Appendix — Solutions — Problem Set 3.5 (Anderson–Rubin Inference and the Instrument-Validity Critique)

Full worked solutions to book/weeks/week-03/ps3.5.md, covering Chapter 3.5. Notation follows the Conventions: instrument z, endogenous regressor x, outcome y; the just-identified IV estimator is the ratio \hat\beta_{\text{IV}} = \widehat{\operatorname{Cov}}(z,y)/\widehat{\operatorname{Cov}}(z,x); the Anderson–Rubin (1949) test of H_0:\beta=\beta_0 regresses the adjusted outcome y-\beta_0 x on z (plus controls) and tests the coefficient on z. The recurring theme of the key, the IV parallel to Chapter 2.5’s bias-versus-precision lesson: a 2SLS standard error cannot tell you whether its own instrument is strong enough to trust. The diagnostics — first-stage F, Olea–Pflueger effective F, the Anderson–Rubin interval, the overidentification test — live outside the point estimate, in the research design. A tight SE on a weak instrument is a confident lie.

Problem 1 — Read an IV paper like a referee (20 pts)

(a) [4 pts] The triple: - Instrument z = the assigned examiner’s historical grant rate (examiner leniency), measured on the examiner’s other applications so it is not mechanically tied to this firm’s outcome. - Endogenous regressor x = whether the firm’s application is granted (a 0/1 grant indicator). - Outcome y = the firm’s market value in the three years after the decision.

There is one instrument for one endogenous regressor, so the design is just-identified. The number of over-identifying restrictions is L-1 = 1-1 = 0, so no overidentification (Sargan/Hansen-J) test is available — there is no surplus instrument to disagree with, nothing to check. Exclusion here must be defended entirely by argument (part c), not by a test.

(b) [4 pts] With a first-stage F of 42, weak-instrument bias is not a live concern. 42 is far above both the Staiger–Stock benchmark of 10 and the Stock–Yogo / Olea–Pflueger critical values. By the 1/(F+1) heuristic, 2SLS retains roughly 1/(42+1)\approx 0.023 — about 2.3\% — of OLS’s bias, i.e. it has shed essentially all of it. (Caveat for the careful referee: this F should ideally be the heteroskedasticity-robust effective F per Section 3.5.7, not a non-robust first-stage F; if the authors report only the latter, ask for the former. But at a value of 42 the design is comfortably strong on relevance.) Relevance is the one question the data can answer cleanly, and this paper answers it well — so the referee’s attention must move entirely to exclusion (part c).

(c) [6 pts] Exclusion requires that examiner leniency move firm value only through the grant decision. The back door is any channel by which the assigned examiner touches firm value without going through whether the patent is granted. Two distinct channels (any two of these earn full credit):

Timing / pendency. Lenient examiners may also be faster (or slower), so the assigned examiner shifts how long the application is pending, not just whether it is granted. A faster decision lets the firm commercialize or raise capital sooner, affecting market value through a timing channel independent of the grant. Defense: control for examiner pendency / decision lag, or show leniency is uncorrelated with speed.
Scope of the granted claims. Examiners differ not only in whether they grant but in how broad a set of claims they allow. A lenient examiner might grant narrower claims; claim breadth affects the patent’s commercial value directly. So leniency could affect y through claim scope conditional on grant. Defense: control for granted claim count/breadth, or restrict to the binary grant margin and argue scope is orthogonal to leniency.
Non-random assignment within art unit. If higher-quality applications are routed to particular examiners (e.g., specialists), assignment is not as-good-as-random and leniency proxies application quality, which drives firm value directly. Defense: demonstrate balance of observable application characteristics across examiners within art-unit × year cells (a randomization-check table).

The common structure: each is a path from the assigned examiner to firm value that bypasses the grant indicator, which is exactly an exclusion violation. A good paper anticipates and closes these; a bad one pretends they do not exist.

(d) [4 pts] The instrument moves the grant outcome only for marginal applications — those whose quality is near the grant threshold, so that a lenient examiner grants them but a strict examiner would reject them. Those are the compliers: borderline applications whose fate is decided by the luck of which examiner they drew. The always-takers are clearly patentable applications granted by every examiner regardless of leniency; the never-takers are clearly unpatentable applications rejected by everyone. IV estimates the LATE: the effect on firm value of a granted patent for marginal, near-threshold applications. So the 8.1\% answers the narrow question “what does a granted patent do to value for firms whose patentability was borderline” — not the universal effect of patenting on value. The title “Does Patenting Raise Firm Value?” therefore overclaims: it advertises a population-wide effect while the design identifies only the complier (marginal-application) effect, the precise overreach the chapter’s question 4 warns about.

(e) [2 pts] “It’s standard in the literature” is an appeal to precedent, not an argument about this setting’s back doors. Exclusion is fundamentally untestable in the just-identified case (part a) and must be defended by reasoning through the specific channels — timing, scope, assignment — that could carry the instrument to the outcome around the treatment. That other papers used examiner leniency tells you nothing about whether those channels are closed in this data; a design that is standard can still be wrong, and “standard” is exactly the kind of misdirection question 3 of the checklist is built to see through. Exclusion is an argument, not a citation and not a statistic.

