git:20260826.ef24590 to git:20260828.039723a

33 added, 113 removed. Audit A to A.

---

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", "panel fixed effects", "within estimator", "strict exogeneity", "marketplace experiment", "surrogate index", "mediation", "mediation analysis", "indirect effect", "conjoint", "AMCE", 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-unstructured, sae, sae-image, conjoint, steering.

+ description: Triage a 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), plain panel fixed effects, and the inference rules shared across designs (clustering, multiplicity, interference routing). TRIGGER on "identification strategy", "which causal method", "research design", "endogeneity", "quasi-experiment", "natural experiment", "selection on observables", "unconfoundedness", "propensity score", "doubly robust", "double machine learning", "causal forest", "policy learning", "sensitivity analysis", "Oster bounds", "overlap", "panel fixed effects", "strict exogeneity", "surrogate index", "mediation", or "how do I estimate the effect of X on Y" with no design chosen yet. Once a design is named, its method skill owns it.

---

# Causal design triage

- The router of the family, grounded in a read canon of three user-picked reviews

- (references/canon.md, current as of 2026-07-28): Imbens (2024) supplies the assumption axis

+ The router of the family, grounded in a read canon of four sources

+ (references/canon.md, current as of 2026-08-05): Imbens (2024) supplies the assumption axis

(what licenses identification), Li, Luo, and Pattabhiramaiah (2024, hereafter AMA) the

marketing data-shape axis (how many treated units, how many pre-periods, how rich the

- covariates), and Feder et al. (2022) the text-role axis (which role unstructured data plays

- in the graph). The deliverable is a design

+ covariates), Feder et al. (2022) the text-role axis (which role unstructured data plays

+ in the graph), and Abadie, Athey, Imbens, and Wooldridge (2023) the clustering rules the

+ family shares. 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.

+ Refresh path: run litreview on quasi-experimental methods in marketing since the canon date,

+ then propose additions to references/canon.md as flagged addenda.

## The triage: four 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). One

sub-route: profile experiments randomizing multiple attributes within alternatives

(conjoint, fully randomized factorial vignettes) go to conjoint, which owns the

per-component estimand family and its correction layers.

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).

- Cases are routed to decision-makers who differ in strictness (judges, patent examiners,

assessors, loan officers, reviewers) and the routing is as good as random within a

stratum: iv, which owns the leniency design. The decision-maker identity is the

instrument, 2SLS on it is biased, and the estimator is UJIVE.

- 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.

- Treatment switches on and off within unit, with no untreated comparisons and no

adoption date: plain panel fixed effects, the section below.

- 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.

4. Does unstructured data (text, image, audio, video) appear anywhere in the graph, and in

which role: confounder, outcome, treatment, or machine-coded measurement?

- causal-unstructured, with the role warnings below. Unknown-concept discovery and

- model-internals measurement: sae. Steering a model's internals (steered stimuli,

- steered model-respondents, dose-response manipulations) is instrument practice owned by

- steering; the design around it still routes through the questions above.

+ The role warnings below apply, and the measurement it rests on is settled before the

+ estimate, not after. Discovering an unknown concept, or measuring one from a model's

+ internals, is a measurement problem with its own validity argument. Intervening on a

+ model's internals to build stimuli or model-respondents is instrument practice, and the

+ design around it still routes through the questions above.

## 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.

## Plain panel fixed effects: no comparison group, no adoption date

The within estimator on Y_it = delta D_it + u_i + eps_it is licensed by strict exogeneity

conditional on the unit effect, E[eps_it | D_i1, ..., D_iT, u_i] = 0 for every t (Wooldridge

2010 for the unobserved-effects model and the assumption). It buys every time-invariant

confounder, observed or not, and lets D_it be arbitrarily correlated with u_i. It buys

nothing against a time-varying unobservable, feedback from past outcomes to current

treatment, or simultaneity. Feedback is what fires in marketing panels: last period's sales

set this period's promotion, last quarter's churn sets this quarter's retention spend. The

Mixtape's own 5% price premium on unprotected sex holds "under the assumption of strict

exogeneity", and the condom decision is settled inside the session alongside the price, so a

session-level shock moving both is the violation it rests on being absent. Reverse causality

and simultaneity defeat the estimator outright: Cornwell and Trumbull (1994) put crime on

police in North Carolina counties and the within estimate is 0.413 (0.027), the wrong sign

against Becker's (1968) prediction, because Y -> D was there all along. Exits: iv under

feedback or simultaneity, did when an adoption date and clean untreated or not-yet-treated

comparisons exist. The design needs within-unit variation in D and identifies no

time-invariant covariate's effect (the Mixtape's Table 8.3 shows the column of exact zeros

with (.) standard errors).

