Causal Inference Foundations

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))
• A new router, ranker or bandit policy must be judged from logs of the old one, a short test must decide on a long-term metric, or outcomes are missing unequally by arm — see Beyond the canonical 12

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 requests an associational summary only — descriptive analytics is enough. The magnitude of a causal effect still requires identification
• No plausible causal mechanism — correlation is just measurement, not insight
• Effective sample size or treatment overlap is inadequate for the target estimand — narrow the population, change the design, or collect more data
• Sensitivity analysis shows that a substantively plausible omitted confounder could reverse the decision — qualify the claim or use a stronger design
• Question is about choosing an action under uncertainty rather than estimating an effect — use foundations-decision-theory; for test sizing and intervals, foundations-statistical-inference
• Question is about strategic interaction (multi-actor) — use foundations-game-theory

Quick Reference: Primitives

Each primitive has a playbook under assets/templates/causal-inference/. Use references/formal-theory-map.md for the theory area (SCM, potential outcomes, identification, quasi-experiments) that grounds each one.

#	Primitive	Use When	Failure Mode It Addresses	Core Output
1	DAGs and Structural Causal Models	Mapping assumed data-generating process	Implicit untested causal assumptions	Causal graph; confounders, mediators, colliders
2	Do-Calculus	Identifying causal effects from observational data	Treating P(Y|X) as causal without identification	Identifiability check; expression for P(Y|do(X))
3	Backdoor / Frontdoor Criterion	Choosing a valid adjustment set	Conditioning on the wrong variables; collider bias	Minimal sufficient adjustment set
4	Instrumental Variables	Unobserved confounders; a valid instrument exists	Omitted-variable bias	LATE for compliers
5	Regression Discontinuity	Treatment assigned by a threshold rule	Selection bias in threshold assignment	Local effect at the cutoff
6	Difference-in-Differences	Pre/post data with treated and comparison groups	Pre-existing trends misattributed as effects	ATT under parallel trends
7	Synthetic Control (and SDiD)	One or few treated units, a donor pool	No valid single control unit	Counterfactual trajectory
8	Propensity Score Methods	Measured confounders only	Covariate imbalance	ATE/ATT via matching, IPW or DR; dose-response via DML for continuous treatment
9	CATE / Uplift Modeling	Heterogeneous effects matter	ATE masking opposing subgroup effects	Subgroup CATE; uplift scores
10	Simpson's Paradox and Confounding Traps	Aggregate trend contradicts subgroups	Aggregation reversals; collider conditioning	Correct stratification
11	Mediation Analysis	Decomposing direct and indirect paths	Total effect treated as direct	NDE, NIE, proportion mediated
12	Sensitivity Analysis	Robustness to unobserved confounding	Conclusions that collapse under modest hidden bias	Scale-compatible sensitivity (partial-R²/OVB, E-value for risk ratios, Rosenbaum Γ, HonestDiD)

Designs outside these 12 — interrupted time series, off-policy evaluation, surrogate index, Manski/Lee bounds, negative controls and proximal inference — are in references/beyond-canonical-designs.md.

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Anti-Patterns and Misuse

Anti-Pattern	Causal Diagnosis	Fix
Treating correlation, prediction or P(Y|X) as a causal effect	Confounders invalidate effect direction, let alone magnitude	State the estimand; check identifiability (#2) before any regression
Drawing a DAG after seeing results, or adjusting for every available variable	Post-hoc graphs encode the desired conclusion; colliders and mediators add bias	Draw the DAG (#1) before modeling; use the backdoor adjustment set (#3)
Conditioning on a post-treatment variable	Blocks the causal path; collider bias on mediator proxies	Identify mediators in the DAG; use mediation analysis (#11) if the path is the target
Parallel-trends violation in DiD, or a passed pretest read as proof	Pre-trend tests have low power; the control group may not be a valid counterfactual	Report pretrends with uncertainty and bounded-trend sensitivity (HonestDiD), not a pass/fail gate; synthetic control (#7) is a different design with its own assumptions, not a drop-in repair
Weak instrument accepted on a first-stage F > 10	With one instrument, a true 5% t-test needs F > 104.7; at F = 10 the valid critical value is 3.43, not 1.96 (Lee, McCrary, Moreira & Porter, AER 2022)	One instrument: report Anderson–Rubin intervals or tF-adjusted inference. Several instruments: report the effective F (Montiel Olea & Pflueger 2013) with weak-IV-robust (AR-type) inference; do not extend the 104.7 threshold beyond one instrument (#4)
Propensity-score overlap failure	Extreme propensities give unstable weights; effective sample collapses	Distinguish numerical tails from structural non-overlap; restrict and disclose the target estimand. Clipping, DR and matching do not identify absent counterfactuals (#8)
Averaging heterogeneous effects, or publishing CATE without overlap checks	Opposing subgroups cancel; CATE extrapolates outside support	Run CATE/uplift (#9) on an identified ATE; check positivity and subgroup N
Calling an observational estimate "proven impact"	Unmeasured confounding remains possible	Choose sensitivity for the effect scale: E-values for risk ratios (or explicitly justified conversions), Rosenbaum bounds for matched designs, partial-R²/OVB for continuous outcomes; for IV, IV robustness values (Cinelli & Hazlett 2025) (#12)
Reporting a unit-randomized marketplace or shared-backend test as the launch effect	Interference changes the identified contrast even under perfect randomization	Name the exposure mapping, assignment support and target contrast; cluster/switchback designs are options, not automatic identification of a global effect

