foundations-causal-inference

name	foundations-causal-inference
description	Causal-inference primitives: DAGs, IV, RDD, DiD, synthetic control, propensity, CATE, interference. Use when attributing confounded impact or rollout and LLM-eval confounding.

Causal Inference Foundations

12 applied causal inference primitives for impact attribution and experiment design, backed by a formal theory map. Each primitive solves a specific identification or estimation problem. Primitives are domain-agnostic: the same instrumental-variable logic that handles omitted-variable bias in econometrics handles it in product analytics; the same difference-in-differences framework that evaluates policy interventions evaluates feature rollouts.

When to Apply

Apply causal-inference when:

• "Did the change cause the outcome, or just correlate?" question
• A/B test is impossible (rollout already happened, ethics, ramping risk) — observational methods needed
• Confounding suspected — non-random treatment assignment
• Heterogeneous treatment effects matter (CATE, uplift)
• Mediation question — "is the effect through path X or path Y?"
• Units interfere — marketplace, social graph, shared inventory, ranking model, or agents sharing a backend resource; randomization alone does not identify the launch effect
• LLM evaluation pipeline uses logged data — prompt distribution, judge bias, or user self-selection confound the quality signal (Pearl's Ladder applies: estimating P(Y|do(prompt)) is different from P(Y|prompt))

Skip and use simpler alternatives when:

• Clean RCT / A/B test is already running and units do not interfere — read the result, don't re-derive it observationally. If units share a marketplace, graph, or backend resource, the test is not clean: see Interference and SUTVA
• Question is "how big is the effect?" rather than "does it cause" — descriptive analytics is enough
• No plausible causal mechanism — correlation is just measurement, not insight
• Sample size too small for propensity overlap (n < 1000 typical) — flag and collect more data
• E-value < 1.5 from sensitivity analysis — claim is fragile; do not ship as causal
• Question is about strategic interaction (multi-actor) — use foundations-game-theory

Contents

• Quick Reference
• Primitive Index
• Formal Supporting Theory
• Anti-Patterns
• Misuse Boundaries
• Decision Checklist
• Composition Recipes
• Interference and SUTVA
• Expert Judgment
• Workflow
• ASCII Flow
• Related Skills
• Navigation
• Fact-Checking

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Quick Reference

#	Primitive	Use When	Core Output
1	DAGs and Structural Causal Models	Mapping assumed data-generating process	Causal graph; identifies confounders, mediators, colliders
2	Do-Calculus	Identifying causal effects from observational data	Identifiability check; expression for P(Y|do(X))
3	Backdoor / Frontdoor Criterion	Choosing a valid adjustment set	Minimal sufficient adjustment set
4	Instrumental Variables	Unobserved confounders present; randomized experiment infeasible	LATE or ATE estimate
5	Regression Discontinuity	Treatment assigned by a threshold rule	Local ATE at the cutoff
6	Difference-in-Differences	Pre/post data with treated and control groups	ATT under parallel trends
7	Synthetic Control	Single treated unit; no clean control group	Counterfactual trajectory for the treated unit
8	Propensity Score Methods	Observational data; balancing covariates needed	ATE or ATT via matching, IPW, or DR estimation (for continuous treatment: dose-response curve via DML)
9	CATE / Uplift Modeling	Heterogeneous treatment effects across subgroups	Individual or subgroup CATE; uplift scores
10	Simpson's Paradox and Confounding Traps	Observed aggregated trend contradicts subgroup trends	Correct stratification; DAG-based decomposition
11	Mediation Analysis	Decomposing total effect into direct + indirect paths	NDE, NIE, proportion mediated
12	Sensitivity Analysis	Assessing robustness of conclusions to unobserved confounding

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Primitive Index

Each primitive is summarized here, expanded in references/primitives-overview.md, and covered by standalone playbooks under assets/templates/causal-inference/. Use references/formal-theory-map.md when the task needs identification assumptions, estimand distinctions, or design boundaries.

