How the Wald ratio is estimated from finite data — the reduced form regression, two-stage least squares, asymptotic inference, and overidentification tests — is the subject of Chapter 13.
Problems
1. The three IV assumptions in three languages. Consider the DAG \(\{Z \to T,\; T \to Y,\; U \to T,\; U \to Y,\; X \to T,\; X \to Y,\; X \to Z\}\) with \(U\) unobserved.
- List all back-door paths from \(T\) to \(Y\). Does \(X\) alone satisfy the back-door criterion? Explain.
- Verify the three IV assumptions using \(d\)-separation: (i) Relevance: identify the directed path from \(Z\) to \(T\) that makes relevance possible, and explain why the absence of \(d\)-separation does not by itself guarantee a nonzero first stage. (ii) Exogeneity: show \(Z \indep U \mid X\) in \(\Gcal\). (iii) Exclusion: show \(Y \indep Z \mid T, X\) in \(\Gcal_{\overline{T}\,\overline{Z}}\) (Rule 3), and explain why the same independence in \(\Gcal_{\overline{T}}\) requires exogeneity as well.
- Now add the arrow \(Z \to Y\) to the DAG. Which IV assumption is violated? Show explicitly which step of the Wald derivation in Section 7.3 breaks down.
- Translate each of the three IV assumptions into the structural language: write the equations for \(T\) and \(Y\) and identify which coefficient restriction corresponds to each assumption.
2. Bias under assumption violations. Let \(Z\) be binary with \(0 < P(Z{=}1) < 1\), and let \(Y = \beta T + \varepsilon\) and \(T = \pi Z + \eta\) with \(\E[\varepsilon \mid Z] = \E[\eta \mid Z] = 0\) and \(\pi \neq 0\).
- Starting from \(\E[Y \mid Z{=}1] - \E[Y \mid Z{=}0]\), substitute the structural equation for \(Y\) and simplify. What role does exogeneity play?
- Show that \(\E[T \mid Z{=}1] - \E[T \mid Z{=}0] = \pi\) in the linear first-stage model. What role does relevance play?
- Derive the Wald estimand and confirm it equals \(\beta\).
- Now suppose the exclusion restriction fails and \(Y = \beta T + \delta Z + \varepsilon\) with \(\delta \neq 0\). Derive the probability limit of the Wald estimator. Confirm the bias formula from Section 7.4.
- Suppose instead that exogeneity fails: \(\E[\varepsilon \mid Z] = cZ\) for some constant \(c \neq 0\). Derive the probability limit of the Wald estimator and express the bias in terms of \(c\) and \(\pi\). Compare the structure of this bias with the exclusion violation bias.
3. Order, rank, and the limits of overidentification. Consider a model with one endogenous variable \(T\) and two instruments \(Z_1\) and \(Z_2\), both satisfying exogeneity and exclusion.
- State the order condition and verify it is satisfied.
- State the rank condition for this model. Show that it fails if and only if neither instrument moves \(T\) after adjusting for \(X\), and that two perfectly collinear instruments that are each relevant satisfy it (one of them is then redundant, which is a different matter from failure of identification).
- Explain intuitively why a second valid instrument can improve estimation precision, and when it adds nothing.
- Now suppose \(Z_1\) is valid but \(Z_2\) violates the exclusion restriction. The Sargan–Hansen \(J\)-test is applied. Under what conditions does the \(J\)-test have power to detect \(Z_2\)’s invalidity? Under what conditions does the test fail to detect it?
- Why does passing the \(J\)-test not confirm that both \(Z_1\) and \(Z_2\) are valid? Give a concrete example of a situation in which both instruments are invalid and the \(J\)-test has no power.
4. Compliance types and the LATE. In a binary instrument, binary treatment study, suppose the population has the following composition: 30% compliers with average treatment effect \(\tau_c = 6\); 25% always-takers with \(\tau_a = 3\); 45% never-takers with \(\tau_n = 1\); no defiers.
- Compute \(P(\text{complier}) = \E[T \mid Z{=}1] - \E[T \mid Z{=}0]\).
- Compute the ATE as a weighted average of \(\tau_c\), \(\tau_a\), \(\tau_n\) with appropriate weights.
- The Wald estimand equals \(\tau_c = 6\). By how much does this overstate the ATE, and why?
- A second study uses a different binary instrument \(Z'\) with a complier population of 50% and a LATE of 2. Is this contradictory? What can you infer about the relative treatment effect in the two complier populations?
- Explain, using compliance type language, why the denominator of the Wald estimand equals \(P(\text{complier})\).
