git:20261009.a3c7501 to git:20261009.6a149ef

---

name: iv

description: Design, estimate, validate, and write up an instrumental-variables analysis: single-instrument LATE designs, weak-instrument-robust inference, shift-share instruments, formula instruments that need recentering, and leniency (judge and examiner) designs estimated by UJIVE. TRIGGER on "instrumental variable", "IV", "2SLS", "LATE", "complier", "exclusion restriction", "first stage", "weak instrument", "Anderson-Rubin", "shift-share", "Bartik", "judge design", "judge IV", "examiner design", "examiner leniency", "UJIVE", "JIVE", "jackknife IV", "LIML", "Rotemberg weights", "exposure-robust", "AKM", "price endogeneity", "cost shifter", "Hausman instrument", "simulated eligibility", "recentered instrument", or any setting where treatment is chosen by agents and an incentive or cost shifter moves it. Randomized encouragement designs are led end to end by field-experiment.

---

# Instrumental variables

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. The skill stops at the four stop points in

../causal-design/references/shared-rules.md (section "Stop points") and puts each choice to the user.

## Six designs to recognize

| Design | Canonical case | Marketing analogue | What kills it |

|---|---|---|---|

| Randomized encouragement with noncompliance (routes to field-experiment) | 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 (Angrist, Graddy, and Imbens 2000), and need not be the elasticity a firm faces

when it sets price itself. Cunningham (The Mixtape, online ch. 7 sec. 7.7) puts it as

*"But when the firm lowers its price, it won't do so using storms!"* 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 that skill accounts for 39 percent of the variation in radiologists'

diagnosis rates, which is the leniency measure in this design). A leniency design needs less

than this. The operative condition is average monotonicity, no unit a defier on average

across pairwise comparisons. Frandsen, Lefgren, and Leslie (2023) show it is sufficient for

nonnegative weights, Goldsmith-Pinkham, Hull, and Kolesár (2026) state it is also necessary,

price a leniency design against the uniform condition. One-sided noncompliance (no

always-takers) buys the uniform version for free, and the LATE then equals the average

treatment effect on the treated (ATT).

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 treatment

or the instrument is non-binary and the first stage varies across units, the LATE weights units

by their first-stage responsiveness. Compliers are then defined by responsiveness and not by

membership alone (Huntington-Klein 2020). With binary Z and D every complier moves by the same

one unit, so this weighting drops out. 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, the AR test of a zero

effect is the robust t-test on the instrument in the reduced form, so it costs one

regression. The inverted interval repeats that test with y - b0 x as the outcome for each

candidate b0.

- 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

- Hold instruments to a robust first-stage F of about 50 (about 50/K^(3/4) with K instruments),

not 10. A sample F of 10 bounds worst-case two-tailed t size at about 13.5 percent, not 5.

Under a uniform prior on rho in [0, 0.45], 2SLS beats OLS in distance to the truth 47

percent of the time at population F 10 and 65 percent at 29.44, the population F that a

sample F of 50 certifies (Keane and Neal 2024, Table 5). 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).

- 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.

## 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.

## 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).

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.

(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

## 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:

```r

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

Report each effect with the results sentence in ../causal-design/references/shared-rules.md

(section "Results sentence"): magnitude, direction, a benchmark, and the calibration vocabulary.

> 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]. [If this is an examiner-style design,

> use the leniency template below in place of this paragraph.] 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 approximately 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, which is weaker than the usual no-defiers condition. The condition is sufficient

> for the weights to be nonnegative (Frandsen, Lefgren, and Leslie 2023) and also necessary

> (Goldsmith-Pinkham, Hull, and Kolesár 2026). We test it by re-running the specification with

> [binary pre-assignment variable] times treatment as the outcome, whose estimand must lie in

> [0, 1]: the estimate is [value], and its 95 percent interval [interval] [overlaps / lies

> wholly outside] [0, 1]. 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. [If a counterfactual policy is the target:]

> We bound the effect of [policy] using the framework of Kolesár, Montiel Olea, and Roth (2025),

> which does not require monotonicity. [Otherwise:] We do not extrapolate beyond the compliers.

Every claim traces to references/canon.md. Keys for the canon papers live in

../causal-design/references/causal.bib; works cited only in passing may have no entry there yet.

## Handoffs

- causal-design: whether IV is the right tool at all; clustering and inference questions shared

across designs. This skill does not take control functions or Gaussian copulas. The decline

paragraph at causal-design's triage question 3 carries the pointers for them.

- 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.

- Preregistration: the user writes it themselves; this skill supplies the instrument, specification,

and weak-IV fallback to pre-specify before outcomes are seen.