#	Primitive	Failure Mode It Addresses
1	DAGs and Structural Causal Models	Implicit untested causal assumptions producing biased estimates
2	Do-Calculus	Treating observational P(Y|X) as causal without identification
3	Backdoor / Frontdoor Criterion	Conditioning on the wrong variables; collider bias
4	Instrumental Variables	Omitted-variable bias when confounders are unobservable
5	Regression Discontinuity	Selection bias in threshold-based assignment
6	Difference-in-Differences	Pre-existing trends misattributed as treatment effects
7	Synthetic Control	No valid control group for single treated unit
8	Propensity Score Methods	Covariate imbalance inflating treatment effect estimates
9	CATE / Uplift Modeling	ATE masking heterogeneous subgroup effects
10	Simpson's Paradox and Confounding Traps	Aggregation reversals; conditioning on colliders
11	Mediation Analysis	Treating total effect as direct; pathway blocked by conditioning
12	Sensitivity Analysis	Conclusions that collapse under modest unobserved confounding

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Formal Supporting Theory

Theory Area	Use When	Applied Primitives It Grounds
Structural causal models	Need graphs, do-operator, counterfactuals, or transportability	#1, #2, #3, #10
Potential outcomes	Need estimands, SUTVA, ignorability, compliance, or randomization logic	#4, #5, #6, #8, #9
Identification theory	Need to know whether the causal effect is learnable from data	#2, #3, #4, #11
Quasi-experimental design	Need threshold, timing, or donor-pool identification	#5, #6, #7
Observational adjustment	Need propensity scores, weighting, matching, doubly robust estimation	#3, #8
Heterogeneous effects	Need CATE, uplift, policy learning, or subgroup effect estimates	#9
Mediation/counterfactual pathways	Need direct/indirect effects and pathway assumptions	#11
Interference / experimental design	Need cluster, geo, or switchback randomization because units affect each other	All — SUTVA is a precondition
Robustness/sensitivity	Need unobserved-confounding bounds or tipping-point analysis	#12

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Anti-Patterns

Anti-Pattern	Causal Diagnosis	Fix
Conditioning on a collider	Opens a spurious association path; introduces bias where none existed	Draw the DAG (#1); block conditioning on non-confounders identified by backdoor criterion (#3)
Using P(Y|X) as a causal estimate without identification	Confounders in the distribution invalidate effect direction, let alone magnitude	Apply do-calculus (#2) to check identifiability before any regression
Parallel-trends violation in DiD	Pre-treatment trends differ; the control group is not a valid counterfactual	Test pre-trends explicitly; consider synthetic control (#7) as a drop-in replacement
Weak-instrument bias	IV estimate amplifies noise when the instrument is weakly correlated with treatment; collapses to OLS bias in small samples	Check first-stage F > 10; use LIML or Anderson-Rubin confidence sets (#4)
Propensity-score overlap failure	Extreme propensity scores (near 0 or 1) produce unstable IPW weights; effective sample collapses	Check overlap; trim or clip weights; switch to DR estimator or matching (#8)
Conditioning on a post-treatment variable	Blocks the causal pathway; introduces collider bias on mediator or mediator-proxy	Identify mediators in the DAG before adjusting; use mediation analysis (#11) if the path is the target
Averaging heterogeneous effects into one ATE	Subgroups with opposing effects cancel; action on ATE harms some users	Run CATE/uplift (#9); segment before averaging
Ignoring unmeasured confounding in observational studies	Effect estimate is unidentified; direction may flip under plausible confounders	Report E-value and Rosenbaum bounds (#12) alongside every observational point estimate. For IV estimates, also compute IV robustness values (Cinelli & Hazlett 2025, Biometrika)
Treating a marketplace or social-graph A/B test as unit-randomized	SUTVA fails: treated units change control units' outcomes, so the difference-in-means is biased even under perfect randomization	Name the interference structure before estimating. Cluster or switchback the design; estimate with a bias-aware estimator rather than difference-in-means

