Instrumental variables

An opinionated IV workflow grounded in a read canon (references/canon.md, current as of 2026-08-04): Imbens' Statistical Science perspective for the assumption structure and the LATE estimand, Keane-Neal's Annual Review guide for the weak-instrument inference regime, the two Borusyak-Hull(-Jaravel) papers for shift-share and formula instruments, Mogstad-Santos-Torgovitsky's Econometrica framework for extrapolating beyond the compliers, and Goldsmith-Pinkham-Hull-Kolesár's JEP operator's manual for leniency designs. Deliverable: the recommendation with its citation, the R estimation and diagnostics code, and a methods paragraph.

Refresh path: run litreview on the method since the canon date, then propose additions to references/canon.md as flagged addenda.

Six designs to recognize

Find your design here before reading about estimators. Fuller rows, with what each canonical case teaches, are in references/details.md.

Design	Canonical case	Marketing analogue	What kills it
Randomized encouragement with noncompliance	Oregon Medicaid lottery (Finkelstein et al. 2012)	ghost ads, PSA holdouts, invite-only betas	the offer itself moves the outcome, because the invitation signals
Leniency routing	Philadelphia bail magistrates (Stevenson 2018)	moderation queues, credit underwriting, support-ticket routing	units re-enter the queue after seeing their assignment; monotonicity across case types
Shift-share exposure	Bartik 1991; Autor-Dorn-Hanson 2013	category demand growth from national demographic shifts weighted by sales shares	generic shares, which proxy exposure to any shock
Formula or network exposure	Borusyak-Hull 2023, China high-speed rail	fraction of friends treated in seeding and referral programs	no recentering; connected users are mechanically more exposed
Cost shifter for price	Wright 1928; Graddy's Fulton fish market	input costs, freight, Hausman other-market prices	the instrument-induced elasticity is not the one you face when you set price yourself
Access or distance	the McClellan-Newhouse differential-distance trick	store, warehouse, or delivery-coverage proximity	distance correlates with everything; condition on generic distance

When IV, and the five assumptions kept separate

IV is the tool when unconfoundedness fails because treatment is chosen: agents select on anticipated gains (program participation, adoption, self-selected exposure), or the treatment is an equilibrium object like a price, where OLS mixes supply and demand slopes (the Fulton fish market numbers in references/details.md are the two-line demonstration). An instrument is an incentive or cost shifter: it changes the attractiveness of taking treatment without entering the potential outcomes. A price elasticity estimated this way is the elasticity of the compliers the instrument moved, and need not be the elasticity a firm faces when it sets price itself: "when the firm lowers its price, it won't do so using storms" (Angrist, Graddy, and Imbens 2000). Route a pricing question to the PRTE ladder below, naming the policy that will move the price.

Before you estimate, establish that the mechanism exists. An instrument is a treatment assignment mechanism, and the design's credibility comes from that mechanism operating in the world, not from the estimator. Interview whoever runs the assignment, the queue owner or the pricing manager, and ask who ended up treated and why. Do not ask them to name an instrument, which is not a question anyone outside this literature can answer. The best instruments come from institutional knowledge of a program and rarely from a new dataset (Angrist and Krueger 2001).

Five assumptions, argued separately because they have different characters (Imbens 2014):

