IV — Estimation

This is a statement about population moments. To estimate \(\beta_1\) from data, we replace population moments with sample analogs.

This lecture: develop the asymptotic theory for the just-identified case (the Angrist setting), then extend to 2SLS to handle controls and (later) multiple instruments.

This is the just-identified IV estimator: one instrument, one endogenous regressor, no controls.

For binary \(Z\) (e.g., the draft lottery), this simplifies to the Wald estimator:

\[ \hat\beta_1^{IV} = \frac{\bar Y_{Z=1} - \bar Y_{Z=0}}{\bar X_{Z=1} - \bar X_{Z=0}} \]

Does this estimator work? Check consistency next.

Numerator: \(n^{-1}\sum(Z_i - \bar{Z})U_i \xrightarrow{p} \text{Cov}(Z, U) = 0\) by LLN + exogeneity.

Denominator: \(n^{-1}\sum(Z_i - \bar{Z})X_i \xrightarrow{p} \text{Cov}(Z, X) \neq 0\) by LLN + relevance.

By the continuous mapping theorem:

\[ \hat\beta_1^{IV} \xrightarrow{p} \beta_1 + \frac{0}{\text{Cov}(Z, X)} = \beta_1 \]

Regularity: i.i.d. sampling, finite second moments, \(\text{Cov}(Z, X) \neq 0\).

Derivation sketch: Rewrite

\[ \sqrt{n}(\hat\beta_1^{IV} - \beta_1) = \frac{n^{-1/2}\sum(Z_i - \bar{Z})U_i}{n^{-1}\sum(Z_i - \bar{Z})X_i} \]

By CLT (numerator) + Slutsky (denominator):

\[ V_{IV} = \frac{E[(Z_i - E[Z])^2 U_i^2]}{[\text{Cov}(Z,X)]^2} \]

Note: IV is not unbiased in finite samples — the ratio of two random variables has no closed-form mean. Inference relies on asymptotics.

• \(Z\) is the instrument, not the treatment: non-compliance (deferments, voluntary enlistment) means \(Z \neq D\). That’s why we need IV — to leverage random \(Z\) to identify the effect of endogenous \(D\).

Most empirical questions don’t have a randomized \(Z\). Researchers must construct identification from observational data — finding instruments that are plausibly exogenous, defending the assumption from theory and institutions.

We turn to one such case next: Card (1995).

The data: Card uses the National Longitudinal Survey of Young Men (NLSYM), a panel of US men aged 14–24 in 1966. Headline regressions use the 1976 cross-section, when respondents were 24–34.

• Outcome \(\ln W_i\): log hourly wage in 1976
• Regressor \(E_i\): years of completed schooling

Schooling is endogenous — people choose how much education to get, so we can’t naively compare wages across schooling levels.

But \(U_i\) still contains unobservables that drive both schooling and wages:

• Cognitive ability
• Motivation, persistence
• Family environment beyond parental education

So \(\text{Cov}(E_i, U_i \mid \mathbf{W}_i) \neq 0\) — OLS remains biased even after controlling for \(\mathbf{W}\).

But the bare Wald ratio (just-identified, no controls) doesn’t accommodate \(\mathbf{W}\) in the equation.

We need an estimator that uses \(Z\) to identify the schooling coefficient while including \(\mathbf{W}\) as controls.

Stage 1 (First Stage): regress \(E\) on \((Z, \mathbf{W})\): \[ E_i = \pi_0 + \pi_1 Z_i + \boldsymbol{\delta}'\mathbf{W}_i + V_i \] Take fitted values \(\hat E_i\) — a linear combination of exogenous variables, uncorrelated with \(U\).

Stage 2 (Second Stage): regress \(\ln W\) on \((\hat E, \mathbf{W})\): \[ \ln W_i = \beta_0 + \beta_1 \hat E_i + \boldsymbol{\gamma}'\mathbf{W}_i + \text{error}_i \] The coefficient on \(\hat E\) is the 2SLS estimator \(\hat\beta_1^{2SLS}\).

