causal-design git:20260801.5eed4e2A

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---
name: causal-design
description: Triage any causal question to the identification strategy the data can support, then hand off to the owning method skill; owns the selection-on-observables branch (overlap, doubly robust estimation, double ML, causal forests, policy learning, sensitivity analysis) and the inference rules shared across designs. Produces the design recommendation with the assumption that licenses it, the estimand and its subpopulation, R estimation code for the observables branch, and a drafted taxonomy paragraph. TRIGGER on "causal inference", "identification strategy", "which method", "research design", "endogeneity", "quasi-experiment", "natural experiment", "observational study", "selection on observables", "unconfoundedness", "conditional ignorability", "matching", "propensity score", "doubly robust", "AIPW", "double machine learning", "DML", "causal forest", "CATE", "policy learning", "targeting", "sensitivity analysis", "omitted variable bias", "Oster bounds", "coefficient stability", "overlap", "trimming", "marketplace experiment", "surrogate index", "mediation", "mediation analysis", "indirect effect", or any "how do I estimate the effect of X on Y" question with no design chosen yet. Once a design is chosen, the method skills own it: field-experiment, did, synthetic-control, rdd, iv.
---

# Causal design triage

The router of the family, grounded in a read canon of two hand-picked reviews
(references/canon.md, current as of 2026-07-28): Imbens (2024) supplies the assumption axis
(what licenses identification), and Li, Luo, and Pattabhiramaiah (2024, hereafter AMA) the
marketing data-shape axis (how many treated units, how many pre-periods, how rich the
covariates). The deliverable is a design recommendation carrying four things: the assumption
that licenses it, the estimand it actually identifies WITH its subpopulation named, the
handoff to the owning skill, and, for the one branch no method skill owns (selection on
observables), estimation code and a methods paragraph. Marketing's framing throughout:
randomization is the gold standard, and quasi-experimental work substitutes statistical rigor
for design rigor (AMA); a design that fails its gate is a verdict, not an obstacle.

Refresh path: the panel-methods corner moves fastest. To update, run the litreview skill on
quasi-experimental methods in marketing since the canon date and fold results into
references/canon.md as flagged addenda.

## The triage: three questions in order

1. Was assignment randomized, or as good as (lottery, randomized rollout)? Yes:
   field-experiment. Two cautions at this gate: naive sample means from adaptive/bandit
   experiments are biased (the arm that looked worse early is truncated; Imbens), and
   suspected interference changes the DESIGN, not just the analysis (routing below).
2. If observational: is unconfoundedness defensible with PRETREATMENT covariates only? The
   conditioning set may contain only non-descendants of treatment and outcome, normally
   justified by temporal precedence. Verbatim, because it is the highest-frequency error
   (Imbens 2024): "In practice, using variables causally affected by the treatment or
   outcome is the most common mistake in choosing variables to condition on in estimating
   average treatment effects using unconfoundedness approaches." The marketing case where
   yes is credible: the targeting rule is known and observable (a campaign targeted on
   demographics or behavior selects on observables by construction; AMA). Tiebreak: a
   known DETERMINISTIC rule (treatment jumps at a cutoff on an observed score) is the rdd
   case, question 3, not this branch; the observables branch needs probabilistic
   assignment, since a deterministic rule makes every propensity 0 or 1 and leaves no
   overlap to estimate on. Yes: the selection-on-observables branch below, owned by this
   skill.
3. If unconfoundedness is not plausible, look for structure in assignment:
   - An incentive or cost shifter moves treatment with no direct path to the outcome: iv.
     It identifies the LATE for compliers only; the ATE needs substantially stronger
     assumptions, and the complier population is the focus because it is the only one
     identifiable (Imbens).
   - Treatment switches at a threshold on a running variable: rdd (fuzzy RD is IV at the
     cutoff).
   - Treatment switches on over time for some units with untreated comparisons: the panel
     branch below, routed by data shape between did and synthetic-control.
   - No structure at all: bounds and sensitivity analysis (the ladder below), or advise
     against the causal claim. Estimate under the best defensible conditioning anyway and
     report how much calibrated confounding overturns it, or report Manski bounds alone;
     the sensitivity report, not the point estimate, is the deliverable.
   - Marketing's regression-based endogeneity corrections (control functions, Gaussian
     copulas; the third leaf of the AMA figure) sit outside this family's coverage: the iv
     skill's exclusion and relevance discipline is the nearest relative, and copula
     identification rests on distributional assumptions that need their own defense.