1. SUTVA, at the level of the instrument and not only the treatment: unit i's potential treatment and potential outcomes depend on i's own instrument alone. The violation to name is instrument-level spillover, a seeded user's friends changing behavior because of the seed itself. The LATE framework does not accommodate it, being built on unit-level potential treatment mappings, so the route is a partial-interference or network model (field-experiment).
2. Unconfounded assignment of the instrument. Can hold by design (randomized encouragement) or conditionally on covariates. On its own it justifies the reduced-form ITT effects ONLY, never the IV ratio.
3. Exclusion. Substantive in essentially every application; Imbens' line is that it holds by design only in double-blind placebo trials. Argue it separately by compliance type: the instrument can push always-takers and never-takers toward outcome-relevant side actions even though it cannot change their treatment (draft-lottery never-takers stayed in school; a retention-offer trigger that also flags the account for priority support).
4. Monotonicity (no defiers). Safe when the instrument is a one-directional incentive (letter, subsidy, default). Strong in examiner and judge designs: by Vytlacil's theorem it is equivalent to every examiner ranking the cases identically and differing only in where the cutoff falls, which fails whenever examiners weight criteria differently or differ in skill (Chan-Gentzkow-Yu find skill accounts for about 40 percent of the variation in radiologist leniency). A leniency design needs less than this. The operative condition is average monotonicity, no unit a defier on average across pairwise comparisons, which is necessary and sufficient for nonnegative weights and is testable. The leniency section below carries the weakening and the test; do not price a leniency design against the uniform condition. One-sided noncompliance buys the uniform version for free and turns the LATE into an effect on treated compliers.
5. Relevance, tested with the discipline in the next section, never with a full-sample afterthought.

The estimand under all five is the complier average effect (LATE). Compliers are the focus because theirs is the only point-identified average, an honest second best. When the first stage varies across units, the LATE weights units by their first-stage responsiveness, so the compliers are defined by responsiveness and not by membership alone (Huntington-Klein 2020). Report the compliance shares (always-takers, never-takers, compliers, three lines of code) and, when the ATE was the stated target, Manski bounds alongside the LATE. When the stated question is a rollout or an incentive change (a bigger subsidy, wider eligibility, "what if we gave it to everyone"), name the target as a PRTE and take the middle rung (Mogstad-Santos-Torgovitsky 2018): the LATE and the policy parameter are weighted averages of the same marginal treatment response functions, so the estimands already computed bound the policy parameter under stated MTR restrictions, with the extrapolation distance alpha explicit. The ladder to report: ITT/LATE first; MST bounds next, priced by the named restrictions and alpha; assumption-free Manski/Balke-Pearl bounds as the floor. When the assignment itself is the policy lever (encouragement campaigns, defaults), the ITT is the headline and rests on the fewest assumptions.

The inference regime: abandon the 2SLS t-test

The binding constraint in modern IV practice is inference, and the canon's position (Keane-Neal 2024) is blunt:

• Test significance with the Anderson-Rubin test at EVERY instrument strength (CLR when overidentified; they coincide with one instrument). Just-identified, AR is simply the robust t-test on the instrument in the reduced form, so it costs one regression.
• Confidence intervals only by inverting AR/CLR, never from the 2SLS standard error. Valid intervals cannot be symmetric in finite samples, and an unbounded AR interval is an honest statement that identification is not established, never something to suppress by switching back to t-intervals. The Mixtape (Cunningham, Causal Inference: The Remix, ch. 7) reports AR intervals "for robustness"; this skill makes them the only interval, because the two disagree in the chapter's own fish example: at an effective F of 22.929 the 2SLS estimate is -1.119 with a robust standard error of 0.431, so the t-interval is about [-1.96, -0.27] against a printed AR interval of [-2.186, -0.394]. Both ends move, and the AR interval is asymmetric.
• Hold instruments to a robust first-stage F of about 50 (about 50/K^(3/4) with K instruments), not 10. F of 10 only controls two-tailed t size; below roughly 50, 2SLS is quite likely farther from the truth than OLS unless endogeneity is severe. The sample-F-to-certified- population-F ladder, and when a severe-endogeneity relaxation of this bar is credible, are in references/details.md. This bar prices 2SLS bias, so it moves with the estimator: it does not transfer to a jackknife estimator in a many-instrument design (see the leniency section). The Mixtape calls an F of 17.6 "strong enough for identification" and the fish instrument "strong (F > 22)", both inside the band this ladder distrusts (a sample F of 23.1 certifies a population F of 10), so a reader who copies that language into a current submission will draw the objection.
• Below F = 3.84 do not run IV at all; the AR interval will be unbounded and rightly so.
• The reason the t-test dies even at strong F is power asymmetry, a mechanism worth knowing when refereeing: the 2SLS standard error is spuriously small exactly when the estimate lands near OLS. An IV estimate close to OLS with F between 10 and 50 and a significant t is the modal reversed result in their AER audit (12 of 49 papers, 24 percent).
• Estimator by identification status: just-identified, the 2SLS point estimate is fine (the estimate, not its t-test). Overidentified: LIML under homoskedasticity, CUE under heteroskedasticity or clustering, with CLR for inference; avoid 2SLS and two-step GMM. Never mix (no CLR p-values stapled to a 2SLS estimate; no screening on t before applying AR).
• Fewer instruments are better. Bias, size, and asymmetry all worsen with K. Legitimate extra instruments come from functions of one continuous instrument or interactions with exogenous covariates, which is exactly how Angrist-Krueger ended up many and weak.
• Compute the F heteroskedasticity- or cluster-robust, always; effective F (Montiel Olea-Pflueger) when overidentified and non-homoskedastic. Match clustering to the level of instrument assignment.

