This was essentially seven questions in a trenchcoat.
Start by framing the causal question and the interference challenge, then propose a cluster-randomized design with clear metrics and power analysis. Address practical issues like noncompliance, spillover, and safety, and outline quasi-experimental fallbacks for when randomization isn't feasible.
Pro tip: Emphasize that fake account removal can create spillovers through social ties, so cluster randomization by network communities is often necessary; also highlight the importance of pre-registering the analysis plan to avoid p-hacking.
Clarify the treatment (removing fake accounts) and outcome (real user experience). Choose a randomization unit that minimizes interference, such as clusters of connected users or geographic regions.
Identify primary metrics (e.g., engagement, retention, reports of fake accounts) and guardrail metrics (e.g., user trust). Conduct power calculations accounting for cluster randomization and intra-cluster correlation.
Design diagnostics to detect spillover (e.g., compare treated and control clusters' exposure). Monitor noncompliance (e.g., fake accounts not removed) and implement safety checks with sequential testing or stopping rules.
If randomization is infeasible, propose alternatives like difference-in-differences, synthetic control, or instrumental variables, and discuss their assumptions and limitations.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
Start by clarifying the experiment's goal and the nature of the fake account removal intervention, then evaluate each randomization unit against the trade-off between contamination control and statistical power. Recommend a hybrid or cluster-based approach that balances both, and explain how you would construct clusters to minimize spillover while preserving power.
Pro tip: Acknowledge that perfect isolation is often impossible in social networks; instead, propose a design that quantifies and bounds contamination, such as using ego-network clusters with a buffer zone, and pre-register sensitivity analyses to check robustness.
Understand what 'fake account removal' entails (e.g., removing accounts, flagging, reducing reach) and the primary metric (e.g., user engagement, spam reports). This determines the likely spillover mechanisms.
Compare user-level, ego-network, and geography-level randomization on contamination risk and power. User-level has high contamination but high power; geography-level has low contamination but low power; ego-network clusters offer a middle ground.
Select ego-network cluster randomization as the best balance, explaining that it groups connected users to limit spillover while retaining more clusters than geography-level, thus preserving power.
Build clusters using community detection algorithms (e.g., Louvain, Leiden) on the interaction graph, then merge small clusters and add buffer zones between treatment and control clusters to reduce cross-treatment interference.
Use cluster-level randomization inference, account for intra-cluster correlation, and consider variance reduction techniques (e.g., CUPED) to maintain power. Pre-register sensitivity analyses for contamination.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
Comments per view as primary felt obvious.
Start by clarifying the experiment's goal and the product surface, then define one primary metric that directly measures success, and 2-3 guardrail metrics that protect user experience and long-term health. For each metric, specify the exact formula, the time window (e.g., 7-day), and whether it's exposure-based (per user exposed) or calendar-based (daily aggregated).
Pro tip: Always tie guardrails to the specific risks of the change—e.g., if testing a new ad format, include ad load and user-reported satisfaction—and mention that you'd monitor them with sequential testing to catch early harm.
Ask about the product area, the change being tested, and the primary objective (e.g., increase engagement, revenue, or retention). This ensures metrics align with business goals.
Choose one metric that directly measures the experiment's success. Specify its formula (e.g., clicks per user), time window (e.g., 7 days post-exposure), and whether it's exposure-based (per exposed user) or calendar-based (daily active users).
Select 2-3 metrics that capture potential negative side effects, such as user retention, satisfaction, or system performance. Define each with formula, time window, and exposure/calendar basis.
For each metric, state the exact time window (e.g., 1-day, 7-day, 28-day) and whether it's measured per user (exposure-based) or aggregated daily (calendar-based). Explain why the window fits the metric's sensitivity.
Briefly recap the primary and guardrail metrics, and explain how they balance measuring success with protecting user experience and long-term goals.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
This is where I embarrassed myself a little.
Start by clarifying the metric definition and assumptions, then derive the sample size formula for a two-sample proportion test with overdispersion and clustering adjustments. Walk through the calculation step-by-step, explaining how each adjustment (overdispersion factor and design effect) inflates the required sample size.
Pro tip: Always discuss the practical implications of the adjustments—overdispersion and clustering can dramatically increase sample size, so it's crucial to consider whether the experiment is feasible and to explore variance reduction techniques like CUPED.
Define comments per view as a ratio metric, confirm baseline rate (0.12), relative change (0.5% => absolute change = 0.0006), and specify significance level (e.g., 5%) and power (e.g., 80%).
Use the standard formula for two proportions: n = (Zα/2 + Zβ)^2 * (p1(1-p1) + p2(1-p2)) / (p2-p1)^2, where p1=0.12, p2=0.1206, to get the per-variant sample size.
Multiply the base sample size by an overdispersion factor (e.g., variance inflation factor) to account for extra variability in the metric beyond binomial assumption.
Compute the design effect = 1 + (average cluster size - 1) * ICC, and multiply the sample size by this factor to account for intra-cluster correlation.
Combine adjustments to get the final required sample size, and discuss sensitivity to assumptions (e.g., ICC, overdispersion) and potential variance reduction methods.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
I suggested a ghost exposure analysis where you look at real users connected to removed fake accounts in the control group and check if their behavior shifts, and an edge-cut A/A where you compare users on the boundary of treatment clusters to interior users.
