Causal Inference Questions

Direct answer. Uplift modeling predicts the incremental effect of a treatment for each individual, rather than the outcome itself, so instead of ranking users by their predicted likelihood of converting, you rank them by how much more likely they are to convert because of the treatment. It's preferable to relying on the average effect from a randomized experiment whenever the effect is genuinely heterogeneous and you can act on that heterogeneity, for example targeting a promotion only at the users it will actually move, rather than spending budget on users who would have converted anyway (or who are actively put off by it).

Structured elaboration. Common modeling families:

• Two-model approach: fit one outcome model on the treated group and one on the control group, and take the difference in their predictions for each user. Simple but each model's own noise compounds in the difference.
• Transformation (class-transformation) approach: recode the outcome so a single classifier can be trained to directly target the uplift signal, avoiding the double-noise problem of the two-model approach at the cost of some interpretability.
• Meta-learners: the S-learner (a single model with treatment as a feature), the T-learner (essentially the two-model approach with a formal name), and the X-learner (a two-stage approach that imputes individual treatment effects and then models them directly), which generally handles imbalanced treatment/control group sizes better than the T-learner.

For evaluation, since you never observe an individual's true incremental effect, the standard tool is a cumulative-gain-style curve (a Qini curve or uplift curve): sort users by predicted uplift, and check that targeting the top-ranked users by predicted uplift produces a larger real, aggregate lift than targeting a random sample of the same size.

Worked example. For a retention promotion, a T-learner trained on randomized controlled trial (RCT) data might identify that lapsing but still-engaged users show the largest predicted incremental lift (say, +8 percentage points in return-rate), while highly loyal users show near-zero incremental lift (they'd have returned anyway) and a small segment of price-sensitive but disengaged users shows a negative predicted effect (the promotion draws attention to pricing and pushes them to churn instead). Targeting only the first segment, rather than everyone, both saves budget and avoids the negative-effect group.

Trade-offs and pitfalls. Uplift models need randomized (or at least well-identified) training data to learn a true incremental effect rather than just a correlational one; training an uplift model on purely observational data without correcting for confounding will produce a model that looks like uplift but is contaminated by the same selection bias that plagues any observational effect estimate.

Direct answer. With treatment $A$, outcome $Y$, a confounder $Z$ (which affects both $A$ and $Y$), a mediator $M$ on the path $A \to M \to Y$, and a collider $C$ caused by both $A$ and $Y$: the backdoor criterion says you must adjust for $Z$ (it opens a non-causal "backdoor" path between $A$ and $Y$ that needs to be blocked), and you must NOT adjust for $M$ (it's on the causal path itself; controlling for it would remove part of the very effect you're trying to measure) or $C$ (conditioning on a collider opens a new spurious association rather than blocking one).

Structured elaboration. The backdoor criterion, informally: a set of variables satisfies it for estimating the effect of $A$ on $Y$ if it blocks every "backdoor path" (a path into $A$ that isn't through the causal arrows you care about) while not including any descendant of $A$ on the causal path to $Y$. Here, $Z \to A$ and $Z \to Y$ forms exactly such a backdoor path; adjusting for $Z$ blocks it. $M$ is a "front-door" variable on the causal path from $A$ to $Y$, not a backdoor variable, so it's excluded. $C$ is a collider: since $A \to C \leftarrow Y$, $C$ is not a path INTO $A$ at all, and conditioning on a collider (by adjusting for it, or by any implicit selection that filters on it) creates a spurious association between $A$ and $Y$ that wasn't there before, because you'd be selecting a biased subsample where $A$ and $Y$ appear artificially linked through their shared effect.

Worked example. In a promotion-click-purchase scenario: promotion increases the chance of a click, and clicking increases the chance of a purchase; income independently increases both the chance of seeing/engaging with the promotion AND the chance of purchasing. To estimate the causal effect of the promotion on purchase, adjust for income (a backdoor confounder), but do NOT adjust for click even though it sits between promotion and purchase; click is a mediator of the very effect (promotion causes purchase partly BY causing clicks), so controlling for it would strip out that channel and understate the promotion's true effect. Similarly, for a loyalty program where users self-select into enrollment based on pre-existing purchase frequency (a confounder) and enrollment also increases engagement which independently affects frequency (a mediator on the path), the same logic applies: adjust for pre-existing purchase frequency, not for post-enrollment engagement.

Trade-offs and pitfalls. The most common real-world mistake is reflexively "controlling for everything available in the dataset," which silently includes mediators and colliders alongside genuine confounders; sketching the DAG (directed acyclic graph) first, even informally, is what turns "which variables go in the model" from an intuition call into a mechanical, checkable decision.

Direct answer. A sensitivity analysis quantifies how strong an unmeasured confounder would need to be, in terms of its relationship to both treatment and outcome, before it could fully explain away your observed effect. Two standard tools are Rosenbaum bounds, which ask how much an unmeasured factor could distort the odds of treatment assignment before your conclusion (the p-value or effect direction) becomes unreliable, and the E-value, a more recent and more directly interpretable measure of the minimum strength of association, on the risk-ratio scale, that an unmeasured confounder would need with BOTH treatment and outcome to fully explain away the estimate.