Problem 2 — Why Anderson–Rubin stays valid, and how to read its shapes (18 pts)

(a) [5 pts] (i) The 2SLS estimator is a ratio whose denominator is the first stage, \hat\beta_{\text{IV}} = \widehat{\operatorname{Cov}}(z,y)/\widehat{\operatorname{Cov}}(z,x). When the instrument is weak, the denominator \widehat{\operatorname{Cov}}(z,x) hugs zero and is itself estimated with error. Dividing by a near-zero, noisy quantity makes the sampling distribution of the ratio fat-tailed and skewed — nothing like the normal the conventional standard-error formula assumes. That formula linearizes around the denominator and badly underestimates the true spread, so the reported SE is too small and the interval too narrow. (ii) The Anderson–Rubin test is immunized because no first stage appears anywhere. Instead of estimating \beta and dividing, AR tests each candidate value \beta_0 directly in a plain reduced-form regression of the constructed variable y-\beta_0 x on z. There is no ratio and no denominator near zero, so the F-test keeps its promised size — a 5% test rejects a true null exactly 5% of the time — regardless of first-stage strength. AR moves the inference off the dangerous division entirely.

(b) [4 pts] The recipe for testing H_0:\beta=\beta_0: 1. Construct the adjusted outcome \text{adj} = y - \beta_0 x — the outcome with the hypothesized treatment effect subtracted out. 2. Regress \text{adj} on the instrument z (and any controls). 3. Test the coefficient on z for zero with an ordinary F-test. Under H_0, if exclusion holds, z touched y only through x; subtracting \beta_0 x removes exactly x’s effect, leaving a quantity z has no relationship with — so the coefficient on z must be zero. A significant coefficient means \beta_0 is the wrong effect (we have not fully removed x’s influence) and we reject. Inversion turns this into a confidence interval: sweep \beta_0 over a grid, run the AR F-test at each, and collect every \beta_0 the test fails to reject at the 5% level. That set is the 95% AR confidence interval; by construction it contains the true \beta in 95% of samples, weak instrument or not.

(c) [5 pts] (i) An unbounded AR interval is the honest face of a weak instrument. It says: given how little this instrument moves the treatment, the test has no power — for almost any \beta_0, the adjusted outcome y-\beta_0 x shows no significant relationship with z (because z is barely related to anything), so almost nothing gets rejected and the interval balloons to the whole real line. The design has failed to identify the parameter: the data are consistent with essentially any effect size, including enormous ones. (ii) The coauthor’s plan is not sound. The 2SLS point estimate is the ratio that divides by the very weak first stage the AR interval just exposed; reporting it “as a best guess” is reporting an artifact of dividing by near-zero. On the same data the conventional 2SLS interval would have come back tight and specific — and would have been lying, since its normal approximation is invalid at this first-stage strength. The unbounded AR interval is what the conventional interval should have looked like; the correct conclusion is “this instrument cannot answer the question,” not a number.

(d) [4 pts] (i) An empty AR interval can only arise under over-identification (more instruments than regressors) because emptiness means the instruments disagree about \beta: no single value of \beta_0 can simultaneously make all instruments uncorrelated with the adjusted outcome. With a single instrument (just-identified) there is always some \beta_0 that drives the one coefficient to zero, so the interval can never be empty — there is nothing for instruments to disagree about. (ii) An empty interval diagnoses a failure of the exclusion restriction or model specification: at least one instrument is invalid, or the model is misspecified, so the instruments cannot all be telling the truth. It does not mean “the effect is zero” — zero is just one more \beta_0 that gets rejected along with every other value. This is the same disagreement principle that drives the overidentification test of Problem 4: the empty AR interval is AR detecting, through its own machinery, exactly what a rejected Sargan/ Hansen-J test detects — that the surplus instruments point in incompatible directions.

Problem 3 — The Bound–Jaeger–Baker lesson and the 1/(F+1) heuristic (16 pts)

(a) [5 pts] By the 1/(F+1) heuristic at F=3.8: \frac{1}{F+1} = \frac{1}{3.8+1} = \frac{1}{4.8} \approx 0.208, so 2SLS carries roughly 21\% of OLS’s bias. This is not a coincidence: with a weak first stage, 2SLS is expected to sit a fair way toward OLS rather than at the truth. We can see the prediction line up with the numbers: OLS is 0.55, 2SLS is 0.42, so 2SLS has moved only a fraction of the way down from OLS — consistent with retaining about a fifth of the bias. Since OLS is biased upward and the residual 2SLS bias points toward OLS (Section 3.5.2), the 0.42 is still biased upward relative to the unknown truth — the true effect is plausibly below 0.42, not above it. The very bias the authors fled with IV has been handed back to them in diluted form.

(b) [4 pts] No. The conventional 2SLS SE relies on the normal/asymptotic approximation to the sampling distribution of the ratio estimator, which assumes the first-stage denominator is comfortably away from zero. At F=3.8 that approximation fails: the true sampling distribution is fat-tailed and skewed, and the linearized formula underestimates its spread — so the reported SE of 0.11 is too narrow, the interval too tight, and the three stars overstate the precision. The danger is precisely that the SE looks reassuring while being invalid; the small SE is not evidence of a reliable estimate, it is a symptom of the pathology.

(c) [4 pts] The Bound–Jaeger–Baker (1995) lesson: statistical significance of the first stage is not the same as strength. In their re-examination of Angrist–Krueger’s quarter-of-birth instrument for schooling, the first stage was significant — but only because the sample ran to hundreds of thousands; the instrument explained a minuscule fraction of the variation in schooling, leaving the design weak in the sense that matters. Their devastating demonstration: they replaced the real quarter-of-birth instrument with a randomly generated one — pure noise, correlated with nothing — and 2SLS still produced a “significant,” plausible-looking schooling coefficient with a respectable standard error. A random number posing as an instrument manufactured a causal estimate. This proves that a small, significant-looking 2SLS standard error is no reassurance at all when the first stage is weak: the machinery will conjure a confident answer out of essentially nothing, and the conventional SE will not warn you. You must check the first-stage F against weak-instrument critical values, not against a t-stat of 2.