This regime is written for designs with one instrument or a handful. A leniency design has hundreds, and three of these rules change there: the F bar stops applying, AR is the wrong robust test because the many-instrument versions are not robust to treatment-effect heterogeneity, and the clustering reflex has to be re-derived from the assignment mechanism. The leniency section below states each replacement.

Overidentification and heterogeneity, one rule

Overid-test rejections conflate instrument invalidity with treatment-effect heterogeneity: different instruments (or share combinations) move different complier populations, so divergent estimates need not mean an invalid instrument, and with correlated instruments the pooled estimate need not be any complier average at all (Imbens 2014; Mogstad-Torgovitsky-Walters 2021 via Borusyak-Hull-Jaravel 2025). A rejected J-test is a red flag for interpretability either way; what it does not do is cleanly convict the instrument. Say which reading you take and why.

Shift-share instruments: pick a path and defend it

A shift-share instrument z_i = sum_k s_ik g_k (common shifts g_k weighted by exposure shares s_ik) does not get identification from "cov(z, eps) = 0". Commit to one of two paths (Borusyak-Hull-Jaravel 2025), each with its own estimator, standard errors, balance tests, and disqualifier:

• Exogenous shifts: the shifts are a shock-level natural experiment (possibly conditional on shift-level controls); the shares may be arbitrarily endogenous. Disqualifier, near-verbatim from their Table 2: do not take this path if you would not use the shifts directly as an instrument in a shift-level regression, for example because they are too few or endogenous.
• Exogenous shares: every individual share satisfies a parallel-trends-style exogeneity condition; shifts only pool the K share instruments and matter for power. Disqualifier: do not take this path if you would not use a single share as an instrument on its own, for example because the shares are generic. Generic shares (industry mix) proxy exposure to any industry shock; tailored shares (origin-country migrant networks for migration treatments) can qualify.

Three mechanical rules that are silently violated in practice:

1. Control for the sum of shares whenever shares are incomplete (do not renormalize), interacted with period indicators in stacked designs.
2. On the shift path, use exposure-robust inference: the AKM variance estimator or the equivalent shift-level regression (ssaggregate), which also delivers the honest first-stage F. Conventional clustering misses the mechanical correlation between units with similar shares.
3. Report the effective number of shifts, 1/sum_k s_k^2 on the importance weights. A small value means a few shocks drive everything and no asymptotics protect you, whatever N is.

Timing: measure shares at the beginning of the natural experiment generating the shifts, so shifts cannot feed back into shares, and lag only with a stated mechanism (it always costs power). On the share path, compute Rotemberg weights, name the shares that carry the design, and balance-test those shares against pre-period outcomes (Card's Philippines share fails this in every period, the canonical caught example). With many shares, TSLS is biased toward OLS: use JIVE, LIML, HFUL, or bias-corrected TSLS. In-sample estimated shifts (classic Bartik, Card) need the leave-out construction.

