Reference: Causal Inference Glossary

This is the working vocabulary file for the Blue Harbor Hotels causal-inference series (Maya, Priya, and the 90-day cancellation policy). Treat it as a lookup table: every term that recurs across the 10-part series lives here, with one plain-English definition, a tiny diagram, and a pointer to where it shows up in the corpus.

If you read the series in order, you’ll notice the same five or six ideas get re-explained in each article. They live here so the articles can stay focused on the method (sensitivity analysis, IV estimation, counterfactual reasoning) instead of re-defining “DAG” every time.

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Roster

Term	Plain-English definition	Mini-DAG (ASCII)	Range / type	When to use it	Used in corpus article
Treatment (Z, T, or A)	The variable whose effect we want to measure — the “intervention.” In Blue Harbor, whether a hotel offered the 90-day cancellation policy.	Z ──► Y	binary or continuous	Define it before you look at data; it’s the policy/feature you’d push a button to change.	All 10 causal-inference articles, plus the A/B-testing article
Outcome (Y)	The metric we believe the treatment moves. In Blue Harbor, rebooking within 12 months (and later, guest satisfaction).	Z ──► Y	continuous, count, or binary	Pick one primary outcome per question; secondary outcomes go in a sensitivity check.	Same as above
Confounder (X or W)	A cause of both treatment and outcome that, if ignored, makes the treatment-outcome association a lie about causality.	X ─► Z X ─► Y Z ─► Y	any type	Adjust / stratify / regress on it, or block it in the DAG. Ignoring it is the most common causal bug.	Simpson’s paradox), P01 correlation vs causation), P04 sensitivity)
Mediator (M)	A variable on the causal path from treatment to outcome. Part of the effect flows through it.	Z ─► M ─► Y	any type	Do not adjust for it on the main effect — you’d block the very effect you’re trying to measure. Use it for mediation / mechanism analysis instead.	P09 counterfactuals), P10 end-to-end)
Collider (C)	A variable caused by both treatment and outcome (or by descendants of them). Conditioning on it opens a spurious path.	Z ─► C ◄─ Y	any type	Avoid unless you’re intentionally studying selection. Conditioning here is a classic “Berkson’s paradox” trap.	Simpson’s paradox), P04 sensitivity)
DAG (directed acyclic graph)	A picture of assumed causal relationships. Nodes are variables; arrows are direct causes; no cycles allowed.	the whole diagram	structure	Sketch it before estimation. The DAG tells you which variables to adjust for and which to leave alone.	P01), P10)
Estimand	The quantity you want to know — written in math, not code. A precise sentence about a target population.	E[Y(z=1) − Y(z=0)]	a scalar target	Specify it before choosing an estimator. “ATE”, “ATT”, “CATE” are all estimands.	P01), P10)
ATE (average treatment effect)	The average causal effect of treatment across the whole population: what would happen if everyone flipped from untreated to treated.	E[Y(1) − Y(0)]	real number	The default “first number to report.”	P01), P10)
CATE (conditional ATE)	The ATE for a subgroup defined by pre-treatment covariates (e.g., business vs leisure guests).	E[Y(1) − Y(0) | X = x]	function of x	Use it for heterogeneous effects / targeting — “does this policy help business travelers?”	P10), partial dependence / ICE)
Identification	The bridge from “what we can observe” to “the estimand we want.” Proves the estimand is recoverable from data + DAG.	estimand = f(observables) given assumptions	proof / argument	Do this before coding an estimator. If it doesn’t identify, no fancy model saves you.	P01), P10)
Backdoor criterion	A sufficient rule: if you block every backdoor path (paths into Z) by conditioning on a valid set, the Z ─► Y association is causal.	X ─► Z, X ─► Y ⇒ condition on X	rule on the DAG	Use when you have measured the confounders. Most common identification strategy.	P01), P10)
Frontdoor criterion	When you can’t adjust for a confounder directly, but a measured mediator fully transmits the effect — use the mediator.	Z ─► M ─► Y, U ─► Z, U ─► Y	rule on the DAG	Use when an unmeasured U confounds Z─Y but a clean mediator M carries the entire effect. Rare but powerful.	P10)
Instrumental variable (IV)	A variable IV that affects treatment but has no direct path to outcome except through treatment.	IV ─► Z ─► Y U ─► Z, U ─► Y	any type	Use when there’s an unmeasured confounder but a clean “nudge” (price, distance, random push).	P04 sensitivity), P10)
Counterfactual	The outcome a single unit would have had under a different treatment than the one received.	Y(z=0) for a unit with z=1	per-unit, unobserved	The fundamental object of causal inference — ATE is an average of these.	P09 counterfactuals), P10)
SUTVA (stable unit treatment value assumption)	No interference between units and no hidden versions of the treatment.	(assumption, not a DAG node)	assumption	Check it before pooling — e.g., one guest’s policy doesn’t spill over onto another’s behavior.	P01), A/B testing)
Positivity	Every subgroup defined by covariates has a nonzero chance of receiving each treatment level.	0 < P(Z=1 | X=x) < 1	assumption	Without it, you can’t estimate CATE for that subgroup — there’s no data to compare against.	P10)
Consistency	The outcome you observe for a unit equals the potential outcome under the treatment they actually got.	Y = Y(z) when Z = z	assumption	It breaks if “treatment = 1” means different things for different people. Define the treatment sharply.	P01), P10)
Exchangeability	Treated and untreated groups are comparable — would have had the same outcomes on average if treated the same.	Y(0) ⊥ Z (or ⊥ Z | X for conditional)	assumption	The “no unmeasured confounding” assumption. The most consequential one in any causal study.	P04 sensitivity), P10)

