Regression Discontinuity Interview Questions: Cutoffs, Manipulation, and Local Effects

A regression discontinuity (RD) interview question asks whether a rule that changes treatment at a score cutoff can identify a local causal effect. The core comparison is between units just below and just above the threshold, not every treated unit against every untreated unit. A strong answer names the running variable, cutoff, treatment jump, outcome window, and assumptions before choosing a model. Then it audits whether people can sort across the line, whether another policy changes there, and whether the result survives reasonable bandwidth choices.

The cases and figures below are original practice examples, not candidate-reported interview items. The methodological boundaries follow primary RD research and the rdrobust documentation. To compare RD against other ways to handle selection bias, use Diagnose and fix selection bias in experiments after this case.

Question 1: What exactly changes at the cutoff?

Original case: Applicants receive a coaching offer when a pre-program score is at least 70. The offer is automatic, and everyone offered accepts in this simplified case. The business wants the effect on completion within 90 days. Scores range from 0 to 100, and applicants with higher scores are more likely to complete even without coaching.

Write X for the score, c = 70 for the cutoff, D = 1{X >= 70} for treatment, and Y for 90-day completion. This is a sharp RD only if treatment really follows the rule with no exceptions. The naive mean completion difference between everyone above and below 70 mixes coaching with baseline score differences. RD instead estimates the difference between the limiting expected outcomes as X approaches 70 from above and below. Under continuity of potential outcomes at the cutoff, that jump identifies the average treatment effect at 70.

Suppose local fits estimate a completion probability of 40% immediately below and 46% immediately above. The estimated discontinuity is 6 percentage points at the threshold. It is not a 6% relative lift, not the effect for a score-95 applicant, and not necessarily the programme's average effect. A confidence interval and design checks still determine how much weight to put on the point estimate.

The assumption is substantive. Without coaching, would expected completion change smoothly through score 70? If applicants can precisely move themselves from 69.9 to 70.1, or an unrelated grant also starts at 70, the two sides may no longer differ only in the coaching offer. RD does not become an experiment by naming a cutoff; the rule must create a credible local comparison.

Question 2: Why is “compare 69 with 70” not the full analysis?

A raw two-bin contrast can mislead when scores are noisy, discrete, or associated with a sloping outcome. People at 69 and 70 might differ for reasons unrelated to coaching; a one-point bin may be too small or too coarse to estimate the limit. In a typical continuous-score RD, fit local trends separately on each side of 70, giving nearby observations more weight and reporting the jump at the boundary. The RD handbook chapter explains the identification and local estimation logic; the rdrobust documentation describes local-polynomial estimation, data-driven bandwidths, and robust confidence intervals.

Do not fit one high-degree polynomial across the full 0–100 range and call its discontinuity “local.” Far-away observations can drive the shape near 70. A local linear specification is a defensible starting point, with bandwidth and inference chosen for the target analysis. The graph is diagnostic, not the estimate itself: binning and axis choices can create or conceal an apparent jump.

If scores are integers with few distinct values near 70, say so. The running variable may be discrete, with mass points and little support immediately next to the threshold. That limits how convincingly a continuous-limit approximation can be made. Report the number of unique score values on each side, inspect the assignment mechanism, and use inference or design strategies suitable to the support rather than treating thousands of applicants at the same score as thousands of independent score locations.

Question 3: How do you choose and defend a bandwidth?

The bandwidth says how far from 70 the local fit reaches. Too wide can import curvature and groups that are unlike those near the cutoff; too narrow can make the estimate noisy or leave too few score values. A data-driven selector is a starting point, not a license to search until a desired sign appears. State the main bandwidth rule before seeing the preferred answer, then show how estimates and uncertainty behave at nearby reasonable widths.

Suppose the estimate is +6 points in a 5-point window, +5 in a 7-point window, and +1 in a 15-point window. Do not report “about six” without investigating why the wider estimate shrinks. Maybe the treatment effect is especially local; maybe the functional form is poor; maybe a different policy starts near 80. Conversely, a small change in estimate across widths does not validate continuity or no sorting. Sensitivity is one check in a larger argument.

Report an interval, not just a point estimate and p-value. Conventional intervals at a bandwidth selected for point estimation can have poor coverage because local polynomial bias matters. Modern RD methods offer robust bias-corrected inference; the Cattaneo and Titiunik review describes the design, estimation, and validation landscape. In an interview, you need not derive the full estimator, but you should know why “a significant jump after trying many widths” is weak evidence.

Question 4: How would you detect score manipulation?

Ask how X is generated and recorded. If an applicant can retake the test, round a reported value upward, or ask staff to reclassify a score, the distribution may bunch immediately above 70. Plot the score counts with enough resolution to see heaping, inspect the exact-score rule, and compare with periods before the coaching threshold existed. A local-polynomial density test can test for a discontinuity in the running-variable density, but its result is evidence to interpret, not a magical validity certificate.