5. The exclusion restriction: plausibility and violations. Evaluate the exclusion restriction for each of the following proposed instruments. For each, (i) state whether the restriction is plausible and why; (ii) describe a specific mechanism by which it could be violated; and (iii) assess whether the violation would bias the IV estimate upward or downward.
- Instrument: rainfall in the home region of a politician, used as an instrument for government infrastructure spending. Outcome: local economic growth.
- Instrument: distance to the nearest hospital, used as an instrument for hospital admission. Outcome: 30-day mortality.
- Instrument: a randomly assigned financial incentive to enroll in a health screening program, used as an instrument for screening uptake. Outcome: health status two years later.
- Instrument: lottery number in the Vietnam-era draft lottery, used as an instrument for military service. Outcome: lifetime earnings. [This is the Angrist (1990) study. Assess the exclusion restriction rather than presupposing it: a low lottery number may have changed schooling or occupational choices made to avoid the draft, which affect earnings outside military service (Angrist and Krueger, 1992).]
6. IV versus back-door adjustment. A researcher studies the effect of job training (\(T\)) on earnings (\(Y\)). Two strategies are available: (A) a rich set of pre-treatment covariates \(X\) (education, age, prior earnings, region) and a propensity-score estimator; (B) a lottery that randomly selected units to be offered training (not required to attend), used as an instrument \(Z\).
- Under what assumption does strategy (A) identify the ATE? What specific unobserved variable would most plausibly violate this assumption?
- Strategy (B) identifies a LATE. Describe the complier population in words. Is the LATE likely to be larger or smaller than the ATE in this setting? Explain.
- Both strategies are implemented and yield estimates of $1,800 and $2,400 per year, respectively. Describe a Hausman-type test that uses both estimates. Under what null hypothesis does the test have an approximate \(\chi^2\) distribution, and what must be assumed about the two estimands for the comparison to be meaningful?
- If the two estimates differ significantly, which strategy would you trust more and why? What additional evidence would help distinguish the two explanations (endogeneity bias in (A) versus LATE \(\neq\) ATE in (B))?
7. Nonparametric nonidentification of the ATE under valid IV assumptions (advanced / second pass). Consider the IV DAG: \(Z \to T\), \(T \to Y\), \(U \to T\), \(U \to Y\), with \(U\) unobserved, \(Z \indep U\), and no direct \(Z \to Y\) edge, so that relevance, exogeneity, and exclusion all hold. This problem shows constructively that these assumptions do not nonparametrically identify the ATE, even with a genuinely relevant instrument.
- Construct two SEMs \(\mathcal{M}_1\) and \(\mathcal{M}_2\), each compatible with the IV graph, that are observationally indistinguishable but causally distinct: \[P_{\mathcal{M}_1}(Z, T, Y) = P_{\mathcal{M}_2}(Z, T, Y), \qquad P_{\mathcal{M}_1}\!\left(Y{=}1 \mid \doop(T{=}1)\right) \ne P_{\mathcal{M}_2}\!\left(Y{=}1 \mid \doop(T{=}1)\right).\] (Hint: let \(Z \sim \mathrm{Bern}(1/2)\) independently of a latent type \(U \in \{\mathrm{C}, \mathrm{A}, \mathrm{N}\}\) (\(\mathrm{C}\) = complier, \(\mathrm{A}\) = always-taker, \(\mathrm{N}\) = never-taker) with \(P(\mathrm{C}) = 1/2\) and \(P(\mathrm{A}) = P(\mathrm{N}) = 1/4\), and in both models set \[T = \begin{cases} Z, & U = \mathrm{C},\\ 1, & U = \mathrm{A},\\ 0, & U = \mathrm{N}, \end{cases}\] so that \(P(T{=}1 \mid Z{=}1) - P(T{=}1 \mid Z{=}0) = 1/2\): the instrument is relevant. In both models set \(Y = T\) for \(U = \mathrm{C}\) and \(Y = 1\) for \(U = \mathrm{A}\); let the models differ only for \(U = \mathrm{N}\), with \(Y = 0\) in \(\mathcal{M}_1\) and \(Y = T\) in \(\mathcal{M}_2\).)
- Verify that both models generate the same joint \(P(Z, T, Y)\), then compute \(P(Y{=}1 \mid \doop(T{=}1))\) and \(P(Y{=}1 \mid \doop(T{=}0))\) in each model and show that the two ATEs differ.
- Verify that both models satisfy monotonicity (there are no defiers), compute the LATE \(\E[Y(1) - Y(0) \mid U = \mathrm{C}]\) in each model, and confirm that it coincides across the two models and equals the Wald ratio computed from the common observed distribution. What does this comparison show about which causal quantity the instrument identifies without further assumptions?