Stage 2 regresses \(\ln W\) on \(\hat E\) — using only the clean variation. The endogenous variation in \(V\) is discarded.

Asymptotic theory carries over: the same LLN + CLT + Slutsky logic from the just-identified case extends to 2SLS — \(\hat\beta_1^{2SLS} \xrightarrow{p} \beta_1\) and is asymptotically normal under analogous conditions.

First stage: regress \(E\) on \(Z + \mathbf{W}\):

\[ E_i = \pi_0 + \pi_1 Z_i + \boldsymbol{\delta}'\mathbf{W}_i + V_i \]

Card finds \(\hat\pi_1 \approx 0.32\) — proximity raises schooling by 0.32 years.

Second stage: regress \(\ln W\) on \(\hat E + \mathbf{W}\):

\[ \ln W_i = \beta_0 + \beta_1 \hat E_i + \boldsymbol{\gamma}'\mathbf{W}_i + e_i \]

Result: \(\hat\beta_1^{2SLS} = 0.132\) (SE 0.049), vs. OLS 0.073 (SE 0.004).

OVB would predict the opposite. Ability is omitted; ability raises both schooling and wages \(\Rightarrow\) OLS overstates the return \(\Rightarrow\) \(\hat\beta^{OLS} > \hat\beta^{IV}\).

But \(\hat\beta^{OLS} < \hat\beta^{IV}\) — and the same pattern shows up across education-IV studies. What’s going on?

By FWL, the OLS slope on \(E_{\text{obs}}\) equals the slope of \(\tilde Y\) on \(\tilde E_{\text{obs}}\) (residuals after partialling out \(\mathbf{W}\)). Since \(\varepsilon \perp \mathbf{W}\): \[ \tilde E_{\text{obs}} = \tilde E^* + \varepsilon. \]

Apply 5a’s bivariate attenuation result to the residualized variables: \[ \hat\beta^{OLS} \xrightarrow{p} \beta \cdot \underbrace{\frac{\text{Var}(\tilde E^*)}{\text{Var}(\tilde E^*) + \text{Var}(\varepsilon)}}_{\text{attenuation factor}\,<\,1}. \]

Substitute \(E_{\text{obs}} = E^* + \varepsilon\). Since \(\varepsilon \perp\!\!\!\perp (Z, \mathbf{W})\), \(E[Z\varepsilon] = 0\) and \(E[\mathbf{W}\varepsilon] = \mathbf{0}\) — they cancel: \[ E\!\bigl[\,Z\,(E^* - \pi_0 - \pi_1 Z - \boldsymbol{\delta}'\mathbf{W})\,\bigr] = 0,\quad E\!\bigl[\,\mathbf{W}\,(\cdot)\,\bigr] = \mathbf{0}. \]

These are the moment conditions defining the linear projection of \(E^*\) on \((Z, \mathbf{W})\). So \((\pi_1, \boldsymbol{\delta})\) are identical to the no-ME projection coefficients.

Stage 2 receives the same predictor it would have under \(E^*\). By the consistency argument earlier in the lecture, \[ \hat\beta^{2SLS} \xrightarrow{p} \beta, \] identical to the no-ME case.

Both land at noise share ≈ 10–15% for US years-of-schooling.

Caveat: the with-controls attenuation factor uses \(\text{Var}(\tilde E^*) < \text{Var}(E^*)\). (Why?)

\(\Rightarrow\) With-controls attenuation is more severe than the unconditional noise share suggests.

Even pessimistically — say attenuation factor \(\approx 0.80\) — the implied no-ME OLS would be \(\approx 0.073/0.80 \approx 0.091\), still well short of the IV’s \(0.132\). ME contributes; it doesn’t close the gap.

Card’s compliers: kids whose schooling was swayed by college proximity. By definition, they’re at the cost margin — return \(\approx\) cost.

• Plausibly liquidity-constrained: cost is what kept them out, not low returns.
• Compliers sit in the high-return tail of the population \(\Rightarrow\) complier returns exceed the population mean.