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Misuse Boundaries

Misuse	Why It Is Wrong	Required Correction
Treating correlation or prediction as causal effect	Association does not identify intervention effects	State estimand and identification strategy
Drawing a DAG after seeing results	Post-hoc graphs encode the desired conclusion	Draw assumptions before modeling
Adjusting for every available variable	Colliders and mediators can introduce bias	Use DAG/backdoor criteria
Reporting DiD without pre-trend diagnostics	Parallel trends is the core identifying assumption	Show pre-trends, event study, or use synthetic control
Using weak IVs	Weak instruments amplify bias and uncertainty	Report first-stage strength and robust intervals
Publishing CATE without overlap checks	Heterogeneous effects extrapolate outside support	Check positivity and subgroup sample size
Calling observational estimates “proven impact”	Unmeasured confounding remains possible	Report sensitivity analysis
Conditioning on post-treatment variables	Blocks or distorts the causal path	Separate total, direct, and mediated effects
Reporting a unit-level A/B result as the launch effect under interference	Unit-level and global treatment effects differ when SUTVA fails	Name the interference structure; use a cluster/geo/switchback design and say which estimand it targets

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Decision Checklist

Use this to pick the right method before modeling:

• Can you draw the assumed DAG? If not, stop — assumptions are implicit and untestable. Draw DAG (#1) first.
• Is the effect you want interventional (do(X)) or conditional? If interventional, check identifiability with do-calculus (#2).
• Can one unit's treatment change another unit's outcome? (marketplace supply/demand, social graph, shared inventory, ranking model, geographic proximity) If yes, SUTVA fails and randomization alone does not save you — fix the design (cluster, geo, or switchback) before choosing an estimator. See Interference and SUTVA.
• Do you have an RCT or clean natural experiment? If yes, use the design directly. If no, continue.
• Is there a threshold that determines treatment? → RDD (#5).
• Is there pre/post data with a comparable untreated group? → DiD (#6). Check parallel trends first.
  • Is treatment staggered (units adopt at different times)? → Use Callaway–Sant'Anna, Sun–Abraham, BJS imputation, or Gardner 2-stage (see primitives-overview Primitive 6). Do NOT use plain TWFE — negative-weight bias.
  • Is parallel trends uncertain? → Apply HonestDiD (Rambachan & Roth 2023) for honest CIs under bounded violations.
• Pre/post data with donor pool but parallel trends uncertain? → Synthetic DiD (Arkhangelsky et al. 2021, #7 extension). Bridges SC and DiD.
• Single treated unit with no clean control? → Synthetic control (#7).
• Are there unobserved confounders and a valid instrument? → IV (#4). Validate exclusion restriction and check first-stage F.
• Observational data with measured confounders only? → Propensity score matching / IPW / DR (#8). Check overlap.
• Do you need individual-level or subgroup effect estimates? → CATE / uplift (#9). Choose meta-learner by sample size.

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Composition Recipes

Uplift from Observational Data

Objective: estimate individual-level treatment effects without an RCT.

Stack:

1. DAG (#1) — draw the assumed data-generating process; identify confounders.
2. Propensity score + doubly robust estimator (#8) — balance covariates; produce unbiased ATE. When treatment is continuous (dosage, spend, exposure level), use kernel-based DML for the average dose-response function — Colangelo & Lee (2025, JBES).
3. CATE / X-learner (#9) — estimate heterogeneous effects using the debiased residuals.
4. Sensitivity analysis (#12) — compute E-value for the strongest subgroup claim. For DML/doubly robust pipelines, additionally apply OVB bounds via Chernozhukov et al. (2026, REStat) to assess robustness of the ATE claim.

Worked example: 50 k users; 15 k treated by a 20%-off discount (self-selected). Propensity model (logistic, 12 covariates) yields p̂ ∈ [0.05, 0.95] for 91% of treated — overlap is acceptable; 9% trimmed. DR-ATE = +$2.40/user (SE $0.31, 95% CI [$1.79, $3.01]). X-learner surfaces a high-value segment (top quintile by LTV) with CATE = +$4.10 (SE $0.52). E-value for the overall ATE = 2.8 — an unobserved confounder would need to ~2.8× both the treatment-odds and the outcome-odds to fully nullify the estimate. Benchmark: E-value < 2 → don't ship without an RCT; E-value ≥ 3 → actionable with documented assumptions.

When to add IV (#4): a valid instrument exists (e.g., randomized discount assignment, geographic variation); use it instead of propensity methods for the first-stage.

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Policy Evaluation with No Control Group

Objective: estimate the impact of a policy or feature applied to a single market or cohort.