(d) [3 pts] Demand the Anderson–Rubin 95% confidence interval (weak-instrument-robust inference). If the instrument is in fact too weak to identify the effect, the AR interval would come back very wide, plausibly unbounded — stretching to \pm\infty or a finite segment plus two infinite rays — honestly declaring that the data cannot pin down \beta. That shape would reveal the tight conventional interval around 0.42 as an artifact of dividing by a feeble first stage, and the right conclusion would become “this instrument cannot answer the question,” not “0.42.” (Reporting the Olea–Pflueger effective F alongside it would corroborate the diagnosis.)

Problem 4 — The overidentification test: what a passed J really certifies (14 pts)

(a) [4 pts] The Sargan (1958) / Hansen-J (1982) test regresses the instruments against the IV residuals \hat u = y - x\hat\beta_{\text{IV}} and measures their total correlation. A valid instrument is uncorrelated with the structural error by exclusion, so under the null hypothesis that all instruments are valid, each should show no relationship with \hat u, and the J statistic follows a chi-squared distribution. A large J (small p-value) rejects the joint null: at least one instrument is correlated with the error — at least one violates exclusion. The degrees of freedom equal the number of over-identifying restrictions, L - 1 where L is the number of instruments for one regressor. Here L=2, so \text{df} = 2 - 1 = 1: two instruments give one surplus restriction — one independent way for the instruments to disagree, hence one degree of freedom.

(b) [4 pts] Two distinct errors: 1. What the test detects. The J test detects disagreement among the instruments, not validity. A passed J is the absence of evidence of disagreement, not evidence of exclusion — it says the two instruments point to compatible values of \beta, nothing more. “Confirms exclusion” reads absence of a flag as a certificate, which it is not. 2. The all-invalid-together scenario. The test can only catch relative disagreement. If both instruments are invalid in the same direction — sharing the same back door — they will agree perfectly, the residual will look uncorrelated with both, and J will pass. So a clean J is fully consistent with both instruments being invalid; it cannot rule that out (part c).

(c) [3 pts] If both instruments are correlated with the same omitted regional economic-vitality factor that also lowers cost of capital, then both are biased the same way, so each implies the same (wrong) \beta. The J test only measures whether the instruments disagree; since they agree (both shifted by the identical back door), the test finds no disagreement and passes. This proves that a clean J does not certify exclusion — it certifies only that the instruments are not contradicting each other. Common invalidity is invisible to the test, exactly as the chapter warns. Exclusion remains an argument Priya must make about the regional-vitality channel directly, not a box the J statistic can check.

(d) [3 pts] For a just-identified design (one instrument, one regressor) there are L - 1 = 1 - 1 = \mathbf{0} over-identifying restrictions, so the J test is unavailable — there is no surplus instrument, nothing to check, the test is empty (Problem 1a). What the analyst is left with is the same thing Problem 1(e) insisted on: a defended argument about back-door channels — reasoning through every path by which the instrument could reach the outcome around the treatment — because no statistic can substitute for that argument when there are no over-identifying restrictions to test.

Problem 5 — Weak-IV diagnosis: first-stage F, effective F, and what to do (16 pts)

(a) [5 pts] (i) The Olea–Pflueger (2013) effective F corrects for heteroskedasticity (and the many-instrument setting), which the conventional non-robust first-stage F ignores. The conventional F assumes homoskedastic first-stage errors; when errors are heteroskedastic — as Sam’s are — that assumption is wrong and the conventional F can overstate identification strength. The effective F is built to measure identification strength honestly under exactly these conditions. (ii) When the two disagree, the effective F is the one to believe because Sam has heteroskedasticity, which is precisely the situation the conventional F mishandles and the effective F was designed for. So the real diagnosis is the effective F of 5.2 (below its critical value), not the conventional 11.6: identification is weak, and the “above 10, so we’re fine” reasoning rests on the wrong statistic.

(b) [4 pts] With an effective F of 5.2, below its critical value, identification is weak. By the 1/(F+1) intuition, 2SLS retains roughly 1/(5.2+1)\approx 0.16 — about a sixth — of OLS’s bias, so Sam’s 2SLS estimate is pulled toward the OLS estimate (toward the endogeneity he used IV to escape). On inference: his conventional 2SLS interval will be too narrow and possibly centered on the wrong place — falsely confident, because the normal approximation to the ratio fails at this strength — while an Anderson–Rubin interval on the same data will be wide, possibly unbounded, and honest, reflecting how little this instrument actually pins down. The contrast (tight-and-lying vs. wide-and-honest) is the whole lesson of the chapter.

(c) [4 pts] (i) This invites many-instruments bias. Mechanism: 2SLS replaces the endogenous x with its first-stage fitted value \hat x — the projection of x onto the instruments. With many instruments, that projection overfits, letting the first stage chase the idiosyncratic noise in x — and the noise in x is exactly the endogenous part correlated with the structural error. So \hat x starts to recover the very endogeneity IV was meant to purge; as the instrument count grows toward the sample size, \hat x \to x and 2SLS collapses back toward OLS — the worst case of the toward-OLS bias. The conventional first-stage F of >20 is the trap, not reassurance: a high F bought by stuffing in weak interacted instruments. (ii) The effective F will not be fooled. Olea–Pflueger is built precisely to flag weak identification honestly in heteroskedastic and many-instrument settings; it does not reward you for piling up junk instruments. That is why the chapter calls it the right diagnostic — a high conventional F from many weak instruments is exactly what it is designed to see through.