\(\Rightarrow \text{LATE}_{\text{Card}} > \text{ATE}\), and \(\hat\beta^{2SLS} > \hat\beta^{OLS}\) even with no OLS bias at all.

Less variation used \(\Rightarrow\) wider standard errors. The weaker the instrument’s effect on \(E\) given \(\mathbf{W}\), the smaller the slice 2SLS leverages, and the bigger the precision penalty.

Card illustrates this directly:

Proximity shifts \(E\) by only ~0.32 years — small relative to \(E\)’s overall variation (SD ~3 years). 2SLS uses only that slice \(\Rightarrow\) SE 12× OLS.

\(\rho^2_{\tilde Z, \tilde E}\) = squared correlation between \(\tilde Z\) and \(\tilde E\) = partial \(R^2\): the share of \(E\)’s variation (net of \(\mathbf{W}\)) that \(Z\) explains.

The “small slice” intuition, made precise: as \(Z\)’s explanatory power for \(E\) given \(\mathbf{W}\) shrinks, the variance ratio explodes.

OLS is centered at the wrong value but precise; IV is centered at the truth but imprecise. IV trades bias for variance.

• Broader complier coverage: different instruments may shift different complier groups, potentially expanding what 2SLS averages over (caveats in two slides).

Terminology (single endogenous regressor): \(L = 1\) instrument = just-identified; \(L > 1\) = overidentified.

Stage 2: regress \(\ln W\) on \((\hat E, \mathbf{W})\) — identical to the just-identified case: \[ \ln W_i = \beta_0 + \beta_1 \hat E_i + \boldsymbol{\gamma}'\mathbf{W}_i + \text{error}_i. \]

With heterogeneous effects, this is a weighted average of pairwise LATEs across the levels \(p_0 < p_1 < \cdots < p_K\) of \(p(Z)\): \[ \beta_1^{2SLS} = \sum_{k=0}^{K-1} w_k \cdot \text{LATE}(p_k, p_{k+1}). \]

The weights factor as: \[ w_k \;\propto\; \underbrace{\lambda_k}_{\text{instrument-shape factor}} \;\cdot\; \underbrace{[p_{k+1} - p_k]}_{\text{complier mass at margin }k}. \]

\(p_{k+1} - p_k\) is the rise in \(P(D=1 \mid Z)\) between adjacent levels — under monotonicity, the share of compliers who switch into treatment at margin \(k\).

A property of the instrument-treatment relationship. Tells you how much \(D\) moves at each margin.

A product of two factors moving in opposite directions:

• \(P(Z > z_k)\) shrinks as the cut rises.
• \(E[Z\mid Z > z_k] - E[Z]\) grows as the cut rises.

At extreme cuts one factor vanishes. The product peaks at \(z_k = E[Z]\).

No causal content: \(\lambda_k\) depends only on \(Z\)’s distribution. Trim the sample and the weights shift, even though no causal mechanism has changed.

• Compliers, not the population: only people whose \(D\) moves across some margin of \(p(Z)\) contribute. Always-takers and never-takers are silent.

• Many complier groups, averaged: each margin \(k\) has its own complier subpopulation. With multiple instruments, \(p(Z)\) has multiple jumps, each indexing a different group. 2SLS pools them.

• In non-uniform proportions: weights depend on \(\lambda_k\) and \([p_{k+1} - p_k]\), not on how representative each complier group is of the population. A small but high-leverage margin can dominate.

\(\Rightarrow\) \(\beta^{2SLS}\) is a specific weighted aggregation of complier-group-specific effects — not a single well-defined “treatment effect” for the population.

• Coverage may be narrow: if \(p(Z)\) takes few effectively distinct values (e.g., all instruments shift the same margin), the weighted average covers a limited range of compliers.

\(\Rightarrow\) More instruments does not automatically move 2SLS toward ATE.

OLS benchmark (with year-of-birth controls): \(\hat\beta^{OLS} = 0.071\) (SE \(0.0003\)).