Suppose the count at 70 is twice the count at 69. That could indicate strategic sorting, but it could also arise from integer scoring, routine rounding, or a natural mass point. Check how scores were calculated, whether bunching appeared only after the rule, and whether the spike is asymmetric relative to nearby values. A density-test rejection does not identify who manipulated or exactly how. A non-rejection does not prove manipulation is absent, especially with limited power or coarse scores.

If sorting is credible, do not hide it by picking another bandwidth. A “donut RD” that excludes the nearest scores can be a sensitivity analysis when local contamination is limited, but removing the observations closest to 70 changes what data support the estimate and does not automatically restore identification. Explain what remains comparable, and be prepared to say the RD cannot answer the question credibly.

Question 5: Which other validity checks matter?

Check variables determined before the coaching offer: prior completion history, region, application channel, or other baseline traits. They should not jump sharply at 70 under the proposed local comparison. A jump could indicate sorting, another rule, a data join problem, or a real discontinuity in the score-generating process. Do not “fix” the design by controlling for variables caused by coaching; post-treatment adjustment can create new bias.

Inventory every policy that uses score 70. If coaching, a fee waiver, and priority support all begin there, the outcome jump is attributable to the bundle unless another design separates the components. A sharp RD for “coaching alone” fails even if the score density is smooth. Similarly, the outcome must start after assignment and be measured comparably on both sides; a different tracking workflow above the line can produce a measurement jump.

Placebo cutoffs are useful falsification checks. If the same method finds large jumps at 60 and 80 where no treatment changes, investigate model shape or another policy. A null placebo result is reassuring but not proof. Also inspect missing outcomes: if applicants below 70 are less likely to have a recorded completion status, the estimate can be distorted by differential observation rather than treatment.

Check	Warning signal	What the answer should say
Rule audit	Exceptions to automatic assignment	Reclassify as fuzzy RD or revise treatment definition
Score density	New bunching just above 70	Investigate retakes, rounding, and sorting
Pre-treatment covariates	Sharp jump at 70	Seek selection, co-treatment, or data error
Other policies	Fee waiver also begins at 70	Interpret bundle, not coaching alone
Bandwidth/specification	Estimate changes sharply	Report instability and investigate functional form
Missing outcomes	Observation rate jumps	Audit measurement and selection

This is an original diagnostic ledger, not a claim that every row can be resolved with one statistical test.

Question 6: What if the rule is not perfectly obeyed?

If some applicants above 70 decline coaching or some below 70 receive it by exception, eligibility changes the probability of treatment rather than treatment itself. That is a fuzzy RD. First show the treatment-probability jump at 70; an almost-flat first stage leaves little information. Under additional assumptions, the ratio of the outcome jump to the treatment jump can identify a local complier effect. Do not divide by a guessed compliance percentage or call the sharp estimate the effect of actually receiving coaching.

Keep this distinction brief if the question asks about a sharp rule. The main challenge of the present case is cutoff validity, not a full instrumental-variable derivation. If exceptions correlate with an unobserved need, describing them as “random noncompliance” is not enough; explain why the cutoff-based comparison still supports the local interpretation and whether the offered treatment is the only thing changed by eligibility.

Question 7: What does a local effect let the business decide?

Return to the estimand. A credible +6-point effect at score 70 says something about marginal applicants who would change eligibility at that line. It may help decide whether to move the threshold a little or whether coaching is beneficial for that boundary group. It does not alone justify offering coaching to score-20 applicants or estimate the budget impact of treating the whole population. Those decisions need additional data, assumptions, or an experiment.

If the interval is wide enough to include meaningful harm and benefit, say the estimate is inconclusive for the decision. If density or covariate checks fail, do not bury that in a footnote beneath a precise coefficient. A useful stakeholder headline is conditional: “Near the score-70 cutoff, the estimated completion change is +6 percentage points, but the result is only credible if score sorting and co-occurring policies are ruled out.” Replace the number and caveat with actual results when available.

Interviewers may ask whether RD “proves causality.” A better answer is that the design can support a causal interpretation at the cutoff under continuity and an unconfounded threshold change. Diagnostics probe those assumptions; they cannot establish every unobserved counterfactual. This precision is more valuable than promising a universal effect.

Sources and further reading

• Cattaneo, Titiunik, and Vazquez-Bare, The Regression Discontinuity Design — primary methodological chapter on identification and local estimation.
• Cattaneo and Titiunik, Regression Discontinuity Designs — research review of designs, inference, and validation.
• rdrobust package documentation — implemented local-polynomial estimation and robust confidence intervals.
• Cattaneo, Jansson, and Ma, density discontinuity tests — methodological source for manipulation diagnostics.