Stack:

1. DAG (#1) — map treatment, outcomes, and potential confounders over time.
2. Synthetic control (#7) — construct a weighted donor pool to serve as the counterfactual.
3. DiD robustness check (#6) — apply DiD on the synthetic control residual to quantify pre-trend fit.
4. Sensitivity analysis (#12) — Rosenbaum bounds on the placebo distribution from donor permutations.

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Mechanism Attribution (Why Did the Effect Happen?)

Objective: decompose a total causal effect into direct and indirect (mediated) components.

Stack:

1. DAG (#1) — identify the mediator path; confirm no unmeasured exposure-mediator confounders.
2. Backdoor criterion (#3) — determine the adjustment set for total effect identification.
3. Propensity / DR estimator (#8) — produce balanced outcome estimates for mediation.
4. Mediation analysis (#11) — decompose NDE and NIE; report proportion mediated.
5. Sensitivity analysis (#12) — E-value for the indirect effect claim.

LLM Evaluation Pipeline — Deconfounding the Quality Signal

Objective: estimate the causal effect of a prompt change, model update, or RLHF policy on output quality, when evaluation data are logged (non-randomised) and judge scores are potentially biased.

Context: LLM development pipelines generate observational logs. User prompt distribution, conversation history, judge LLM identity, and user self-selection all confound quality metrics. Simply comparing average scores before and after a model update conflates the treatment effect with distributional shift. (Reference: arxiv 2605.25998, "Causal Methods for LLM Development and Evaluation", May 2026.)

Stack:

1. DAG (#1) — draw: Prompt → LLM_response → Quality_score; annotate confounders (prompt difficulty, user type, judge identity) and potential colliders (filtered output).
2. Do-calculus / backdoor (#2, #3) — check whether P(Quality | do(model_update)) is identified given available logs; identify the minimal adjustment set.
3. Propensity / DR estimator (#8) — balance on prompt covariates and user context; use doubly robust ATE. For continuous interventions (e.g., RLHF reward weight), use kernel-based DML (Colangelo & Lee 2025).
4. CATE (#9) — surface heterogeneous effects by prompt category, task type, or user cohort; avoid reporting a flat ATE that masks regressions in a subgroup.
5. Sensitivity analysis (#12) — compute E-value on the key quality claim; judge-bias is a plausible unmeasured confounder — report how strong it would need to be to nullify the finding.

Note on LLM-assisted causal discovery: LLMs can propose DAG edges from domain knowledge but cannot replace data-driven identification checks — autoregressive next-token modeling has no mechanism for establishing direction. Use LLM outputs as priors to seed a DAG; validate edges with statistical tests (faithfulness, independence). Do not treat LLM-generated graphs as identified causal models. The restriction is on decisional authority, not on all LLM involvement: LLM-guided heuristic search over the structure space is a legitimate accelerator, since the search result is still validated against data. Reported LLM causal-discovery accuracy is separately confounded by memorization: the standard bnlearn benchmark graphs (Sachs, Asia, Alarm, Child) are widely published and plausibly in pretraining corpora, so benchmark scores are weak evidence of causal reasoning — prefer a graph your own domain generated. (Wu, Yu, Wu & Tan 2025, arXiv:2506.00844; contamination caveat per CausalBench, arXiv:2404.06349.)

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Interference and SUTVA: When Randomization Is Not Enough

Every primitive above assumes SUTVA: one unit's treatment does not affect another unit's outcome. In marketplaces, social graphs, shared-inventory systems, and ranking models this is false by construction, and a clean randomized A/B test is still biased — the control group is contaminated by the treatment. This is a design problem; no estimator applied afterwards recovers the estimand.