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The Ladder of Causation (Pearl)

Pearl frames causal reasoning as three nested rungs. Each one is strictly more than the one below.

1. Seeing (association) — P(Y | Z = z). What’s the pattern in observed data? This is what regression and most ML report by default. Question: “What if I see Z = 1?”
2. Doing (intervention) — P(Y | do(Z = z)). What would happen if I forced Z to a value, cutting incoming arrows? Question: “What if I do Z = 1?”
3. Imagining (counterfactual) — Y(z = z') for a unit with Z = z. What would have happened for this specific person under a different treatment? Question: “What if I had done Z = 0 instead?”

The ladder matters because each rung needs more assumptions, more structure, and more machinery. A predictive ML model lives on rung 1. An A/B test answers a rung-2 question by running a real do(). The Blue Harbor observational study wants a rung-2 answer but only has rung-1 data — so it leans on DAGs, identification, and assumptions to climb.

Seeing, Doing, Imagining — formal version

Plain English	Statistical symbol	Python equivalent
Distribution of Y given we observe Z = z	$P(Y \mid Z = z)$	df[df.Z==z].Y (just filter observed rows)
Distribution of Y given we force Z = z (cut incoming arrows)	$P(Y \mid do(Z = z))$	requires a model or experiment; not a simple filter
Outcome for unit i under treatment z, even if their actual treatment was z’	$Y_i(z)$ or $Y_i^{(z)}$	unobservable for the “other” treatment — fundamental missing-data problem
ATE = average of the difference in two potential outcomes	$\mathbb{E}[Y(1) - Y(0)]$	np.mean(Y_if_treated - Y_if_untreated) (in counterfactual land)
Conditional ATE	$\mathbb{E}[Y(1) - Y(0) \mid X = x]$	stratify by X, compute ATE per stratum

The whole game of observational causal inference is: given only $P(Y \mid Z = z)$, can I recover $P(Y \mid do(Z = z))$? The DAG and assumptions say when the answer is yes.

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Which concept for which problem? (decision tree)

Use this to figure out which tool in this glossary applies to your situation.

• I have a question about a policy I could change.
  • Is it a randomized experiment you can run? → It’s an A/B test; the randomization guarantees exchangeability. (A/B testing))
  • It’s observational (no randomization) → keep going.
    • Do you have a guess at the causal structure? → Draw a DAG.
      • Are there common causes of treatment and outcome? → Confounder(s); apply the backdoor criterion.
      • Is the effect fully transmitted through a measured mediator? → consider the frontdoor criterion.
      • Is there a “nudge” that affects treatment but not outcome (except through treatment)? → instrumental variable.
      • Is the effect different per subgroup? → CATE.
    • You don’t know the structure? → you have a prediction problem, not a causal one. Stop here.
• I have an effect estimate; I want to know if it’s robust.
  • How sensitive is the conclusion to unmeasured confounding? → sensitivity analysis (P04)).
• I want to ask “what would have happened to this guest under the other policy?”
  • That’s a counterfactual question → P09).
• I want to summarize a model’s behavior for a treated vs untreated group.
  • Use partial dependence / ICE to surface model-implied heterogeneity (PDP & ICE)) — but read it as association, not cause, unless your model was built causally.

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Worked example — every term in one Blue Harbor scene

The setup, repeated across the series: Maya (data scientist) and Priya (head of analytics) want to know whether Blue Harbor’s 90-day cancellation policy increased rebooking within 12 months. Some hotels adopted it (Z = 1), some didn’t (Z = 0). The observable association is positive but Maya doesn’t trust it — business-heavy city hotels, which already had higher rebooking, were more likely to adopt.