(d) [3 pts] Sam should find a better instrument, not more of them — a few strong instruments beat many weak ones, always; the fix for low identification strength is stronger relevance from a genuinely exogenous source, not interactions that manufacture a high conventional F. And regardless of first-stage strength he should report the Anderson–Rubin confidence interval, which stays valid whether the instrument is strong or weak, so a reader can judge the result honestly rather than trusting a conventional SE that the pathology has corrupted.

Problem 6 — Design-critique essay: apply the referee checklist to a finance scenario (16 pts)

This is graded against the six required components of the §3.5.9 ledger. A model report follows; full credit requires the substance of each bracketed component, in order, in roughly 250–400 words.

Model referee report.

Relevance [3 pts]. The reported first-stage F of 7.5 is below the Staiger–Stock benchmark of 10 and below standard weak-instrument critical values — a single-digit F is a klaxon. By the 1/(F+1) heuristic the 2SLS estimate still carries about 1/(7.5+1)\approx 0.12, roughly 12\%, of OLS’s bias, pulling it toward the endogenous OLS estimate it was meant to escape. Worse, default data are almost certainly heteroskedastic, so the relevant statistic is the Olea–Pflueger (2013) effective F, which the author does not report; given heteroskedasticity the effective F is likely lower still than 7.5. I would require it before believing the design is identified.

Exclusion [4 pts]. Officer assignment must affect default only through approval. But loan officers do far more than approve: they set loan terms (interest rate, loan amount, collateral requirements), which directly affect a borrower’s ability to repay regardless of the binary approval; they may monitor or coach borrowers differently, affecting default through effort rather than access; and assignment may not be random if certain applicant types are routed to certain officers, so officer strictness proxies borrower quality and reaches default directly. Each is a back door from officer to default that bypasses the approval indicator. “Loan-officer assignment is plausibly exogenous” is an assertion, not an argument — it names no channel and closes none; in a just-identified design exclusion is untestable and must be defended by reasoning through exactly these paths.

Compliers / LATE [3 pts]. The instrument moves approval only for marginal applicants near the approval threshold — those a lenient officer approves but a strict one rejects. These are the compliers. Always-takers are clearly creditworthy applicants approved by every officer; never-takers are clearly unqualified applicants rejected by all. The 6-point estimate is therefore the LATE for marginal borrowers, not the universal effect of “access to credit”; the abstract’s broad framing overreaches the complier-specific estimate.

Identification count [2 pts]. One instrument (officer approval rate), one endogenous regressor (approval): just-identified. Hence L-1=0 over-identifying restrictions and no Sargan/Hansen-J test is available — there is no internal check on exclusion, which makes the argument in the Exclusion paragraph the load-bearing defense.

Honest inference [2 pts]. The author reports no Anderson–Rubin interval. Given the low first-stage F, an honest AR interval could plausibly be very wide or unbounded, in which case the headline 6-point result is an artifact of dividing by a weak first stage and the real answer is “the data cannot say.” I would require the AR interval before trusting the SE of 2.9 points.

Verdict and connection to Maya’s question [2 pts]. Revise-and-resubmit at best, leaning toward reject-as-uninformative: the design fails the relevance bar, mounts no real exclusion argument, has no J-test option, and omits weak-IV-robust inference, so the confident 6-point result is not yet credible. For Maya’s own fair-lending work the lesson is exact: a credible causal number where unobserved borrower quality confounds everything is earned by the design, not by a tight standard error — relevance must clear the weak-IV bar, exclusion must be argued channel by channel, and inference must be reported in a form (Anderson– Rubin) that does not collapse when the instrument is weak. This is the IV analog of the Chapter 2.5 lesson: the diagnostics that decide credibility live outside the point estimate.

A full-credit report hits all six components in order, argues exclusion with concrete channels (not generic worry), correctly identifies the complier population and the just-identified status, flags the missing AR interval, and renders a reasoned verdict — inventing no numbers beyond those given.

End of solutions for Problem Set 3.5. The through-line of Week 3: each causal strategy trades one heroic, largely untestable assumption for another — conditional independence for matching, exclusion for IV — and the art is knowing which your setting can support. The diagnostics this set drilled (first-stage and effective F, the Anderson–Rubin interval, the overidentification test) are the tools that keep IV honest, all living outside* the 2SLS point estimate. Week 4 changes the game with design-based methods that exploit structure in the data itself — difference-in-differences differences away fixed confounders through panels, regression discontinuity manufactures a local experiment at an arbitrary cutoff, synthetic control builds a bespoke counterfactual — needing fewer leaps of faith. Maya’s fair-lending question and Leah’s patent question return there with designs whose credibility comes from the shape of the natural experiment.*

