Iv

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.

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.

Compliers and external validity. The same trick with non-binary v identifies complier means of any pre-assignment characteristic under the headline weights. Put the complier mean beside the sample mean covariate by covariate and let the gaps carry the external-validity claim. Untreated compliers come from using one minus the treatment. To pool the two, run UJIVE of v times (2x - 1) on (2x - 1). This doubles as a monotonicity check, since a complier mean outside logical bounds rejects. Do not carry the MST extrapolation ladder into a leniency design without flagging it: neither the MTE-curve approach nor MST has been formalized for many decision-makers or controls.

Chyn-Frandsen-Leslie 2025 (JEL 63(2)) is the companion practitioner's guide. Read both when the design is the whole paper.

Diagnostics battery

1. Robust first-stage F, computed at the level the design lives at: in-bandwidth for fuzzy RD (that skill), shift-level for shift-share, cluster-robust at the assignment level otherwise. Read it against the ladder in references/details.md, not against 10. Leniency designs are the exception: report sqrt(K) times (E[F] - 1) and skip the threshold entirely.
2. Compliance-share table (binary instrument): pi_a, pi_n, pi_c. A thin complier slice means wide intervals and honest extrapolation language.
3. Balke-Pearl inequality checks (binary Y, X, Z): four testable inequalities implied by the assumptions; a violation means the design is internally inconsistent, and passing proves nothing. Worked flu-data numbers in references/details.md.
4. OLS next to IV, always, and the OLS-proximity audit: t-significant IV near OLS with moderate F is the configuration to distrust. When IV lands above OLS, name which explanation you are claiming, measurement error in the endogenous regressor or higher complier returns, and why.
5. Overid J (with CUE) where applicable, interpreted under the heterogeneity rule above.
6. Balance of the instrument on predetermined covariates, with the design's controls and the design's standard errors (exposure-robust on the shift path; RI for recentered instruments). On the share path this is a pre-trends exercise and did-style scrutiny applies.
7. TSLS-LIML divergence in overidentified designs as a cheap weak/many-instrument alarm. Also re-estimate with random draws in place of the instruments: the second stage typically still looks reasonable while the first-stage F sits near one (Bound, Jaeger, and Baker 1995).
8. Placebo outcomes: lagged outcomes as the dependent variable, RI-based for recentered designs (sharp null sidesteps the RI-with-heterogeneity complication). 8b. Placebo first stage, bounded by the mechanism: name the margin the mechanism can reach and show the instrument does not move treatment past it. Quarter of birth moves high-school completion and not college completion, because compulsory schooling binds only through high school (Angrist-Krueger 1991). A cost shifter should move price and not assortment, a delivery-radius instrument purchase and not browsing. 9b. Leniency designs run the battery in their own section instead: UJIVE balance regressions on the covariates and on a post-assignment variable, the [0, 1] monotonicity test, and the complier table. Item 7 is replaced there by reporting UJIVE next to OLS, 2SLS, and JIVE, where 2SLS sitting between OLS and UJIVE is the many-instrument alarm.
9. MST feasibility tests, two cheap re-solves of the extrapolation LP (Mogstad-Santos-Torgovitsky 2018): restrict the MTR pairs to zero average selection bias and re-solve, then to zero selection on gains. Infeasibility rejects that behavioral hypothesis and turns the OLS-IV gap of item 4 into a formal test; with unrestricted MTRs, infeasibility is item 3's Balke-Pearl falsification in general form.

Exhibits: three figures and one table

Three figures carry an IV paper: the instrument's own variation, the first stage, and the reduced form (Angrist-Krueger 1991 for the pair, Cunningham-Finlay 2012 for the three-figure structure). Never plot the outcome against fitted treatment, a processed quantity that reads as opaque. Where a placebo series exists (an untreated market, an unaffected product category), plot it on the same axes so the reader can see the shock hit one thing. The table carries OLS beside IV, the first-stage coefficient on the instrument, the strength statistic (effective F, or sqrt(K) times (E[F] - 1) in a leniency design), N, and the AR interval in brackets under the point estimate, which puts the valid interval where a reader looks for it.

The live disputes, carried honestly

Whether the just-identified 2SLS t-test is rescuable. Angrist-Kolesár 2024 defend it (size is approximately fine at realistic endogeneity); Lee et al. 2022 patch it with tF/VtF critical values. The canon's position (Keane-Neal) is that both miss the binding problem: power, not size. The t-test has near-zero power against effects opposite the OLS bias, which under publication bias manufactures spurious literature-wide consensus, and tF inherits the asymmetry. Default in a few-instrument design: AR/CLR and the F-50 standard. When a referee pushes back with Angrist-Kolesár, report both and cite the dispute. The AR test costs one regression, so there is no economy argument for the t-test.

Two further disputes are scope boundaries this skill draws, not positions either set of authors picked. The F-50 bar and the AR default both come out of the few-instrument literature, and neither transfers to a leniency design, where strength is read off sqrt(K) times (E[F] - 1) and the weak fallback is Yap 2025. Keane-Neal and Goldsmith-Pinkham-Hull-Kolesár do not cite each other, so say which regime you are in before quoting either bar. All four disputes are in references/canon.md.