## The panel branch: routing by data shape

The AMA heuristic: DiD/SC-family methods match on outcomes (pretreatment paths),
propensity-family methods match on covariates; pick the branch by which matching the data
supports. Within outcomes-matching, crossed with the Arkhangelsky-Imbens (2024) three-axis
taxonomy (data type, frame shape, assignment mechanism; did skill):

- Many treated units, parallel trends plausible (only its pretreatment shadow is testable;
  did owns the statement of which variant is imposed): did. Same-time adoption: TWFE is
  fine; staggered: Callaway-Sant'Anna, Sun-Abraham, or stacked regression (whose implicit
  weights carry a caveat in did), and justify the clean controls (AMA).
- One or few treated aggregate units, long pre-period: synthetic-control (few treated
  CLUSTERS of micro units with plausible parallel trends stay in did on its few-clusters
  map). The AMA gate, both parts: plot treated vs fitted counterfactual and verify
  pretreatment fit, AND run a backdating exercise; "only using the methods that satisfy
  both best practices." Both parts are necessary, never sufficient: backdating assumes
  strict exogeneity and backfires under selection on recent shocks, and
  synthetic-control's fuller feasibility gate (pre-fit quality, T0 length, overfitting
  screens) controls the final verdict.
- The routing result between them: under selection on lagged outcomes with autocorrelated
  errors, DiD is inconsistent while SC is consistent (Arkhangelsky-Hirshberg, via the
  panel survey, Arkhangelsky and Imbens 2024). The DiD-to-SC-to-SDID decision path lives
  in did and synthetic-control.
- Data-shape fan-out when neither default fits (estimator details in synthetic-control's
  extensions map): treated outcome outside the donor convex hull: augmented DiD (Li and
  Van den Bulte 2023); outcome in range but too few pre-periods for SC: forward DiD (Li
  2024); control units far fewer than pre-periods: HCW OLS (Hsiao, Ching, and Wan 2012);
  many treated units or short panels: generalized synthetic control / factor models (Xu
  2017) or matrix completion (Athey et al. 2021), with the warning that the gsynth
  parametric bootstrap yields biased CIs, subsampling or the Li-Sonnier corrections
  instead (Li and Sonnier 2023, via AMA); unit AND time reweighting wanted: synthetic DiD;
  the inference-procedure-by-data-shape rules live in synthetic-control.

## Selection on observables (the branch this skill owns)

- Overlap before estimation, always: estimate the propensity score and look at its
  distribution by arm. Violations move the ESTIMAND, not just the estimator: trim with the
  variance-minimizing rule of Crump et al. (2009) (the 0.1/0.9 rule of thumb is its common
  approximation) and report the retained population, or switch to overlap weights
  e(x)(1-e(x)) (Li, Morgan, and Zaslavsky 2018), which target the population that could
  plausibly receive either treatment.
- Estimator default: doubly robust (AIPW; Bang and Robins 2005), "the most attractive" under
  unconfoundedness with many covariates (Imbens): consistent if either the outcome model
  or the propensity model is consistent, tolerates ML-rate nuisance estimation. In
  practice: grf's causal forest with its built-in AIPW average effect, or double ML
  (Chernozhukov et al. 2018) when you want explicit nuisance control. Plain regression or
  matching are acceptable in low dimensions, with two caveats: fixed-number-of-matches
  matching is never fully efficient and its bias does not vanish with many covariates
  (Imbens), and marketing has moved off propensity score matching for its sensitivity to
  parametric assumptions (AMA).
- Weight by the ESTIMATED propensity score even when the true one is known; the true score
  is inefficient (Hirano, Imbens, and Ridder 2003).
- Heterogeneity has two different goals: describing CATEs (causal forest, Wager and Athey
  2018, honest inference without prespecified subgroups) and deciding WHO to treat, which
  is policy learning (Athey and Wager 2021; policytree), where the complexity of the
  policy class is the key choice. Do not answer a targeting question with a CATE map.
- Sensitivity analysis is mandatory, because unconfoundedness is untestable. The graded
  ladder (details in references/details.md): Manski bounds (assumption-free, honest,
  usually uninformative); calibrated confounder models (Rosenbaum and Rubin 1983, Imbens
  2003, with Oster 2019 and Cinelli-Hazlett 2020 as the modern reporting standards;
  sensemakr implements Cinelli-Hazlett); Rosenbaum design sensitivity (Rosenbaum 2002). An
  estimate that flips under mild confounding indicts the design, not the estimator.