# Solutions — Problem Set 3.5 (Anderson–Rubin Inference and the Instrument-Validity Critique) Full worked solutions to `book/weeks/week-03/ps3.5.md`, covering Chapter 3.5. Notation follows the Conventions: instrument $z$, endogenous regressor $x$, outcome $y$; the just-identified IV estimator is the ratio $\hat\beta_{\text{IV}} = \widehat{\operatorname{Cov}}(z,y)/\widehat{\operatorname{Cov}}(z,x)$; the Anderson–Rubin (1949) test of $H_0:\beta=\beta_0$ regresses the adjusted outcome $y-\beta_0 x$ on $z$ (plus controls) and tests the coefficient on $z$. The recurring theme of the key, the IV parallel to Chapter 2.5's bias-versus-precision lesson: **a 2SLS standard error cannot tell you whether its own instrument is strong enough to trust. The diagnostics — first-stage $F$, Olea–Pflueger effective $F$, the Anderson–Rubin interval, the overidentification test — live *outside* the point estimate, in the research design. A tight SE on a weak instrument is a confident lie.** --- ## Problem 1 — Read an IV paper like a referee (20 pts) **(a)** [4 pts] The triple: - Instrument $z$ = **the assigned examiner's historical grant rate** (examiner leniency), measured on the examiner's *other* applications so it is not mechanically tied to this firm's outcome. - Endogenous regressor $x$ = **whether the firm's application is granted** (a 0/1 grant indicator). - Outcome $y$ = **the firm's market value** in the three years after the decision. There is one instrument for one endogenous regressor, so the design is **just-identified**. The number of over-identifying restrictions is $L-1 = 1-1 = 0$, so **no overidentification (Sargan/Hansen-$J$) test is available** — there is no surplus instrument to disagree with, nothing to check. Exclusion here must be defended entirely by argument (part c), not by a test. **(b)** [4 pts] With a first-stage $F$ of $42$, **weak-instrument bias is not a live concern.** $42$ is far above both the Staiger–Stock benchmark of $10$ and the Stock–Yogo / Olea–Pflueger critical values. By the $1/(F+1)$ heuristic, 2SLS retains roughly $1/(42+1)\approx 0.023$ — about $2.3\%$ — of OLS's bias, i.e. it has shed essentially all of it. (Caveat for the careful referee: this $F$ should ideally be the *heteroskedasticity-robust effective $F$* per Section 3.5.7, not a non-robust first-stage $F$; if the authors report only the latter, ask for the former. But at a value of $42$ the design is comfortably strong on relevance.) Relevance is the *one* question the data can answer cleanly, and this paper answers it well — so the referee's attention must move entirely to exclusion (part c). **(c)** [6 pts] Exclusion requires that examiner leniency move firm value *only* through the grant decision. The back door is any channel by which the *assigned examiner* touches firm value without going through whether the patent is granted. Two distinct channels (any two of these earn full credit): 1. **Timing / pendency.** Lenient examiners may also be *faster* (or slower), so the assigned examiner shifts how long the application is pending, not just whether it is granted. A faster decision lets the firm commercialize or raise capital sooner, affecting market value through a timing channel independent of the grant. *Defense:* control for examiner pendency / decision lag, or show leniency is uncorrelated with speed. 2. **Scope of the granted claims.** Examiners differ not only in *whether* they grant but in how broad a set of claims they allow. A lenient examiner might grant *narrower* claims; claim breadth affects the patent's commercial value directly. So leniency could affect $y$ through claim scope conditional on grant. *Defense:* control for granted claim count/breadth, or restrict to the binary grant margin and argue scope is orthogonal to leniency. 3. **Non-random assignment within art unit.** If higher-quality applications are routed to particular examiners (e.g., specialists), assignment is not as-good-as-random and leniency proxies application quality, which drives firm value directly. *Defense:* demonstrate balance of observable application characteristics across examiners within art-unit × year cells (a randomization-check table). The common structure: each is a path from the assigned examiner to firm value that *bypasses* the grant indicator, which is exactly an exclusion violation. A good paper anticipates and closes these; a bad one pretends they do not exist. **(d)** [4 pts] The instrument moves the grant outcome only for **marginal applications** — those whose *quality is near the grant threshold*, so that a lenient examiner grants them but a strict examiner would reject them. Those are the **compliers**: borderline applications whose fate is decided by the luck of which examiner they drew. The **always-takers** are clearly patentable applications granted by every examiner regardless of leniency; the **never-takers** are clearly unpatentable applications rejected by everyone. IV estimates the **LATE**: the effect on firm value of a granted patent *for marginal, near-threshold applications.* So the $8.1\%$ answers the narrow question "what does a granted patent do to value for firms whose patentability was borderline" — **not** the universal effect of patenting on value. The title *"Does Patenting Raise Firm Value?"* therefore **overclaims**: it advertises a population-wide effect while the design identifies only the complier (marginal-application) effect, the precise overreach the chapter's question 4 warns about. **(e)** [2 pts] "It's standard in the literature" is an appeal to precedent, not an argument about *this* setting's back doors. Exclusion is fundamentally **untestable in the just-identified case** (part a) and must be defended by reasoning through the specific channels — timing, scope, assignment — that could carry the instrument to the outcome around the treatment. That other papers used examiner leniency tells you nothing about whether *those* channels are closed in *this* data; a design that is standard can still be wrong, and "standard" is exactly the kind of misdirection question 3 of the checklist is built to see through. Exclusion is an argument, not a citation and not a statistic. --- ## Problem 2 — Why Anderson–Rubin stays valid, and how to read its shapes (18 pts) **(a)** [5 pts] (i) The 2SLS estimator is a **ratio** whose denominator is the first stage, $\hat\beta_{\text{IV}} = \widehat{\operatorname{Cov}}(z,y)/\widehat{\operatorname{Cov}}(z,x)$. When the instrument is weak, the denominator $\widehat{\operatorname{Cov}}(z,x)$ **hugs zero and is itself estimated with error.