• Compulsory schooling laws let students drop out at age 16.
• Q1-borns reach the dropout age with fewer completed grades than Q4-borns.
• Detrended schooling gap \(\bar E_{\text{Q4}} - \bar E_{\text{Q1}} \approx 0.124\) years.

\[ \hat\beta^{IV} \;=\; \frac{\bar Y_{Z=1} - \bar Y_{Z=0}}{\bar E_{Z=1} - \bar E_{Z=0}} \;=\; \frac{-0.0111}{-0.109} \;=\; 0.1020 \quad (\text{SE } 0.0239). \]

Same pattern as Card: IV \(>\) OLS (\(0.1020\) vs \(0.0711\)) — the systematic IV-bigger-than-OLS finding across education-IV studies. SE is also two orders of magnitude wider than OLS’s \(0.0003\) — IV’s precision cost.

2. Replace the single \(Q1\) instrument with \(3 \times 10 = 30\) QoB × cohort interactions: \[ Z_{i,(q,y)} \;=\; \mathbf{1}\{\text{quarter}_i = q\} \cdot \mathbf{1}\{\text{cohort}_i = y\}, \] \(q \in \{1, 2, 3\}\), \(y \in \{1930, \ldots, 1939\}\).

Payoff: cohort-specific first-stage signals add variation to \(\hat E\) → tighter SE.

• OLS unchanged by YoB controls (0.0709 → 0.0711): cohort confounding is small.
• IV \(>\) OLS in both Wald and 2SLS — same pattern as Card.
• 2SLS shrinks SE by ~⅓ (0.0239 → 0.0161): precision gain from multiple instruments.
• Point estimate moves toward OLS (0.1020 → 0.0891): cohort interactions reweight the LATE.

• Wald (Q1 vs rest): pools all cohorts into one \(Q1\)-vs-rest comparison → a single LATE on cohort-pooled compliers.
• 2SLS (QoB × cohort): each (quarter, cohort) cell contributes its own complier group → weighted average of cohort-specific LATEs.

Both target the same complier population (dropout-margin kids) but aggregate over them differently.

Who is silent in both?

• Always-takers — kids who go to college regardless of birth quarter.
• Never-takers — kids who drop out at 16 regardless of quarter.

\(\Rightarrow\) Neither \(\hat\beta^{IV}\) corresponds to the ATE.

• Effect on: kids whose schooling is shifted at the dropout margin (compulsory-attendance cutoff at age 16).
• Right parameter for: policies operating at that margin (e.g., raising the dropout age).
• Wrong parameter for: policies targeting other groups (college access, gifted students).

Beyond this lecture: the marginal treatment effect (MTE) framework (Heckman-Vytlacil) targets effects for specific subpopulations directly.

Rank condition: \(\mathrm{rank}(E[\mathbf{Z}_i\mathbf{X}_i']) = k\).

The instruments must shift \(X_1, \ldots, X_k\) in linearly independent ways. If two instruments shift \(X_1\) and \(X_2\) identically (e.g., both proxy for the same factor), we can’t separate \(\beta_1\) from \(\beta_2\).

This implies the order condition \(L \geq k\) — a count check, since a matrix with fewer rows than columns can’t have full column rank.

Computing 2SLS with multiple endogenous regressors: run a separate first-stage for each \(X_j\) (using all \(L\) instruments), then plug all fitted values \(\hat X_1, \ldots, \hat X_k\) into the second stage together.

2. Do we need IV? Is the regressor really endogenous, or would OLS suffice? — Hausman test.

3. Is the instrument strong enough? Weak instruments distort point estimates and inference at once — first-stage \(F\), Staiger-Stock.

Big caveat: none of these validates the design. Exogeneity is ultimately a theoretical claim; the tests catch some failures, not all.

The test: regress the 2SLS residuals \(\hat U_i = Y_i - \mathbf{X}_i'\hat\beta^{2SLS}\) on the instruments \(\mathbf{Z}_i\). Under \(H_0\) (all instruments valid), residuals should be uncorrelated with \(\mathbf{Z}_i\) — so the \(R^2\) from this regression should be near zero.