The mini-DAG

                segment  ────────────────►  rebooking
                  │                              ▲
                  ▼                              │
                policy  ────────────────►    rebooking
                  │                              ▲
                  └────────►  satisfaction ──────┘
                              (mediator)

Read it out loud:

• segment ─► policy and segment ─► rebooking: segment is a confounder.
• policy ─► satisfaction ─► rebooking: satisfaction is a mediator.
• If we (wrongly) compared only guests who left a review, then “left a review” would be a collider (policy ─► reviewed ◄─ rebooking).

The code (one runnable illustration)

import numpy as np
import pandas as pd

rng = np.random.default_rng(42)
n = 4000

# Covariate: guest segment (0 = leisure, 1 = business). Causes both adoption and rebooking.
segment = rng.binomial(1, 0.5, n)

# Treatment: 90-day policy. Business-heavy hotels more likely to adopt.
policy = rng.binomial(1, 0.25 + 0.40 * segment)

# Mediator: post-stay satisfaction score (0-100). Pushed up by policy.
satisfaction = 60 + 8 * policy + 5 * segment + rng.normal(0, 6, n)

# Outcome: rebooking within 12 months. True effect of policy ~ +10pp.
rebooking = rng.binomial(1, 0.15 + 0.15 * segment + 0.10 * policy)

df = pd.DataFrame({"segment": segment, "policy": policy,
                   "satisfaction": satisfaction, "rebooking": rebooking})

# (a) Naive association -- confounded by segment
naive = df.loc[df.policy == 1, "rebooking"].mean() - df.loc[df.policy == 0, "rebooking"].mean()
print(naive)  # ~ 0.178   <-- too high; segment is inflating it

# (b) Backdoor adjustment by stratifying on segment
ate_leisure  = df.query("segment == 0 & policy == 1").rebooking.mean() \
             - df.query("segment == 0 & policy == 0").rebooking.mean()
ate_business = df.query("segment == 1 & policy == 1").rebooking.mean() \
             - df.query("segment == 1 & policy == 0").rebooking.mean()
ate = 0.5 * ate_leisure + 0.5 * ate_business
print(ate)  # ~ 0.10   <-- close to the true 0.10 we baked in

The naive number (~17.8 pp) is not the ATE — it’s a biased association. The stratified number (~10 pp) is the backdoor-adjusted ATE and matches the truth because segment was the only confounder and we adjusted for it.

Line by line:

• segment = rng.binomial(1, 0.5, n) — 50/50 mix of leisure and business guests. This is the confounder in the DAG.
• policy = rng.binomial(1, 0.25 + 0.40 * segment) — business hotels are ~40 percentage points more likely to have adopted (25% baseline vs 65% for business). This is the source of confounding: segment influences policy.
• satisfaction = ... — a mediator: the policy changes satisfaction, and satisfaction is part of how rebooking happens. We won’t adjust for it on the main ATE (we’d block part of the effect).
• rebooking = ... — the outcome. The coefficient 0.10 * policy is the true ATE.
• naive = ... — the seeing rung. It tells us the conditional association, which is not the causal effect because segment is a common cause.
• The stratified block — the doing rung. We compute the effect within each segment, then average. This is the backdoor criterion applied by hand: one covariate, one stratum at a time.

The gap between naive and ate is the confounding bias — exactly what the series’ P01 article warns about.

Mapping every term onto this scene

Term	Where it lives in the Blue Harbor scene
Treatment	policy (the 90-day cancellation offer)
Outcome	rebooking (rebooked within 12 months)
Confounder	segment (leisure vs business)
Mediator	satisfaction
Collider	would be left_a_review if we filtered to reviewers only
DAG	the picture above
Estimand	ATE = “average rebooking rate if every hotel had the policy minus if none did”
ATE	the ~0.10 number above
CATE	ATE for business vs leisure separately (ate_business, ate_leisure)
Identification	“We can identify the ATE from observational data because segment blocks the only backdoor path.”
Backdoor criterion	“Condition on segment.”
Frontdoor criterion	not needed here — would be relevant if segment were unmeasured and satisfaction fully mediated the effect
IV	would be “distance to nearest competitor with the policy” or “regional marketing push” if segment were unmeasured
Counterfactual	“What would this specific business guest’s rebooking have been if their hotel hadn’t adopted?” — Y_i(0) for a unit we saw with policy = 1
SUTVA	“One guest’s adoption doesn’t change another’s rebooking” — would fail if guests compared policies across hotels and switched
Positivity	“Both segments have some hotels with and without the policy.” Without that, CATE for the empty cell is undefined.
Consistency	“A hotel labeled policy = 1 really did implement the 90-day offer the same way.”
Exchangeability	“Within a segment, treated and untreated hotels would have rebooked at the same rate if treated the same.” This is the assumption we can’t test — P04 (sensitivity)) stress-tests it.