Formula instruments: recenter or control

Trigger rule (Borusyak-Hull 2023): if the treatment or instrument is computed from exogenous shocks plus nonrandom exposure by a known formula, shock exogeneity is not enough. Their one-sentence version: randomizing transportation upgrades does not randomize the market access growth generated by them. Recognition is the hard part; the standing examples are network spillover counts (number of treated friends), market-access measures, and simulated eligibility instruments, and the structure also covers media-coverage instruments and randomized rollouts propagating through nonrandom networks.

The fix is one-dimensional: simulate counterfactual shock vectors from a specified assignment process (a permutation class in natural experiments), recompute the instrument under each, average to get the expected instrument mu_i, then instrument with z_i - mu_i or control for mu_i. Recenter first in a true experiment; in a natural experiment prefer controlling for several candidate mu_i from different guessed assignment processes, which is doubly robust (a wrong candidate cannot introduce bias where none existed). The same draws give randomization inference and the balance test of the recentered instrument. The China HSR numbers (0.23 significant collapsing to 0.08 insignificant after recentering) are the calibration for how much pure exposure bias can look like an effect. Ordinary controls do not substitute: geography absorbing 82 percent of the instrument's variation still left a significant biased estimate.

Leniency designs: UJIVE and the five checks

Recognition: cases are routed to decision-makers who differ in strictness, and the routing is as good as random within a stratum. Judges, patent examiners, disability assessors, loan officers, child-protection investigators, radiologists, immigration officers, and any platform review queue that assigns by roster. The instrument is the decision-maker identity itself, and keeping it that way instead of collapsing it to a constructed leniency number drives everything below (Goldsmith-Pinkham-Hull-Kolesár 2026).

Two practices to drop first. Do not build an external leniency measure and plug it into a just-identified IV ("manual leniency IV"), because the construction details drive the bias and the second-stage standard errors are wrong. Do not read design strength off the variance of a constructed leniency measure, because estimation noise inflates it. Pass the examiner dummies in directly and let the estimator do the leave-out.

The estimator is UJIVE (Kolesár 2013), which instruments treatment with leave-one-out fitted relative leniency: residualize the examiner dummies on the controls first, then fit the first stage without observation i. The reason it is the default here is arithmetic. Bias is proportional to the trace of the estimator's weighting matrix, and a leniency design is the setting that carries many instruments and many controls at once: 2SLS has trace K, so its bias scales in the number of examiners; JIVE has trace -L, so its bias scales in the number of controls and points the opposite way; UJIVE has trace zero. Bias-corrected 2SLS also has trace zero, but only under homoskedasticity. IJIVE does not fully clear the bias, though in practice it lands close. The trace algebra is in references/details.md.

The Mixtape (ch. 7) demonstrates JIVE in its bail exercise, calling that treatment "somewhat backwards looking", and flags UJIVE itself as the more robust version. This skill runs UJIVE: by the trace argument above, many examiners and many controls at once leave JIVE's many-covariate bias live and pointing opposite to 2SLS's. Report JIVE beside UJIVE as a diagnostic.

The five checks, in their order:

1. Name the controls that buy as-good-as-random assignment, and let the assignment mechanism pick both the estimator and the standard errors. The institutional story is what names the controls, so with no institutional story there is no principled control set. Keep necessary controls (in every specification) separate from precision controls (optional, and in their application these widened the intervals, because the first-stage noise the extra controls introduce outweighed the gain in the outcome equation). E[z|w] has to be linear in the covariates, which is automatic when w is fixed effects and otherwise needs interactions or higher-order terms (sufficient in Kolesár 2013, necessary in Blandhol et al. 2026). Assignment can be random and the design still broken if units act on the realization: Gaudet, Harris, and St. John (1933) recorded defendants changing their plea to draw a different judge. Where the data record it, instrument with the initial assignment instead of the final one, and ask the administrators how often re-routing happens, since check 2 misses sorting on unobservables. The platform analogue is the appealed moderation decision or the re-submitted ticket.
2. Balance, run as the same UJIVE specification with the covariate as the outcome. This is the step that gets done wrong. Do not regress observables on a constructed leniency measure, which manufactures mechanical correlation and carries errors-in-variables bias even when the measure is leave-out, and do not report the joint F on the examiner dummies, which is invalid with many examiners (Anatolyev-Sølvsten 2023). Running balance as UJIVE puts any imbalance in the same units as the treatment effect, so the two are directly comparable: in their patent reanalysis the balance coefficients came in about ten times smaller than the effects. The same machinery on a post-assignment variable tests exclusion (their instance is months under review). The Mixtape (ch. 7) calls balance "an absolute must" and says nothing about how, and the two implementations a reader reaches for first are the two ruled out here.
3. Estimate by UJIVE and report the alternatives beside it. 2SLS on the examiner dummies landing between OLS and UJIVE is the signature of many-instrument bias pulling toward OLS, and 2SLS standard errors 3 to 4 times tighter than UJIVE's are that same pathology showing up in the variance.
4. Test monotonicity (below).
5. Characterize compliers (below).

Inference. Clustering follows assignment, so with independent assignment to examiners plain robust standard errors are valid and clustering on the examiner is never justified. Say so explicitly when a referee expects examiner clusters. Clustered assignment (one doctor covers a whole shift) also changes the estimator, calling for leave-own-cluster-out UJIVE (Frandsen-Leslie-McIntyre 2025), so the clustering decision comes before the estimation. Full argument: ../causal-design/references/shared-rules.md.

Strength and the weak-instrument fallback. Do not read the first-stage F against a threshold here. UJIVE stays approximately unbiased and consistent even as E[F] approaches one, provided sqrt(K) times (E[F] - 1) is large, so that product is the statistic to report. F is also mechanically small in these designs because the formula divides by K, so a modest F is uninformative about whether leniency moves treatment. The heterogeneity-robust plug-in variance absorbs the Bekker many-instrument term, so one standard error covers both. When sqrt(K) times (E[F] - 1) is small, the fallback is Yap 2025, which substitutes the null-imposed residual into the UJIVE standard error. The many-instrument AR of Mikusheva-Sun 2022 and Matsushita-Otsu 2024 do not apply here, since neither survives treatment-effect heterogeneity, which a leniency design has by construction.

Monotonicity, weakened and tested. Price the design against average monotonicity (Frandsen-Lefgren-Leslie 2023), meaning no unit is a defier on average across pairwise comparisons. That condition is necessary and sufficient for nonnegative weights on the individual effects, which is what uniform monotonicity was protecting against in the first place, and it is strictly weaker. It is not invariant to first-stage misspecification: when examiners work across several strata with stratum-specific leniency, an additive first stage can break average monotonicity where the true relative leniency satisfies it. Check robustness to interacting examiner assignment with the stratum fixed effects, and expect that flexibility to cost precision.

The test: pick a v determined before assignment, replace the outcome with v times treatment, hold the treatment, instruments, and controls fixed, and run UJIVE. The estimate is a convex weighted average of v under the same weights as the headline estimate, so for binary v it has to land in [0, 1]. Outside those bounds something in the LATE theorem has failed. Two limits to state when reporting it: the null is joint across assignment, exclusion, and monotonicity, so a rejection does not localize; and it catches only gross violations, since on-average defiers have to be both common and unlike the compliers to push a weighted average out of [0, 1]. What it buys over testing the stronger condition is that its rejections bear directly on sign reversals, and it needs neither bounded outcomes nor a small number of decision-makers. Sigstad 2026 is the calibration for how much to worry: monotonicity is often violated in judicial panels, and the disagreements are too small to move leniency IV estimates much.