Statistic: \(J = n \cdot R^2 \;\xrightarrow{d}\; \chi^2_{L - k}\) under \(H_0\).

Falsification, not validation: rejection signals at least one invalid instrument. Non-rejection means the data don’t contradict joint validity — it isn’t proof.

Test statistic:

\[ H = (\hat\beta^{IV} - \hat\beta^{OLS})' (\hat V^{IV} - \hat V^{OLS})^{-1} (\hat\beta^{IV} - \hat\beta^{OLS}) \xrightarrow{d} \chi^2_k \]

where \(k\) is the number of endogenous regressors. Reject \(\Rightarrow\) \(X\) is endogenous, IV is needed.

Caveat: even with a valid, reasonably strong instrument, the test is often underpowered. IV’s SE is intrinsically much larger than OLS’s (the \(1/\rho^2\) penalty), so substantively large OLS–IV gaps can still fail to reject statistically. The test also relies on IV being valid in the first place — if it isn’t, the comparison is meaningless.

But: IV is 80% larger than OLS — a substantively huge gap. The test fails to reject only because IV’s SE is so wide. Hausman is underpowered when IV is imprecise — it can’t detect endogeneity that IV’s precision is too low to resolve.

Don’t lean on Hausman as the primary diagnostic for whether to use IV. It tells you more about IV’s precision than about \(E\)’s endogeneity.

As \(\rho^2_{\tilde Z, \tilde E} \to 0\) (weak instrument):

• \(V_{2SLS} \to \infty\): standard errors explode.
• But the problem is worse than large variance.

As the first stage weakens, \(\hat\beta^{2SLS}\) shifts toward OLS and its distribution becomes non-normal and heavy-tailed. Standard confidence intervals lose their nominal coverage.

Rule of thumb (Staiger & Stock 1997): \(F < 10\) ⇒ weak instrument. The cutoff is calibrated so that finite-sample 2SLS bias is at most ~10% of OLS bias.

Always report \(F\). The single most important diagnostic for IV.

• Anderson–Rubin (AR) confidence set: a CI whose coverage is correct regardless of first-stage strength (relevance still required). Approaches the standard 2SLS CI under a strong first stage; widens (and can become unbounded) when the first stage is weak.
• Lee–McCrary–Moreira–Porter (2022) \(tF\) correction: keep the usual \(\hat\beta_1/\text{SE}\) statistic, but compare it to a critical value \(c(F)\) that depends on the first-stage \(F\), instead of \(1.96\). \(c(F) \approx 1.96\) when the first stage is strong; \(c(F)\) is larger (CI wider) when it is weak.

Practical recommendation: when \(F\) is borderline, report AR (or \(tF\)) intervals alongside standard 2SLS CIs. If they agree, inference is robust; if they diverge, the AR/\(tF\) interval is the trustworthy one.

If overidentified (\(L > k\)):

4. Sargan/Hansen \(J\)-test for overidentification.
5. Just-identified estimates for each instrument separately, to check stability.

Defend exogeneity from theory — the most important step. Tests are partial diagnostics; the data alone cannot validate identification.

The Stage-2 OLS routine builds residuals using \(\hat E_i\): \[ \hat e_i = Y_i - \hat\beta_0 - \hat\beta^{2SLS}\,\hat E_i - \hat{\boldsymbol{\gamma}}'\mathbf{W}_i. \] But the correct \(V_{2SLS}\) uses residuals with the actual endogenous regressor: \[ \hat U_i = Y_i - \hat\beta_0 - \hat\beta^{2SLS}\, E_i - \hat{\boldsymbol{\gamma}}'\mathbf{W}_i. \]

Use the built-in IV command — it computes the correct \(V_{2SLS}\) internally:

• Stata: ivregress 2sls Y W (X = Z), robust
• R: ivreg(Y ~ X + W | Z + W, data = ...)
• Python: IV2SLS(Y, [W, const], X, Z).fit()