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Edge cases and common mistakes

Adjustment mistakes — the wrong choice of what to condition on:

• Adjusting for a mediator blocks your own effect. If Maya regresses rebooking ~ policy + satisfaction, the coefficient on policy is not the total effect — it’s the direct effect, minus what flows through satisfaction. This is the most common analytical mistake in the corpus’s P10 case study.
• Conditioning on a collider opens a non-causal path. If you restrict the analysis to guests who left a review, and both the policy and the (re)booking outcome affect the probability of leaving a review, you’ve created a spurious association. Classic “Berkson’s paradox” trap.
• “Control for everything” is a heuristic, not a rule. It works for pre-treatment covariates that aren’t colliders or mediators. Post-treatment covariates are usually trouble. The DAG, not a checklist of available columns, decides the adjustment set.

Assumption violations — the four identifying assumptions failing quietly:

• Positivity violations hide as empty strata. If no leisure-segment hotel adopted the policy, you can’t estimate CATE(segment = leisure) — and the ATE will be a weighted Frankenstein of “we can identify business, we can’t identify leisure.” Check the support of policy | segment before estimating.
• Consistency breaks when the “treatment” is fuzzy. “90-day policy” might mean different things at different hotels (some with fees, some without). Define the treatment so Y(z) is well-defined for each z. If two units both have Z = 1 but different actual policies, consistency is violated.
• Exchangeability is untestable. You can never prove from data that there’s no unmeasured confounder. That’s why P04 exists: pick a plausible unmeasured confounder, see how strong it would have to be to flip the conclusion, and report that.
• SUTVA breaks in networked settings. If a guest at a treated hotel calls a friend at an untreated hotel and changes their behavior, or if “treatment” leaks through shared marketing, units aren’t independent. In the Blue Harbor setting, this matters if city-pairs share a market.

Estimand mismatches — solving the wrong quantity even when the math is right:

• The ATE is not the policy-relevant quantity if treatment uptake is selective. If only 12% of hotels would ever adopt, the ATT (average treatment effect on the treated) might be more policy-relevant than the ATE. Pick the estimand to match the decision being made — P10) covers this choice.
• CATE is not “the subgroup effect I see in a tree.” It’s the causal effect in a subgroup. A tree split’s leaf difference is an association unless you’ve built the tree to estimate causal effects (e.g., causal forest, T-learner). The PDP/ICE article (here)) is explicitly not causal — keep the distinction clean.

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Cross-references

These corpus articles use the vocabulary in this reference:

• Causal inference in Python — P01: Correlation isn’t causation)
• Causal inference in Python — P04: Sensitivity analysis)
• Causal inference in Python — P09: Counterfactual reasoning)
• Causal inference in Python — P10: End-to-end case study on the hotel data)
• Simpson’s paradox: when aggregated data tells the wrong story)
• Partial dependence plots and ICE curves)
• A/B testing: deployed models, shadow deployments, and…)

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Further reading

• Pearl, J. (1995). “Causal diagrams for empirical research.” Biometrika, 82(4), 669–688. — the original introduction of the causal-DAG framework and the backdoor criterion.
• Pearl, J. (2009). Causality: Models, Reasoning, and Inference, 2nd ed. Cambridge University Press. — the canonical book; Chapter 1 lays out the Ladder of Causation and Chapter 3 the backdoor and frontdoor criteria.
• Imbens, G. W., & Rubin, D. B. (2015). Causal Inference for Statistics, Social, and Biomedical Sciences. Cambridge University Press. — the potential-outcomes (“Neyman–Rubin”) framework at book length; this is where the counterfactual notation $Y(1) - Y(0)$ and the SUTVA / consistency / positivity / exchangeability assumptions are stated precisely.
• dowhy documentation — https://py-why.github.io/dowhy/ — the Python library used throughout the Blue Harbor series. Its four-step API (model the DAG, identify the estimand, estimate, refute) mirrors the structure of this glossary exactly.
• Hernán, M. A., & Robins, J. M. (2020). Causal Inference: What If. — free online at https://www.hsph.harvard.edu/miguel-hernan/causal-inference-book/. Chapters 1–3 are a gentler complement to Pearl’s formalism and use the same “treatment / outcome / confounder” vocabulary this reference leans on.