Structured elaboration. The E-value for an observed risk ratio $RR$ (for $RR \geq 1$) is:

$$E = RR + \sqrt{RR \times (RR - 1)}$$

This gives the minimum risk ratio an unmeasured confounder would need to have with BOTH the treatment and the outcome, on this same multiplicative scale, to fully explain away the observed association. A larger E-value means a stronger, harder-to-dismiss result; an E-value close to 1 means even a weak unmeasured confounder could explain the whole effect away.

Worked example. Suppose an observational estimate finds a risk ratio of $RR = 1.5$ for a retention-boosting feature. Computing the E-value:

$$E = 1.5 + \sqrt{1.5 \times 0.5} = 1.5 + \sqrt{0.75} \approx 1.5 + 0.866 = 2.366$$

This means an unmeasured confounder would need to be associated with BOTH feature adoption and retention by a risk ratio of at least about 2.37 (each) to fully explain away the observed 1.5 effect. A plain-language interpretation for a non-technical stakeholder: "for this result to be spurious, there would need to be some unmeasured factor that makes users roughly two and a half times more likely to both adopt the feature and retain, purely by coincidence with the true effect being zero. Given the confounders we've already controlled for, that's a high bar, but not an impossible one, which is why we're still recommending a confirmatory experiment before scaling investment."

Trade-offs and pitfalls. A sensitivity analysis doesn't prove the result is unconfounded, it quantifies how much confounding would be needed to overturn it, which is a meaningfully different and more honest claim; the biggest pitfall is presenting a comfortably large E-value as proof of causality, when a genuinely strong unmeasured confounder (a marketing campaign that happened to target both feature-adopters and high-retention users) could still plausibly exceed even a moderately large threshold.

Direct answer. A directed acyclic graph (DAG) is a diagram of variables connected by arrows representing assumed causal direction, with no cycles (you never follow the arrows back to where you started). Sketching one before running a causal regression forces you to make your assumptions about what causes what explicit, which is exactly the information you need to decide which variables belong in your regression as controls, and which ones you must leave out.

Structured elaboration. Without a DAG, "control for everything you have data on" feels like the safe default, but it is actually a common source of bias: some variables (mediators, colliders) must be excluded, and getting this wrong quietly corrupts the estimate while the regression output still looks perfectly normal. A DAG turns "which variables should I control for" from a guess into a mechanical exercise, using the backdoor criterion, once the causal structure is drawn out.

Worked example. You want the causal effect of a loyalty program on purchase frequency. Before regressing, sketch: does the program affect frequency directly (yes, that's the effect you want)? Does anything affect both program enrollment and purchase frequency (baseline spend level, likely a confounder to control for)? Does the program affect anything that in turn affects frequency (an app-usage increase driven by program engagement, a mediator to leave out of a total-effect estimate)? Ten minutes of sketching turns a vague "control for everything" plan into a specific list: control for baseline spend, do not control for post-enrollment app usage.

Trade-offs and pitfalls. A DAG is only as good as the assumptions behind it, and two reasonable analysts can draw different DAGs for the same problem; the value is not that it produces one objectively correct answer, but that it makes the disagreement explicit and debatable instead of hidden inside a regression's variable list.

Direct answer. Because signup was voluntary, treated users aren't a random sample of the target population, they're systematically younger, which biases a naive average treatment effect if age (or whatever drove the younger skew) also affects the outcome. Inverse probability weighting (IPW), post-stratification, or a transportability adjustment can each recover an estimate that better represents the intended target population rather than just the self-selected sample.

Structured elaboration.

• Inverse probability weighting: model the probability of selecting into the sample (using age and other observed characteristics), then weight each observed unit by the inverse of that probability, so underrepresented groups (older users, in this case) count more heavily in the weighted average, correcting for the skew.
• Post-stratification/reweighting: split the sample into strata by age band, compute the effect within each stratum, then combine using the age distribution of the TARGET population (not the sample) as weights.
• Transportability: a more general framework for formally stating what additional assumptions are needed to transport an effect estimated in a selected sample to a different target population, useful when the selection mechanism is complex or only partially known.

Worked example. If the sample skews toward users under 30 (60% of the sample vs. 35% of the full user base), and the treatment effect is meaningfully different for younger versus older users, a raw average over the sample overweights the under-30 effect relative to the population you actually care about. Reweighting each age stratum's estimated effect by the population's true age distribution (35% weight for under-30, not 60%) produces an estimate that better reflects the effect for the population as a whole, assuming age captures the main driver of who self-selected in.

Trade-offs and pitfalls. All three corrections only fix selection ON OBSERVED characteristics; if something unmeasured (unusual motivation, prior exposure to a similar product) drove both the decision to sign up and the outcome, none of these techniques touch that, and the corrected estimate is still biased, just less so than the raw sample average. It's also worth being explicit that these corrections change WHAT population the estimate describes (the full target population versus the self-selected sample), which is exactly the kind of nuance interviewers probe for.