Start by defining what spillover effects mean in the context of the experiment, then propose two distinct tests: one for detecting spillover via network or geographic proximity, and another for quantifying it using a difference-in-differences or instrumental variable approach. For each test, clearly state the null hypothesis of no spillover effect. Emphasize the importance of randomization unit and potential interference.
Pro tip: Mention that spillover can bias treatment effect estimates, and propose using cluster randomization or saturation design to mitigate it. Also, highlight the need to pre-register the analysis plan to avoid p-hacking.
Clarify what spillover means in this experiment (e.g., users influencing each other through social ties or geographic proximity) and why it matters for causal inference.
Suggest a test to detect spillover, such as comparing outcomes of control users who are connected to treatment users versus those who are not, using network data. State the null hypothesis: no difference in outcomes between these groups.
Suggest a test to quantify spillover, such as a regression with treatment intensity of neighbors as a covariate, or a difference-in-differences design comparing areas with varying treatment saturation. State the null hypothesis: the coefficient on spillover term is zero.
Acknowledge assumptions like no unmeasured confounding, and limitations such as imperfect network data. Mention potential biases and how to address them.
Summarize how these tests inform experiment design and decision-making, and suggest mitigation strategies if spillover is detected.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
Used removal intensity (fraction of flagged accounts actually removed in a cluster) as the instrument for actual fake account exposure reduction.
Start by acknowledging that imperfect detection creates measurement error and noncompliance, which bias naive estimates. Then propose using an instrumental variable (IV) or difference-in-differences (DiD) design to isolate the treatment effect, depending on the setting. Walk through the assumptions, implementation, and sensitivity checks for each approach.
Pro tip: Emphasize that the IV must affect treatment take-up but not the outcome directly (exclusion restriction), and for DiD, the parallel trends assumption is key—suggest placebo tests and robustness checks to build credibility.
Clarify the treatment effect of interest (e.g., LATE) and explain how misclassification and noncompliance introduce bias in naive comparisons.
Decide between IV and DiD based on available data and context. For IV, identify a valid instrument; for DiD, define treatment and control groups with pre/post periods.
For IV: relevance, exclusion, and monotonicity. For DiD: parallel trends. Discuss how to test or probe these assumptions (e.g., first-stage F-stat, pre-trends).
Use two-stage least squares for IV or regression with interaction terms for DiD. Interpret the effect in light of the assumptions and potential violations.
Perform placebo tests, alternative specifications, and bounds analysis to assess how violations of assumptions might affect conclusions.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
Staged rollout was pretty standard: start at 1%, check guardrails, expand.
Start by outlining a phased rollout plan with clear success metrics and kill-switch thresholds, then address label leakage by describing how to isolate treatment effects from social influence. Emphasize the importance of pre-registering criteria and using techniques like cluster-based randomization or holdout groups to prevent contamination.
Pro tip: At Meta, where social networks are dense, label leakage is a major concern; propose using ego-network clustering or graph-aware randomization to minimize interference, and always have a pre-defined kill-switch that triggers automatically if guardrail metrics degrade beyond a threshold.
Clearly state the primary success metric (e.g., engagement, revenue) and guardrail metrics (e.g., user satisfaction, latency). Establish minimum detectable effect and required sample size.
Plan phases: internal test, small percentage (e.g., 1%), then gradual increase (5%, 10%, 50%). At each stage, monitor metrics and have pre-defined kill-switch criteria (e.g., if guardrail metric drops by >2% with statistical significance).
Use cluster-based randomization (e.g., by user ego-networks or geographic regions) to reduce interference. Alternatively, employ a holdout group or switchback testing to isolate treatment effects.
Set up real-time dashboards and automated alerts. If kill-switch criteria are met, automatically halt the experiment and revert changes. Document learnings for future experiments.
After rollout, analyze results accounting for interference (e.g., using causal inference methods). If successful, continue scaling; if not, iterate on design or abandon.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.
Synthetic control or staggered rollout with two-way fixed effects were the two options I laid out.
Start by acknowledging that randomization isn't always possible and propose a quasi-experimental design like difference-in-differences or synthetic control, using pre-treatment trends to validate. Then specify the covariates you'd pull from logs (e.g., user demographics, historical engagement, abuse-related signals) and how they'd be used to control for confounding. Finally, weigh the short-term engagement drop against the significant reduction in abuse reports, and recommend a product change that balances both metrics, such as a targeted intervention or a phased rollout.
Pro tip: Show that you understand the trade-off between engagement and abuse is not just a metric conflict but a business decision—tie your recommendation to Meta's mission and long-term user trust, and suggest a follow-up experiment to measure the intervention's impact on both metrics.
Select an appropriate method such as difference-in-differences, synthetic control, or regression discontinuity, depending on the market and data availability. Explain why it's valid and how you'd test its assumptions.
List specific covariates like user demographics, historical engagement metrics, abuse report rates, and time-based features. Explain how they'd be used to adjust for confounding and ensure comparability between treatment and control groups.
Quantify the short-term engagement drop and the reduction in abuse reports, and assess whether the abuse reduction is significant enough to justify the engagement loss. Consider segment-level impacts and long-term effects.
Propose a concrete product change, such as a targeted intervention that mitigates engagement loss while preserving abuse reduction, or a phased rollout with monitoring. Justify it with data and business goals.
Recommend a follow-up experiment or analysis to validate the quasi-experimental findings and measure the long-term impact of the product change on both engagement and abuse.
AI-generated suggestions, not part of the candidate's original notes. May be inaccurate — verify before relying on them.