** Dividing by a near-zero, noisy quantity makes the sampling distribution of the ratio fat-tailed and skewed — nothing like the normal the conventional standard-error formula assumes. That formula linearizes around the denominator and badly *underestimates* the true spread, so the reported SE is too small and the interval too narrow. (ii) The Anderson–Rubin test is immunized because **no first stage appears anywhere.** Instead of estimating $\beta$ and dividing, AR tests each candidate value $\beta_0$ directly in a *plain reduced-form regression* of the constructed variable $y-\beta_0 x$ on $z$. There is no ratio and no denominator near zero, so the $F$-test keeps its promised size — a 5% test rejects a true null exactly 5% of the time — **regardless of first-stage strength.** AR moves the inference off the dangerous division entirely. **(b)** [4 pts] The recipe for testing $H_0:\beta=\beta_0$: 1. **Construct** the adjusted outcome $\text{adj} = y - \beta_0 x$ — the outcome with the *hypothesized* treatment effect subtracted out. 2. **Regress** $\text{adj}$ on the instrument $z$ (and any controls). 3. **Test** the coefficient on $z$ for zero with an ordinary $F$-test. Under $H_0$, if exclusion holds, $z$ touched $y$ *only through* $x$; subtracting $\beta_0 x$ removes exactly $x$'s effect, leaving a quantity $z$ has no relationship with — so the coefficient on $z$ must be **zero**. A significant coefficient means $\beta_0$ is the wrong effect (we have not fully removed $x$'s influence) and we reject. **Inversion** turns this into a confidence interval: sweep $\beta_0$ over a grid, run the AR $F$-test at each, and **collect every $\beta_0$ the test fails to reject** at the 5% level. That set is the 95% AR confidence interval; by construction it contains the true $\beta$ in 95% of samples, weak instrument or not. **(c)** [5 pts] (i) An unbounded AR interval is **the honest face of a weak instrument.** It says: given how little this instrument moves the treatment, the test has no power — for almost any $\beta_0$, the adjusted outcome $y-\beta_0 x$ shows no significant relationship with $z$ (because $z$ is barely related to *anything*), so almost nothing gets rejected and the interval balloons to the whole real line. The design has **failed to identify the parameter**: the data are consistent with essentially any effect size, including enormous ones. (ii) The coauthor's plan is **not sound.** The 2SLS point estimate is the ratio that divides by the very weak first stage the AR interval just exposed; reporting it "as a best guess" is reporting an artifact of dividing by near-zero. On the same data the conventional 2SLS interval would have come back *tight and specific* — and would have been lying, since its normal approximation is invalid at this first-stage strength. The unbounded AR interval is what the conventional interval *should* have looked like; the correct conclusion is "this instrument cannot answer the question," not a number. **(d)** [4 pts] (i) An empty AR interval can **only** arise under over-identification (more instruments than regressors) because emptiness means the instruments *disagree* about $\beta$: no single value of $\beta_0$ can simultaneously make *all* instruments uncorrelated with the adjusted outcome. With a single instrument (just-identified) there is always some $\beta_0$ that drives the one coefficient to zero, so the interval can never be empty — there is nothing for instruments to disagree about. (ii) An empty interval diagnoses a failure of the **exclusion restriction or model specification**: at least one instrument is invalid, or the model is misspecified, so the instruments cannot all be telling the truth. It does **not** mean "the effect is zero" — zero is just one more $\beta_0$ that gets rejected along with every other value. This is the same **disagreement principle** that drives the overidentification test of Problem 4: the empty AR interval is AR detecting, through its own machinery, exactly what a rejected Sargan/ Hansen-$J$ test detects — that the surplus instruments point in incompatible directions. --- ## Problem 3 — The Bound–Jaeger–Baker lesson and the $1/(F+1)$ heuristic (16 pts) **(a)** [5 pts] By the $1/(F+1)$ heuristic at $F=3.8$: $$\frac{1}{F+1} = \frac{1}{3.8+1} = \frac{1}{4.8} \approx 0.208,$$ so 2SLS carries roughly **$21\%$ of OLS's bias.** This is **not a coincidence:** with a weak first stage, 2SLS is *expected* to sit a fair way toward OLS rather than at the truth. We can see the prediction line up with the numbers: OLS is $0.55$, 2SLS is $0.42$, so 2SLS has moved only a fraction of the way *down* from OLS — consistent with retaining about a fifth of the bias. Since OLS is biased *upward* and the residual 2SLS bias points *toward OLS* (Section 3.5.2), the $0.42$ is still biased **upward relative to the unknown truth** — the true effect is plausibly *below* $0.42$, not above it. The very bias the authors fled with IV has been handed back to them in diluted form. **(b)** [4 pts] **No.** The conventional 2SLS SE relies on the **normal/asymptotic approximation to the sampling distribution of the ratio estimator**, which assumes the first-stage denominator is comfortably away from zero. At $F=3.8$ that approximation **fails**: the true sampling distribution is fat-tailed and skewed, and the linearized formula *underestimates* its spread — so the reported SE of $0.11$ is **too narrow**, the interval too tight, and the three stars overstate the precision. The danger is precisely that the SE looks *reassuring* while being invalid; the small SE is not evidence of a reliable estimate, it is a symptom of the pathology. **(c)** [4 pts] The Bound–Jaeger–Baker (1995) lesson: **statistical significance of the first stage is not the same as strength.** In their re-examination of Angrist–Krueger's quarter-of-birth instrument for schooling, the first stage was *significant* — but only because the sample ran to hundreds of thousands; the instrument explained a minuscule fraction of the variation in schooling, leaving the design weak in the sense that matters. Their devastating demonstration: they replaced the real quarter-of-birth instrument with a **randomly generated** one — pure noise, correlated with nothing — and 2SLS *still* produced a "significant," plausible-looking schooling coefficient with a respectable standard error. A random number posing as an instrument **manufactured a causal estimate.