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Decision Checklist

Use this to pick the right method before modeling:

• Can you state the assumed data-generating process? For adjustment-based methods (matching, IPW, DR, CATE), draw the DAG (#1) first; if you cannot, stop, because assumptions are implicit and untestable. Design-based methods (RDD, DiD, randomized rollouts) rest on stated design assumptions, and a DAG is optional there.
• 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, specify direct, indirect, total or global estimand, exposure mapping and assignment support before choosing an estimator; redesign only when current support/assumptions do not identify the target. See Interference and SUTVA.
• Do you have an RCT or clean natural experiment? If yes, use the design directly. If outcomes are missing unequally by arm (attrition, timeouts), use Lee bounds (beyond-canonical-designs). If the decision metric arrives long after the test, consider a validated surrogate index. If no, continue.
• Is there a threshold that determines treatment? → RDD (#5). Report the robust bias-corrected interval, not the conventional one.
• 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. Use a heterogeneity-robust estimator aligned with the target ATT; dynamic effects can contaminate TWFE comparisons.
  • Is the treatment a continuous dose? → Continuous-treatment DiD (Callaway, Goodman-Bacon & Sant'Anna); parallel trends alone does not make comparisons across doses causal.
  • 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).
• Single treated unit with no clean control? → Synthetic control (#7). No donor units at all, only one series? → Interrupted time series / BSTS, the weakest design here (beyond-canonical-designs).
• Are there unobserved confounders and a valid instrument? → IV (#4). Validate exclusion; use weak-IV-robust inference (AR or tF for one instrument), not an F > 10 gate. Use the heteroskedasticity-robust F when errors are not homoskedastic. An unbounded AR set means the data are uninformative about the effect, not a software failure.
• Observational data with measured confounders only? → Propensity score matching / IPW / DR (#8). Check overlap. If a known confounder is unmeasured, test with negative controls first.
• Is the "treatment" a new decision policy evaluated on logs of the old policy? → Off-policy evaluation; propensities must be logged (beyond-canonical-designs).
• Do you need conditional average effects for covariate-defined groups? → CATE / uplift (#9). Choose meta-learner by sample size.
• Does the aggregate trend contradict subgroup evidence? → Check for Simpson's paradox via DAG stratification (#10).
• Is the total effect mediated by an intermediate variable? → Mediation analysis (#11). Requires treatment and mediator exchangeability, consistency and positivity; natural effects also require no exposure-induced mediator–outcome confounding.
• Is the conclusion actionable under unobserved confounding? → Select a design- and scale-compatible sensitivity method (#12), name plausible confounders, and report it. If point identification fails, report bounds instead.
• Before writing any number. Verify every citation against a primary source before writing it; data/sources.json is the canonical citation list — do not restate it here. Never invent a coefficient, p-value, or weight; re-derive worked examples and hedge or omit what you cannot verify.

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Composition Recipes

Multi-method stacks for common scenarios; full stacks, worked examples and caveats are in references/composition-recipes.md.

Recipe	Use When	Key Stack
Uplift from Observational Data	Conditional average effects, no RCT	DAG (#1) → propensity/DR, DML for continuous treatment (#8) → CATE/X-learner (#9) → sensitivity (#12); add IV (#4) if a valid instrument exists
Policy Evaluation with No Control Group	Single market/cohort, no comparison group	DAG (#1) → synthetic control with donors and donor/pre-fit checks; if no donors, ITS/BSTS with time-series sensitivity (#7, #12)
Mechanism Attribution	Decompose direct vs indirect (mediated) effect	DAG (#1) → backdoor adjustment (#3) → propensity/DR (#8) → mediation analysis (#11) → sensitivity (#12)
LLM Evaluation Pipeline	Deconfound a logged, judge-scored quality signal for a prompt/model/RLHF change	DAG (#1) → do-calculus/backdoor (#2, #3) → DR (#8), or off-policy evaluation if the change is a per-request policy → CATE (#9) → sensitivity (#12). LLM-proposed DAG edges are priors to validate, not identified structure.