Identify the interference structure first, then pick the design:

Interference structure	Design	Estimation note
Spatial or graph neighbors (social, geo, ride-hailing)	Cluster randomization on the graph's dense components	Difference-in-neighbors (Peng, Ye & Zheng 2025) attains second-order bias in interference magnitude with far lower variance than Horvitz–Thompson
Temporal carryover on a single shared system (pricing, matching, ranking)	Switchback: randomize treatment over time blocks	Block length must exceed the carryover order m; optimal design in Bojinov, Simchi-Levi & Zhao (2023, Management Science)
Both spatial and temporal (delivery, marketplace supply)	Clustered switchback (Jia, Kallus & Yu 2025)	Truncated Horvitz–Thompson; MSE matches the lower bound up to log terms on sparse graphs
Market-level equilibrium effects (budget, inventory, auction)	Geo or market-level randomization; unit-level tests cannot see it	Few treated units — use randomization inference, not asymptotic SEs

The reporting distinction that matters: under interference, the unit-level "treatment effect" and the effect of switching everyone (the global/total treatment effect) are different quantities. A cluster or switchback design estimates the latter, which is usually the decision-relevant one for a launch. Say which one you estimated.

Agent and LLM products hit this directly: agents sharing a rate limit, a retrieval index, a cache, or a tool backend interfere through the shared resource, so per-session randomization understates or inverts the launch effect.

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Expert Judgment

What separates an expert from a checklist-follower is not knowing more formulas — it is reading the shape of the data before picking a formula, and knowing which textbook assumption is the one that actually breaks.

Picking an Identification Strategy From Data Shape

• One treated unit, a time series, and a pool of comparable untreated units → synthetic control or synthetic DiD, not a hand-picked comparison unit. If pre-treatment fit is poor, say so and stop rather than force it.
• A rule with a hard numeric cutoff and enough density of units near it → RDD, not a linear control for the running variable. If the running variable is coarse (rounded scores, integer ages), check for heaping before trusting continuity.
• Treatment rolled out at different times across units → check whether never-treated or not-yet-treated units exist, then use a heterogeneity-robust staggered-DiD estimator (Callaway–Sant'Anna, Sun–Abraham, BJS, or Gardner). Plain TWFE is a bug, not a baseline, once adoption is staggered and effects can vary by cohort.
• Confounders you can name and measure completely, with common support across treated/control → propensity/DR. If you cannot name the confounders, no amount of covariate adjustment substitutes for a design — look for a natural experiment (IV, RDD) instead.
• An exogenous shock or rule that shifts treatment for some units and not others, for a reason unrelated to the outcome → IV, but only if the exclusion story survives being explained to a skeptical colleague in one sentence. If the one-sentence version needs three caveats, the instrument is probably not clean.
• The real question is "who benefits," not "what's the average effect" → CATE/uplift layered on top of an already-validated ATE/ATT, never as a substitute for identification. A confounded CATE just reports which subgroup has the most confounding.

The Assumption That Actually Fails in Practice

The textbook assumption is rarely violated the way the textbook describes it. What experts actually watch for:

Method	Textbook assumption	What breaks in real data
DiD	Parallel trends	Treated units were selected because they were already diverging (mean reversion, selection on trend) — pre-trend tests have low statistical power, so a "flat" pre-trend plot is weak evidence, not proof (Roth 2022)
IV	Exclusion restriction	The instrument is excludable in theory but leaks through an unmodeled common shock (e.g., a policy or cohort effect correlated with both the instrument and unobserved confounders)
RDD	Continuity / no manipulation	The running variable is granular (rounded, integer, self-reported) — heaping at the cutoff looks like a density blip, not manipulation, and the McCrary test at one bandwidth can miss it
Synthetic control	Good pre-treatment fit	Low aggregate RMSPE is achieved by 2–3 donors carrying nearly all the weight (interpolation bias) — inspect the weight vector itself, not just RMSPE
Propensity / DR	Strong ignorability (all confounders measured)	Treatment was assigned by a human or algorithm using private information not in X (a manager's judgment, a salesperson's read on the customer) — balance tables on measured covariates cannot detect this, and it is the single most common real-world failure
CATE / uplift	Same ignorability as ATE, per subgroup	Overlap can fail in exactly the subgroup with the highest estimated CATE; the "best segment" is often the one with the least support and the most confounding, not the most persuadable one
Mediation	No exposure-induced mediator-outcome confounder	Almost always violated when the mediator is a downstream behavior nobody randomized — default to reporting the total effect with a caveat instead of NDE/NIE unless both stages are experimental

