I went with signup rate as primary, defined as unique users who started a trial divided by unique eligible visitors assigned to each variant.
Start by clarifying the experiment's goal and the product's north star, then define a primary metric that directly captures trial success (e.g., conversion to paid). Choose secondary metrics that explain the funnel and guardrail metrics that ensure the change doesn't harm user experience or long-term value. For each metric, specify the exact numerator and denominator to avoid ambiguity.
Pro tip: Always tie metrics to the decision the experiment will inform—if the primary metric moves but guardrails degrade, you need a clear rule for what you'd ship. Also, consider using a ratio metric like conversion rate with a well-defined denominator (e.g., users who started trial) rather than a simple count.
Restate the purpose of the free-trial experiment: to increase paid conversions without harming user experience. Define the target population and randomization unit (e.g., users).
Choose a metric that directly measures trial success, such as trial-to-paid conversion rate. Specify numerator (number of users who convert to paid within X days) and denominator (number of users who started the trial).
Select 2-3 metrics that provide insight into the funnel and user behavior, e.g., trial start rate (trial starts / eligible users), engagement during trial (e.g., daily active usage / trial users), and time-to-convert (median days from trial start to conversion).
Identify at least one metric to ensure no negative impact, such as refund rate (refunds / paid conversions) or customer support contacts per trial user. Set acceptable thresholds.
For each metric, state the exact numerator and denominator, time window, and how you'll handle edge cases (e.g., users who start trial multiple times). Mention statistical power and minimum detectable effect.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
ITT was my instinct and I think I got the reasoning right: you assign, you analyze, regardless of whether they saw the banner.
Start by clarifying that the choice between ITT and per-protocol depends on the estimand: ITT measures the effect of assignment, while per-protocol measures the effect of treatment receipt. For users assigned to treatment but never exposed, ITT includes them in the treatment group (preserving randomization), while per-protocol excludes them (risking selection bias). Recommend ITT as the default for causal inference, but discuss when per-protocol or CACE/LATE might be appropriate.
Pro tip: Emphasize that ITT is the gold standard for causal inference in randomized experiments because it preserves randomization and avoids selection bias, but acknowledge that per-protocol can be useful for understanding mechanism or when non-compliance is high. Mention that OpenAI likely values rigorous causal reasoning and practical trade-offs.
Clarify whether the goal is to estimate the effect of treatment assignment (ITT) or the effect of treatment receipt (per-protocol or CACE). This determines the appropriate analysis population.
Quantify how many users were assigned to treatment but never saw the offer. If non-compliance is low, ITT and per-protocol may yield similar results; if high, the choice matters more.
Default to ITT for causal inference because it preserves randomization and avoids selection bias. Report ITT as the primary analysis.
If interested in the effect among those who would comply, use per-protocol or CACE/LATE as secondary analyses, but acknowledge their limitations (e.g., selection bias, need for instrumental variables).
In ITT, include them in the treatment group as assigned. In per-protocol, exclude them, but discuss potential bias and consider sensitivity analyses.
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First, clarify that the treatment effect on retention is only defined for the subpopulation that would sign up under either treatment, and that conditioning on observed signup introduces post-treatment selection bias. Then propose estimating the effect within the always-signup principal stratum using either a principal stratification framework or a randomized encouragement design, and discuss assumptions and sensitivity analyses.
Pro tip: Emphasize that the estimand should be defined at the principal stratum level (e.g., always-signups) and that you would use a randomized encouragement design or instrumental variables to avoid conditioning on the post-treatment signup variable. This shows you understand both the causal inference nuance and the practical need for a valid identification strategy.
Explain that retention is only defined for signups, so the treatment effect on retention is a principal stratum effect (e.g., among always-signups). Conditioning on observed signup is post-treatment selection and can bias the effect estimate.
Propose using a randomized encouragement design or an instrumental variable approach where treatment assignment encourages signup but does not directly affect retention except through signup. Alternatively, use principal stratification with monotonicity and exclusion restriction assumptions.
Apply methods such as instrumental variables (e.g., two-stage least squares) or principal stratification (e.g., EM algorithm, Bayesian modeling) to estimate the treatment effect on retention among always-signups, using the full randomized data.
Discuss the plausibility of the exclusion restriction and monotonicity assumptions, and perform sensitivity analyses to check how violations would affect conclusions. Also consider alternative estimands like the effect on the treated signups with caveats.
Summarize that the estimated effect applies only to the always-signup subpopulation, and that generalizing to other strata may require additional assumptions. Highlight the importance of pre-registering the analysis plan to avoid p-hacking.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
I rattled off a bunch: wrong join type pulling in duplicate rows, filtering on post-assignment behavior before running the test (classic leakage), using event timestamps instead of assignment timestamps for the denominator, peeking at p-values daily without correction, and computing retention only on a subset of signups because of a bad date filter.
Structure your answer around the experiment lifecycle: data collection, metric computation, and statistical analysis. Emphasize that you would look for common pitfalls like selection bias, metric definition errors, and violations of statistical assumptions. Highlight the importance of reproducibility and sanity checks to catch setup problems early.
Pro tip: Mention that you would first verify the randomization and sample ratio mismatch (SRM) because if that's broken, nothing else matters. Also, emphasize that you'd check for subtle bugs like incorrect joins or timezone issues that can silently skew results.
Check for sample ratio mismatch (SRM) between control and treatment groups, and verify that randomization was properly implemented. Look for any data leakage or selection bias in how users were assigned.
Ensure metrics are correctly defined and computed consistently across groups. Look for bugs like incorrect aggregation, double counting, or missing data handling that could distort results.
Verify that the statistical tests used are appropriate for the data and that assumptions (e.g., normality, independence) are met. Check for multiple testing issues and correct calculation of p-values and confidence intervals.
Look for reproducibility issues such as hardcoded paths, lack of version control, or non-deterministic code. Suggest sanity checks like comparing pre-experiment metrics or running A/A tests.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
I framed it around whether the primary metric moved, whether guardrails held, and whether the retention gap (if any) was small enough that LTV still came out positive.
Start by defining clear success metrics that tie directly to long-term business value, such as retention, LTV, and expansion revenue. Then outline a decision framework that weighs statistical significance, practical significance, and strategic alignment. Finally, describe additional analyses like cohort analysis, sensitivity testing, and long-term holdout to ensure the decision is robust and connected to durable business outcomes.
Pro tip: Emphasize that the decision should not be based solely on short-term metrics; propose a long-term holdout or surrogate metrics to capture delayed effects. Also, consider the cost of delaying the decision and the opportunity cost of iterating versus killing.
Identify primary metrics (e.g., conversion, retention) and guardrail metrics (e.g., churn, support tickets) that reflect long-term value. Ensure they are measurable and aligned with business goals.
Analyze the experiment results for statistical significance, but also assess effect sizes and confidence intervals to determine if the impact is meaningful for the business.
Run cohort analyses, sensitivity tests, and if possible, a long-term holdout to measure sustained effects. Use surrogate metrics or predictive models to estimate LTV impact.
Consider strategic alignment, resource requirements, and opportunity costs. Assess whether iterating could yield better outcomes or if killing is more prudent.
Synthesize findings to decide ship, iterate, or kill. If iterating, define specific changes and success criteria for the next test. If shipping, outline monitoring and rollout plan.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.