- The Mixtape (Cunningham, Causal Inference: The Remix, panel-data chapter) presents columns 3

- and 4 of its Table 8.2, from Cornwell and Rupert (1997), which add job tenure and then

- quadratics in years married and walk the marriage premium from the column 1 FGLS 0.083 to

- 0.033, as evidence about time-varying unobserved heterogeneity; under this skill's rule

- those columns are inadmissible, because years married and job tenure are plausibly

- consequences of marriage, so they condition on descendants of the treatment, which is

- verbatim the error Imbens (2024) calls the most common one. The chapter assumes constant

- effects and declares that scope. A non-absorbing time-varying treatment with heterogeneous

- effects has left it, the implicit weighting is live, and the dCDH weight diagnostic in did

- applies. Random effects, Mundlak-Chamberlain devices, and dynamic panel estimators stay out,

- and Wooldridge (2010) is the shelf for them.

+ Do not add controls that are consequences of the treatment, which is what makes columns 3 and 4

+ of the Mixtape's Table 8.2 inadmissible here (references/details.md for the argument, the

+ constant-effects scope it assumes, and the estimators that stay out).

```r

library(fixest) # panel: one row per unit-period, unit = the panel id

## Within-variation check first: units with no variation in d contribute nothing to the

## within estimate and every FE routine drops them silently (singletons return NA here).

nv <- tapply(panel$d, panel$unit, function(z) var(z, na.rm = TRUE))

c(no_within_variation = sum(is.na(nv) | nv == 0), units = length(nv))

pols <- feols(y ~ d, data = panel, cluster = ~unit) # u_i left in the composite error

within <- feols(y ~ d | unit, data = panel, cluster = ~unit)

etable(pols, within) # side by side: the gap is the unit effects at work, and

# no time-invariant covariate enters the within column.

## Stata FE standard errors instead (argument-name trap in references/details.md):

# estimatr::lm_robust(y ~ d, data = panel, fixed_effects = ~unit, clusters = unit,

# se_type = "stata")

```

## 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.

- The decision "depends on the nature of the sampling and the assignment processes only, and

- not on the presence of within-cluster error components in the outcome variable," so

- within-cluster outcome correlation is not a reason to cluster and the size of the change in

- your standard error is not evidence you needed it. Both errors are live and they are not

- symmetric. Robust standard errors can be ANTI-conservative, severely so when clusters explain

- much of the heterogeneity in treatment effects or potential outcomes. Clustered standard

- errors are always conservative and never anti-conservative, but the conservativeness scales

- with average sampled cluster size, so clustering "just in case" is not free. Under random

- sampling with unit-level random assignment, do not cluster at all; under clustered

- assignment, cluster at the assignment level; when the sampled clusters are a small fraction

- of the population, or few units are sampled per cluster, the choice stops mattering.

- One half of this decision is untestable and the skill states it rather than estimating it:

- the sample "is not informative" about what fraction of clusters was sampled, so "information

- about the need to adjust for clustered sampling must come from outside the sample," while the

- sample IS informative about clustered assignment. The Mixtape's rationale for clustering

- by panel unit, "to allow for correlation in the eps_it's for the same person i over time,"

- is the one reason AAIW rule out, and the answer often coincides only because panel units

- in a survey are genuinely the sampling clusters. Say which of the two you are invoking.

- Two further facts to carry. Robust standard errors are conservative rather than exact when

- the sample is a large share of the population and effects are heterogeneous (the Neyman

- finite-sample correction; `abadie2020sampling` buys the precision back if unit attributes

- predict the treatment effect). And for partially clustered assignment with large clusters,

- their CCV and TSCB estimators sit between robust and clustered and can be considerably

- smaller than conventional cluster standard errors; neither applies under perfectly clustered

- assignment, and this family ships no implementation of either. Scope: linear estimators only

- (least squares and fixed effects). Once the level is chosen, few-cluster inference is a

- separate problem with its own answer (MacKinnon, Nielsen, and Webb 2023; the map is in did).