Placebo and Robustness Checks an Expert Always Runs

• Placebo-in-time: rerun the design as if treatment happened one period earlier; expect a null effect.
• Placebo-in-space / placebo-outcome: rerun on units or outcomes the treatment should not affect.
• Leave-one-out: drop the highest-weight synthetic-control donor, or the strongest component of a composite instrument, and confirm the estimate does not collapse.
• Specification / bandwidth curve: show the estimate across a range of RDD bandwidths or DiD control sets, not just the one preferred specification.
• Randomization inference: use permutation p-values instead of asymptotic SEs when clusters or treated units are few (a handful of treated states or markets).
• Sensitivity analysis as a routine output, not an appendix: E-value, Rosenbaum bounds, or HonestDiD accompany every observational or DiD point estimate, not just the ones that look fragile.

When Causal ML Adds Nothing Over a Good Quasi-Experiment

• If a credible design already exists (valid IV, sharp RDD, staggered DiD with a heterogeneity-robust estimator) and the target is a single ATE/ATT/LATE, doubly-robust ML nuisance estimation buys efficiency, not identification. The design is doing the causal work; DML is just a better nuisance-function fitter.
• Causal ML (causal forests, DML, meta-learners) earns its complexity when: (a) covariates are high-dimensional with an unknown confounding functional form, (b) the question is heterogeneity (CATE/uplift) that a single quasi-experiment cannot answer without infeasible sample size, or (c) treatment is continuous/high-cardinality with no closed-form estimator.
• It does not repair a broken identification strategy. Running econml on top of a DiD with violated parallel trends, or a dowhy refutation suite on top of an IV with a leaky exclusion restriction, produces a precise, doubly-robust, wrong answer. Fix identification before reaching for machine learning.
• Where the literature is genuinely unsettled (state this plainly rather than picking a side): (1) which staggered-DiD estimator (Callaway–Sant'Anna, Sun–Abraham, BJS, Gardner) to prefer is setting-dependent, not resolved — the 2026 JEL practitioner's guide (Baker, Callaway, Cunningham, Goodman-Bacon & Sant'Anna) frames the choice by design and target estimand rather than naming a winner, and the estimators can disagree meaningfully on the same panel; (2) the best-practice sensitivity-analysis default for ML-based ATEs (Chernozhukov, Cinelli et al. 2026 vs. simpler partial-R² benchmarks) is still settling in applied practice; (3) using LLMs to propose or accelerate causal discovery has no consensus validation protocol as of mid-2026 — treat LLM-proposed edges as priors to test, not conclusions to report.

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Workflow

1. Identify the causal question: intervention effect, mechanism, or heterogeneous effect?
2. Draw the DAG (#1). Identify confounders, mediators, and colliders.
3. Use the Decision Checklist to select the identification strategy.
4. Open references/primitives-overview.md for inputs, assumptions, and worked conceptual examples. Its Tooling Landscape table maps each primitive to the maintained Python/R library that implements it.
5. For multi-method stacks, use the Composition Recipes above.
6. Check references/patterns-scenarios-traps.md and always close with sensitivity analysis (#12) when reporting observational estimates.

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ASCII Flow

Causal claim or impact question
  -> State intervention, outcome, unit, and estimand
  -> Draw DAG and mark confounders, mediators, colliders
  -> Select identification strategy
     +-- randomized evidence exists -> analyze experiment directly
     +-- observational only -> choose IV, RDD, DiD, synthetic control, or propensity design
  -> Estimate effect and run sensitivity analysis
  -> Report assumptions, effect, uncertainty, and fragility

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Related Skills

Wave 2 has landed. These consumer skills build applied-recipe layers on top of these primitives via their own references/causal-inference-applied.md (or domain-named equivalent) files. Each gates on this skill's When to Apply before invoking:

• ../marketing-cro/references/causal-inference-applied.md and causal-inference-experimentation.md — CUPED, switchback and geo-experiments, CATE for personalization
• ../marketing-product-analytics/references/causal-inference-applied.md and causal-inference-analytics.md — funnel and retention attribution
• ../marketing-paid-advertising/references/causal-inference-applied.md — media-mix and geo-lift attribution
• ../marketing-email-automation/references/causal-inference-applied.md — send-time and lifecycle-campaign lift
• ../data-analytics-engineering/references/causal-inference-applied.md — metric-layer causal contracts
• ../product-management/references/causal-inference-applied.md — feature-rollout impact
• ../startup-business-models/references/causal-inference-applied.md — pricing and monetization lift
• ../qa-debugging/references/causal-inference-applied.md — regression root-cause attribution

New consumer domain layers should follow the same gate-then-recipe pattern rather than duplicating the primitives themselves.