** This proves that a small, significant-looking 2SLS standard error is no reassurance at all when the first stage is weak: the machinery will conjure a confident answer out of essentially nothing, and the conventional SE will not warn you. You must check the first-stage $F$ against weak-instrument critical values, not against a $t$-stat of 2. **(d)** [3 pts] Demand the **Anderson–Rubin 95% confidence interval** (weak-instrument-robust inference). If the instrument is in fact too weak to identify the effect, the AR interval would come back **very wide, plausibly unbounded** — stretching to $\pm\infty$ or a finite segment plus two infinite rays — honestly declaring that the data cannot pin down $\beta$. That shape would reveal the tight conventional interval around $0.42$ as an artifact of dividing by a feeble first stage, and the right conclusion would become "this instrument cannot answer the question," not "$0.42$." (Reporting the Olea–Pflueger effective $F$ alongside it would corroborate the diagnosis.) --- ## Problem 4 — The overidentification test: what a passed J really certifies (14 pts) **(a)** [4 pts] The Sargan (1958) / Hansen-$J$ (1982) test regresses the **instruments against the IV residuals** $\hat u = y - x\hat\beta_{\text{IV}}$ and measures their total correlation. A *valid* instrument is uncorrelated with the structural error by exclusion, so under the **null hypothesis that all instruments are valid**, each should show no relationship with $\hat u$, and the $J$ statistic follows a chi-squared distribution. A **large $J$ (small $p$-value) rejects** the joint null: at least one instrument is correlated with the error — at least one violates exclusion. The **degrees of freedom equal the number of over-identifying restrictions**, $L - 1$ where $L$ is the number of instruments for one regressor. Here $L=2$, so $\text{df} = 2 - 1 = 1$: two instruments give one surplus restriction — one independent way for the instruments to disagree, hence one degree of freedom. **(b)** [4 pts] Two distinct errors: 1. **What the test detects.** The $J$ test detects *disagreement* among the instruments, not validity. A passed $J$ is the **absence of evidence of disagreement**, not evidence of exclusion — it says the two instruments point to compatible values of $\beta$, nothing more. "Confirms exclusion" reads absence of a flag as a certificate, which it is not. 2. **The all-invalid-together scenario.** The test can only catch *relative* disagreement. If **both** instruments are invalid *in the same direction* — sharing the same back door — they will agree perfectly, the residual will look uncorrelated with both, and $J$ will pass. So a clean $J$ is fully consistent with *both* instruments being invalid; it cannot rule that out (part c). **(c)** [3 pts] If both instruments are correlated with the same omitted regional economic-vitality factor that also lowers cost of capital, then **both are biased the same way**, so each implies the *same* (wrong) $\beta$. The $J$ test only measures whether the instruments *disagree*; since they agree (both shifted by the identical back door), the test finds no disagreement and **passes**. This proves that **a clean $J$ does not certify exclusion** — it certifies only that the instruments are not *contradicting each other*. Common invalidity is invisible to the test, exactly as the chapter warns. Exclusion remains an argument Priya must make about the regional-vitality channel directly, not a box the $J$ statistic can check. **(d)** [3 pts] For a **just-identified** design (one instrument, one regressor) there are $L - 1 = 1 - 1 = \mathbf{0}$ over-identifying restrictions, so **the $J$ test is unavailable** — there is no surplus instrument, nothing to check, the test is empty (Problem 1a). What the analyst is left with is the same thing Problem 1(e) insisted on: **a defended argument about back-door channels** — reasoning through every path by which the instrument could reach the outcome around the treatment — because no statistic can substitute for that argument when there are no over-identifying restrictions to test. --- ## Problem 5 — Weak-IV diagnosis: first-stage F, effective F, and what to do (16 pts) **(a)** [5 pts] (i) The **Olea–Pflueger (2013) effective $F$** corrects for **heteroskedasticity (and the many-instrument setting)**, which the conventional non-robust first-stage $F$ ignores. The conventional $F$ assumes homoskedastic first-stage errors; when errors are heteroskedastic — as Sam's are — that assumption is wrong and the conventional $F$ can *overstate* identification strength. The effective $F$ is built to measure identification strength honestly under exactly these conditions. (ii) When the two disagree, **the effective $F$ is the one to believe** because Sam *has* heteroskedasticity, which is precisely the situation the conventional $F$ mishandles and the effective $F$ was designed for. So the real diagnosis is the effective $F$ of $5.2$ (below its critical value), not the conventional $11.6$: identification is **weak**, and the "above 10, so we're fine" reasoning rests on the wrong statistic. **(b)** [4 pts] With an effective $F$ of $5.2$, below its critical value, **identification is weak.** By the $1/(F+1)$ intuition, 2SLS retains roughly $1/(5.2+1)\approx 0.16$ — about a sixth — of OLS's bias, so Sam's 2SLS estimate is pulled **toward the OLS estimate** (toward the endogeneity he used IV to escape). On inference: his **conventional 2SLS interval will be too narrow and possibly centered on the wrong place** — falsely confident, because the normal approximation to the ratio fails at this strength — while an **Anderson–Rubin interval on the same data will be wide, possibly unbounded, and honest**, reflecting how little this instrument actually pins down. The contrast (tight-and-lying vs. wide-and-honest) is the whole lesson of the chapter. **(c)** [4 pts] (i) This invites **many-instruments bias.** Mechanism: 2SLS replaces the endogenous $x$ with its first-stage fitted value $\hat x$ — the projection of $x$ onto the instruments. With many instruments, that projection **overfits**, letting the first stage chase the *idiosyncratic noise* in $x$ — and the noise in $x$ is exactly the endogenous part correlated with the structural error. So $\hat x$ starts to recover the very endogeneity IV was meant to purge; as the instrument count grows toward the sample size, $\hat x \to x$ and **2SLS collapses back toward OLS** — the worst case of the toward-OLS bias. The conventional first-stage $F$ of $>20$ is the *trap*, not reassurance: a high $F$ bought by stuffing in weak interacted instruments. (ii) The **effective $F$ will not be fooled.