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Interference and SUTVA: When Randomization Is Not Enough

No-interference is part of SUTVA, which also concerns treatment versions. Many conventional unit-level formulas assume it, but DAGs/SCMs and potential-outcome models can explicitly include cross-unit causes. Interference does not make every estimand unrecoverable. Specify the exposure mapping, the direct/indirect/total/global intervention contrast, assignment probabilities and support, consistency of exposures, and remaining identification assumptions. Randomization alone does not turn a direct effect into the all-treated-versus-all-control launch effect.

Counterexample: independent Bernoulli(.5) assignments Z1,Z2 with Y1=3Z1+7Z2 and Y2=3Z2+7Z1 have interference. The Horvitz–Thompson direct-effect estimator averaging 2ZiYi−2(1−Zi)Yi over the two units has expectation 3 across the four equally likely assignments. The global all-treated-versus-all-control contrast is 10. Both contrasts exist; they answer different questions. Exposure-probability weighting requires positive probability for the exposures being contrasted. Aronow & Samii (2017), design/exposure/estimand framework.

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	Align schedule and estimator with carryover order m. Under its horizon assumptions, Bojinov et al., Theorem 3.7 permits interior epochs of length m
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. Cluster or switchback designs target contrasts defined by their allocation, carryover and exposure assumptions; neither automatically identifies the global rollout effect. Say which contrast was identified and justify any extrapolation.

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 can identify a different contrast and may understate or invert the launch effect; establish this for the actual resource/exposure model.

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Expert Judgment

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). Dynamic effects can contaminate TWFE comparisons; cohort heterogeneity alone does not imply negative weights or bias for every target.
• 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 a density 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	Sequential ignorability	Randomizing exposure alone does not establish mediator–outcome exchangeability. Defend mediation identification assumptions and report mediation-specific sensitivity; see Imai et al., pp. 309–313

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: a scale-compatible method (partial-R²/OVB, E-value for risk ratios, Rosenbaum bounds, or HonestDiD) accompanies 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. DoWhy placebo-treatment, random-common-cause and data-subset refuters test pipeline sanity and estimator stability inside the assumed DAG; they cannot detect a missing confounder. Only sensitivity analysis (#12) speaks to hidden confounding, so never present a passed refutation suite as evidence of none.
• 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 had no consensus validation protocol in the sources reviewed for this skill — treat LLM-proposed edges as priors to test, not conclusions to report.

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Workflow

1. State the intervention, outcome, unit and estimand: intervention effect, mechanism, heterogeneous effect, or policy value?
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 the decision map, estimand taxonomy, assumption inventory and Tooling Landscape; open the matching template for inputs, failure modes and a worked example.
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. For risk ratios, python3 scripts/evalue.py --rr RR --ci-low LOW --ci-high HIGH validates the interval and uses the confidence bound closest to the null.
7. Report assumptions, effect, uncertainty and fragility; on unidentified effects report an association, bounds, or "inconclusive".

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Related Skills

Consumer skills keep domain adapters in references/causal-inference-applied.md (or a domain-named equivalent). Each gates on this skill's When to Apply and links back here for theory:

• ../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
• ../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
• ../foundations-decision-theory/references/thresholds-stopping-and-ope.md — OPE estimators and acting on a policy-value estimate

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Navigation

• Designs beyond the 12 (ITS/BSTS, off-policy evaluation, surrogate index, bounds, negative controls/proximal) — read when the checklist lands outside the canonical primitives: references/beyond-canonical-designs.md
• Practical completion contract and known-answer controls: references/practical-contract.md
• Formal theory map: references/formal-theory-map.md
• Patterns, scenarios, and traps: references/patterns-scenarios-traps.md
• Decision map, estimands, assumptions, tooling: references/primitives-overview.md
• Per-primitive playbooks: assets/templates/causal-inference/README.md
• Sources: data/sources.json is the citation register; verify a claim against the primary source it lists before quoting a number.

Learnings Loop

When prior decisions or pitfalls are relevant, consult learnings.consolidated.md if present; use learnings.md only for needed history or as the available fallback. Otherwise skip both.

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.