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Navigation

• Formal theory map: references/formal-theory-map.md
• Patterns, scenarios, and traps: references/patterns-scenarios-traps.md
• Full primitives overview with TOC: references/primitives-overview.md
• Per-primitive playbooks: assets/templates/causal-inference/README.md
• Sources: data/sources.json

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Fact-Checking

• Pearl (2009) Causality is the canonical source for DAGs, do-calculus, and the backdoor/frontdoor criteria. Verify structural claims against that text.
• Imbens & Rubin (2015) Causal Inference for Statistics, Social, and Biomedical Sciences is the canonical source for potential-outcomes framework, IV, and matching.
• Angrist & Pischke (2009) Mostly Harmless Econometrics covers IV, RDD, and DiD in applied settings; use for identification assumption checks.
• Athey & Imbens (2017) machine-learning–based CATE estimation is the source for meta-learner claims; verify heterogeneous-effect benchmarks against that paper.
• Hernán & Robins What If (2020, freely available) is the canonical reference for time-varying treatments, IPW, and marginal structural models.
• Chernozhukov et al. (2018) on double/debiased machine learning (DML) is the source for doubly robust and Neyman-orthogonal estimator claims. For continuous treatments, the DML extension is Colangelo & Lee (2025, Journal of Business & Economic Statistics, doi:10.1080/07350015.2025.2505487). For omitted-variable sensitivity analysis of DML estimates, see Chernozhukov, Cinelli et al. (2026, Review of Economics and Statistics, doi:10.1162/REST.a.1705). Implemented in dml.sensemakr.
• Sensitivity analysis E-values: VanderWeele & Ding (2017); Rosenbaum bounds: Rosenbaum (2002) Observational Studies. Sensitivity analysis for IV estimates: Cinelli & Hazlett (2025, Biometrika, doi:10.1093/biomet/asaf004) extends the partial-R² OVB framework to handle exclusion-restriction violations and instrument confounding. Implemented in iv.sensemakr R package.
• For staggered DiD, the canonical method set (as of 2026) is: Callaway & Sant'Anna (2021, JoE, doi:10.1016/j.jeconom.2020.12.001); Sun & Abraham (2021, JoE, doi:10.1016/j.jeconom.2020.09.006); Borusyak, Jaravel & Spiess (2024, RES, doi:10.1093/restud/rhae011) imputation estimator; Gardner (2022, arXiv:2207.05943) two-stage DiD. Goodman-Bacon (2021, JoE, doi:10.1016/j.jeconom.2021.03.014) decomposition explains why plain TWFE fails. Navigational synthesis: Roth, Sant'Anna, Bilinski & Poe (2023, JoE, doi:10.1016/j.jeconom.2022.11.001). The current practitioner-facing reference is Baker, Callaway, Cunningham, Goodman-Bacon & Sant'Anna (2026, JEL 64(2), 498–557, doi:10.1257/jel.20251650) — organizes DiD designs by estimand, covariates, weights, and timing rather than prescribing one estimator.
• For parallel-trends robustness: Rambachan & Roth (2023, RES, doi:10.1093/restud/rhad018) HonestDiD. Pre-trend tests have low power; HonestDiD provides honest CIs under bounded violations without the binary pass/fail logic.
• For Synthetic DiD (bridging SC and DiD): Arkhangelsky et al. (2021, , doi:10.1257/aer.20190159). R package .

Learnings Loop

Before applying this skill on a non-trivial task, read learnings.consolidated.md in this directory (and learnings.md if present).

After applying it, if you encountered a pattern worth remembering, a mistake worth preventing, or a domain fact that surprised you, append one dated bullet to learnings.md via agents-skills-feedback-loop/scripts/append_learning.py. Do not modify SKILL.md itself.