** Olea–Pflueger is built precisely to flag weak identification honestly in heteroskedastic *and many-instrument* settings; it does not reward you for piling up junk instruments. That is why the chapter calls it the right diagnostic — a high conventional $F$ from many weak instruments is exactly what it is designed to see through. **(d)** [3 pts] Sam should **find a *better* instrument, not *more* of them** — a few strong instruments beat many weak ones, always; the fix for low identification strength is stronger relevance from a genuinely exogenous source, not interactions that manufacture a high conventional $F$. And regardless of first-stage strength he should **report the Anderson–Rubin confidence interval**, which stays valid whether the instrument is strong or weak, so a reader can judge the result honestly rather than trusting a conventional SE that the pathology has corrupted. --- ## Problem 6 — Design-critique essay: apply the referee checklist to a finance scenario (16 pts) This is graded against the six required components of the §3.5.9 ledger. A model report follows; full credit requires the substance of each bracketed component, in order, in roughly 250–400 words. **Model referee report.** *Relevance* [3 pts]. The reported first-stage $F$ of $7.5$ is **below the Staiger–Stock benchmark of $10$** and below standard weak-instrument critical values — a single-digit $F$ is a klaxon. By the $1/(F+1)$ heuristic the 2SLS estimate still carries about $1/(7.5+1)\approx 0.12$, roughly $12\%$, of OLS's bias, pulling it *toward* the endogenous OLS estimate it was meant to escape. Worse, default data are almost certainly heteroskedastic, so the relevant statistic is the **Olea–Pflueger (2013) effective $F$**, which the author does not report; given heteroskedasticity the effective $F$ is likely *lower* still than $7.5$. I would require it before believing the design is identified. *Exclusion* [4 pts]. Officer assignment must affect default *only* through approval. But loan officers do far more than approve: they set **loan terms** (interest rate, loan amount, collateral requirements), which directly affect a borrower's ability to repay regardless of the binary approval; they may **monitor or coach** borrowers differently, affecting default through effort rather than access; and **assignment may not be random** if certain applicant types are routed to certain officers, so officer strictness proxies borrower quality and reaches default directly. Each is a back door from officer to default that bypasses the approval indicator. "Loan-officer assignment is plausibly exogenous" is an **assertion, not an argument** — it names no channel and closes none; in a just-identified design exclusion is untestable and must be defended by reasoning through exactly these paths. *Compliers / LATE* [3 pts]. The instrument moves approval only for **marginal applicants near the approval threshold** — those a lenient officer approves but a strict one rejects. These are the **compliers**. **Always-takers** are clearly creditworthy applicants approved by every officer; **never-takers** are clearly unqualified applicants rejected by all. The 6-point estimate is therefore the **LATE for marginal borrowers**, not the universal effect of "access to credit"; the abstract's broad framing **overreaches** the complier-specific estimate. *Identification count* [2 pts]. One instrument (officer approval rate), one endogenous regressor (approval): **just-identified.** Hence $L-1=0$ over-identifying restrictions and **no Sargan/Hansen-$J$ test is available** — there is no internal check on exclusion, which makes the argument in the *Exclusion* paragraph the load-bearing defense. *Honest inference* [2 pts]. The author reports **no Anderson–Rubin interval.** Given the low first-stage $F$, an honest AR interval could plausibly be **very wide or unbounded**, in which case the headline 6-point result is an artifact of dividing by a weak first stage and the real answer is "the data cannot say." I would require the AR interval before trusting the SE of $2.9$ points. *Verdict and connection to Maya's question* [2 pts]. **Revise-and-resubmit at best, leaning toward reject-as-uninformative:** the design fails the relevance bar, mounts no real exclusion argument, has no $J$-test option, and omits weak-IV-robust inference, so the confident 6-point result is not yet credible. For Maya's own fair-lending work the lesson is exact: a credible causal number where unobserved borrower quality confounds everything is *earned by the design*, not by a tight standard error — relevance must clear the weak-IV bar, exclusion must be argued channel by channel, and inference must be reported in a form (Anderson– Rubin) that does not collapse when the instrument is weak. This is the IV analog of the Chapter 2.5 lesson: the diagnostics that decide credibility live *outside* the point estimate. A full-credit report hits all six components in order, argues exclusion with concrete channels (not generic worry), correctly identifies the complier population and the just-identified status, flags the missing AR interval, and renders a reasoned verdict — inventing no numbers beyond those given. --- *End of solutions for Problem Set 3.5. The through-line of Week 3: each causal strategy trades one heroic, largely untestable assumption for another — conditional independence for matching, exclusion for IV — and the art is knowing which your setting can support. The diagnostics this set drilled (first-stage and effective $F$, the Anderson–Rubin interval, the overidentification test) are the tools that keep IV honest, all living *outside* the 2SLS point estimate. Week 4 changes the game with **design-based** methods that exploit structure in the data itself — difference-in-differences differences away fixed confounders through panels, regression discontinuity manufactures a local experiment at an arbitrary cutoff, synthetic control builds a bespoke counterfactual — needing fewer leaps of faith. Maya's fair-lending question and Leah's patent question return there with designs whose credibility comes from the shape of the natural experiment.*