## Rules shared across every design

- Estimand first, subpopulation named: IV and fuzzy RDD identify complier effects; DiD and
  SC identify the ATT of the treated units; overlap weighting identifies the overlap
  population. The methods template forces the clause.
- Clustering is a design property, not a data property (Abadie, Athey, Imbens, and
  Wooldridge 2023): cluster standard errors at the level at which treatment was assigned
  or the sample was drawn, and be able to say which; do not cluster by habit at whatever
  level makes the panel.
- Interference routing, by structure (designs, estimators, and diagnostics live in
  field-experiment): clustered interference routes to two-stage randomization (Hudgens
  and Halloran 2008, Crepon et al. 2013); network interference to exposure mappings
  (Aronow and Samii 2017) with exact tests (Athey, Eckles, and Imbens 2018); marketplaces
  and two-sided platforms to multiple randomization designs (Bajari et al. 2023, Johari
  et al. 2022).
- Combined experimental and observational data: the surrogate index for long-run outcomes
  (retention, LTV) from short experiments, valid only when all causal paths from treatment
  to the long-run outcome pass through the surrogates (Athey, Chetty, Imbens, and Kang
  2026). The family ships no estimation template for the surrogate index; Athey, Chetty,
  Imbens, and Kang's own empirical implementation is the recipe to follow, and the
  router's deliverable stops at the validity argument.
- Mediation (process evidence, treatment affecting the outcome through a mediator, natural
  direct and indirect effects) has NO route in this family: sequential ignorability is an
  assumption regime none of the family's skills carries. Where to go: Imai, Keele, and
  Tingley (2010) for identification and sensitivity analysis, Pieters (2017) for the
  marketing-native statement of what a mediation claim requires.

## Implementation

scripts/unconfoundedness_template.R is the runnable path for the branch this skill owns
(overlap diagnostics and trimming, grf AIPW, CATE and policy learning, sensemakr
sensitivity reporting), verified against package documentation. Package index with
versions, links, and traps in references/details.md. Every other branch's code lives in
the owning skill's template.

## Methods paragraph template

> Following the taxonomy in Imbens (2024), our setting is [randomized / observational with
> a defensible unconfoundedness argument / observational with assignment structure X /
> combined]. The assignment structure that identifies the effect is [structure], which
> points to [estimator], identifying [estimand] for [subpopulation]. [Observables branch:]
> We condition on [pretreatment covariates], none causally affected by treatment or
> outcome; overlap is [assessed how, trimmed how, moving the estimand to whom]; estimation
> is doubly robust [implementation]; and we report [Cinelli-Hazlett robustness values /
> Oster's delta] against a confounder as strong as [benchmark covariate]. [Panel branch:]
> Given [T treated units, K pre-periods], we use [method] per the data-shape criteria in
> Li, Luo, and Pattabhiramaiah (2024). A limitation I accept: [the identifying assumption
> this design rests on], stated where the choice is made, with its price named.

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

## Handoffs

- field-experiment: anything randomized, prospective experimental design, interference
  analysis, power.
- did: many treated units with timing variation; parallel-trends machinery.
- synthetic-control: few treated units, long pre-periods; SDID; factor models and matrix
  completion; the augmented/forward DiD and HCW conditions stated above.
- rdd: thresholds on running variables; the design gate and falsification battery.
- iv: instruments, shift-share, formula instruments; weak-instrument inference.
- preregister: pre-analysis plans once the design is chosen (experiment-first skill;
  quasi-experimental and measurement PAPs adapt its structure).