R implementation

The complete runnable pipeline is scripts/iv_template.R (estimation, the full weak-IV inference menu, compliance shares and Balke-Pearl checks, both shift-share paths with exposure-robust inference, recentering with RI, and an optional ivmte block for MST extrapolation bounds), with every call verified against package documentation. The core:

library(fixest); library(ivmodel); library(ivDiag)
est <- feols(y ~ w1 + w2 | x ~ z, data = df, vcov = ~cl)   # 2SLS point estimate
m   <- ivmodel(Y = df$y, D = df$x, Z = df$z, X = df[, c("w1","w2")])
AR.test(m); CLR(m)                       # identification-robust tests + inverted CIs
LIML(m); Fuller(m)                       # overidentified / many-weak point estimates
ivDiag(data = df, Y = "y", D = "x", Z = "z",
       controls = c("w1","w2"), cl = "cl")   # bootstrapped F, effective F, AR, tF in one call

Shift-share: ShiftShareSE (reg_ss / ivreg_ss, AKM and AKM0) and the shift-level equivalent regression via ssaggregate. Recentering is a hand-coded permutation loop (no package needed; the template has it). Leniency: ManyIV, the authors' own package, which returns OLS, 2SLS, UJIVE, IJIVE, and JIVE from one call with heterogeneity-robust standard errors, and which the paper's own tables were produced with. Package index with versions, links, and traps in references/details.md.

Methods paragraph template

Treatment here is chosen, not assigned: [selection story]. We instrument with [instrument], which shifts the incentive to take treatment through [channel]. Assignment of the instrument is [randomized / plausibly unconfounded conditional on X], which justifies the reduced-form intention-to-treat estimates; the IV estimate additionally requires exclusion, which we assess separately for always-takers and never-takers ([arguments]), and monotonicity, which [holds because the instrument is a one-directional incentive / is threatened because this is an examiner-style design, and we report the corresponding bounds]. The estimand is the complier average effect (Imbens 2014); compliers are [share] of the sample. Our instrument's robust first-stage F is [value], certifying a population F of at least [ladder value] at 95 percent confidence; following Keane and Neal (2024) we report Anderson-Rubin [CLR] tests and inverted confidence intervals in place of 2SLS t-statistics. [Shift-share designs add: identification follows the exogenous-[shifts/shares] path of Borusyak, Hull, and Jaravel (2025), with (exposure-robust inference and the effective number of shifts reported / Rotemberg weights and per-share balance tests reported).] A limitation of this design is that it identifies effects for compliers only. [If the question stops at the compliers, say so and stop. Otherwise:] Because our policy question concerns [the rollout / the incentive change], the target is the policy-relevant treatment effect for [policy population]. Following Mogstad, Santos, and Torgovitsky (2018) we report bounds on it consistent with our IV and OLS estimands under [the MTR restrictions imposed: bounded outcomes / decreasing MTE / spline of stated degree], for a policy that raises participation by [alpha]. The bounds [range] widen as the extrapolation grows, which is the price of asking about individuals the instrument did not move.

A leniency design shares almost none of that structure, so it gets its own template:

Cases here are assigned to [decision-makers] who differ in strictness, and assignment is [randomized / as good as random conditional on the [stratum] fixed effects that [institution]'s routing rule makes necessary]. We instrument [treatment] with the full set of [decision-maker] indicators and estimate by UJIVE (Kolesár 2013), which instruments with a leave-one-out estimate of covariate-residualized leniency and stays unbiased with many decision-makers and many controls at once, where 2SLS and JIVE do not (Goldsmith-Pinkham, Hull, and Kolesár 2026). We report OLS, 2SLS on the indicators, and JIVE alongside. [If assignment is independent across units:] Because assignment is independent across [units], we report heteroskedasticity-robust standard errors and do not cluster on [decision-makers], following Goldsmith-Pinkham, Hull, and Kolesár (2026). [If assignment is clustered:] Because a single [decision-maker] covers an entire [shift], we cluster at the [shift] level and use the corresponding leave-own-cluster-out estimator. Instrument strength is sqrt(K)(E[F] - 1) = [value] across K = [number] [decision-makers]. We do not report the first-stage F against a threshold, because it divides by K and is small here even when leniency moves treatment substantially. We assess assignment by running the same UJIVE specification with each pre-assignment covariate as the outcome, which puts any imbalance in treatment-effect units: the coefficients are [magnitude] times smaller than the estimated effects. We assess exclusion the same way, using [post-assignment variable] as the outcome. The estimand is a convex weighted average of individual treatment effects under average monotonicity (Frandsen, Lefgren, and Leslie 2023), which is weaker than the usual no-defiers condition and is necessary and sufficient for the weights to be nonnegative. We test it by re-running the specification with [binary pre-assignment variable] times treatment as the outcome, where the estimate must lie in [0, 1]: we obtain [value]. A limitation of this test is that it detects only gross violations, since on-average defiers have to be both common and unlike the compliers to move a weighted average outside those bounds, and its null is joint across assignment, exclusion, and monotonicity, so a rejection would not tell us which failed. Compliers resemble the full sample on [characteristics], which is the basis for reading the estimate as informative beyond the marginal cases. We do not extrapolate further, because the frameworks for doing so have not been formalized for designs with many decision-makers.

Every claim traces to references/canon.md; keys live in ../causal-design/references/causal.bib.

Handoffs

• causal-design: whether IV is the right tool at all; clustering and inference questions shared across designs.
• rdd: fuzzy RD is IV at a cutoff; its first-stage and exclusion discipline lives there, the weak-IV inference regime here.
• did: the share-exogeneity path is a stack of DiD-style exposure designs, so parallel-trends scrutiny and pre-trend tools from did apply to share balance.
• field-experiment: randomized encouragement designs end to end (including the ITT/LATE analysis) and randomization inference on a simple physically randomized instrument; recentered and formula instruments keep their RI machinery here.
• Perceived-treatment designs, where an actual feature instruments the perceived feature, arrive here: the exclusion and weak-instrument discipline apply to them unchanged.
• preregister: pre-specifying the instrument, specification, and weak-IV fallback before outcomes are seen (experiment-first skill; adapt its structure for quasi-experimental PAPs).