- - Multiplicity, staged by what a false positive costs. One correction applied at every stage is

- wrong in both directions at once, so match the procedure to what the output is. SCREENING,

- where the output is a candidate list something downstream will re-test: FDR, at q = .10 and

- not .05, since a false positive costs one wasted follow-up. Benjamini-Hochberg is the

- default and holds under positive regression dependence; the Benjamini-Krieger-Yekutieli

- two-stage sharpened q-values that Anderson (2008) made the applied convention recover power

- by estimating the null proportion instead of fixing it at 1, at the price of an

- independence-flavoured guarantee and less stability. So BKY suits a screen over

- machine-generated candidates and BH suits estimates that share respondents; the choice is

- design-dependent, and say which you took and why. CONFIRMATORY, where each hypothesis is

- named and defended: FWER by a resampling method that bootstraps the actual dependence among

- the test statistics (Romano-Wolf stepdown, Westfall-Young maxT), uniformly at least as

- powerful as Holm and equal to it only under independence. Where resampling is impractical,

- Holm. Never plain Bonferroni: Holm step-down dominates it at zero cost under no extra

- assumptions, so Bonferroni is never the right answer to a question Holm also answers. ACROSS

- STAGES of a staged design: fixed-sequence gatekeeping. Preregister the order, test each

- stage's primary hypothesis at full alpha, stop at the first failure. It costs no alpha, and

- the price accepted in advance is that nothing downstream of a failed gate is confirmatory.

- Worked instantiations: sae (screens over a latent dictionary), field-experiment (subgroups

- and multiple outcomes), conjoint (AMCE families).

- - 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.

- - Text-role warnings at handoff (Feder): as confounder, ignorability over text aspects is

- untestable, argue it from domain knowledge, and audit positivity (a representation that

- nearly encodes the treatment leaves no counterfactual); as outcome or discovered

- treatment, never train the measurement function on the estimation sample (split-sample,

- via Egami; the authoritative rule lives in causal-unstructured); as treatment,

- disentangle the named aspect from correlated aspects, and random assignment of texts

- leaves reader-side confounding. Any machine-coded variable in any design gets the PPI

- rectifier logic before it enters a regression (causal-unstructured). One revision the

- family makes to Feder: his supervised text-as-confounder route (fine-tuned causally

- sufficient embeddings, Veitch 2020) is superseded; the GPI results say never fit the

- inference-time propensity on a representation learned with a treatment-prediction loss

- (on GPI's own simulation evidence; causal-unstructured carries the dispute and owns the

- replacement).

- - 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. causal-unstructured's

- note that Fong-Grimmer treatment discovery is not mediation remains authoritative there.

+ - Estimand first, with the subpopulation named: complier, ATT, or overlap population.

+ - Cluster where treatment was assigned or the sample was drawn, and say which of the two.

+ - Multiplicity staged by cost: FDR to screen, resampling FWER to confirm, gatekeeping by stage.

+ - Interference routes to field-experiment by structure: clustered, network, or marketplace.

+ - Surrogate index for long-run outcomes, valid only if every causal path runs through it.

+ - Text-role warnings at handoff (Feder). Machine-coded variables get PPI first.

+ - Mediation has no route here. Sequential ignorability is a regime no skill carries.

+ Full argument: references/shared-rules.md.

## 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.

- conjoint: profile experiments with multiple randomized attributes (AMCEs, marginal

means, measurement-error and multiple-testing corrections, HB partworths and WTP).

- did: many treated units with timing variation; parallel-trends machinery; it sends

plain-FE cases with no comparison group back to the plain panel fixed effects section.

- 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, leniency and examiner designs;

weak-instrument inference.

- - causal-unstructured: any text/image/audio/video role in the graph; PPI for machine-coded

- variables; GPI for internal-state adjustment; the split-sample rule.

- - sae: unknown-concept discovery in text; model-internals measurement instruments.

- - steering: activation-steering practice for steered stimuli and model-respondents

- (instrument choice, strength calibration, damage audits); the surrounding design stays

- with the owning method skill.

+ - Any text, image, audio, or video role in the graph carries a measurement design of its own:

+ a prediction-powered correction for machine-coded variables, an internal-state adjustment

+ where the confounder is latent, and the split-sample rule throughout.

+ - Unknown-concept discovery and model-internals measurement are instruments, and their

+ validity is argued before they enter a design.

+ - Activation steering for stimuli and model-respondents (instrument choice, strength

+ calibration, damage audits) is instrument practice; the surrounding design stays with the

+ owning method skill.

- preregister: pre-analysis plans once the design is chosen (experiment-first skill;

quasi-experimental and measurement PAPs adapt its structure).