- Which interpretation best reflects the usual bandwidth tradeoff in this setting?
Answer: The narrower bandwidth may reduce functional-form bias but increases variance by using fewer observations
Whenever you see a regression discontinuity (RD) question involving bandwidth choice, think about the fundamental tension between bias and variance — the same tradeoff that appears throughout statistics, but with a specific flavor here.
In an RD design, you compare outcomes just above and just below an eligibility cutoff. A wider bandwidth pulls in more observations farther from the cutoff, increasing statistical power (lower standard error), but those distant observations may follow a different trend than what holds right at the cutoff — introducing functional-form bias if the underlying relationship isn't perfectly linear. A narrower bandwidth restricts attention to observations very close to the cutoff, making the local-linearity assumption more plausible and reducing that bias, but it uses far fewer observations, which inflates the standard error. That's exactly what you see here: the wide-bandwidth estimate of 8 pp has a tight SE of 1 pp, while the narrow-bandwidth estimate of 3 pp has a much larger SE of 2.5 pp. Answer C correctly names this tradeoff — narrower may cut bias but raises variance.
A is wrong because a smaller standard error reflects precision, not freedom from bias. A precisely wrong estimate is still biased. B is wrong because proximity to the cutoff reduces one source of bias (functional-form misspecification), but doesn't guarantee zero bias — other threats like sorting or measurement error can still exist. D is wrong because a difference between two specifications is expected under the bandwidth tradeoff; it doesn't, by itself, prove manipulation.
Your study tip: on any RD or causal-inference question, always ask both "how precise is this estimate?" and "how credible is the identifying assumption?" — precision and validity are separate concerns. - How should the resulting IV estimate of 8/(0.45−0.25)=40 dollars be interpreted?
Answer: It is the adoption effect for customers whose adoption decision is changed by the invitation
Whenever you see instrumental variables (IV) in a setting with heterogeneous treatment effects, ask yourself: whose behavior is actually being changed by the instrument? That question is the key to interpreting what the IV estimate captures.
Here, the email invitation is the instrument, product adoption is the treatment, and revenue is the outcome. The IV formula divides the reduced-form effect (the invitation's impact on revenue, 8)bythefirst−stageeffect(theinvitation′simpactonadoption,0.45 - 0.25 = 0.20),yielding8/0.20 = 40dollars.UnderthestandardIVassumptions—includingthemonotonicityconditionstatedinthepassage(nocustomerbecomes∗less∗likelytoadoptbecauseoftheinvitation)—thisratioidentifiesthe∗∗LocalAverageTreatmentEffect(LATE)∗∗,whichistheaveragetreatmenteffectspecificallyfor∗∗compliers∗∗:customerswhoadopt∗becauseof∗theinvitationandwouldnothaveadoptedwithoutit.Thatmakes∗∗Dcorrect∗∗.∗∗A∗∗iswrongbecausetheIVestimateexcludesalways−adopters(whoadoptregardless)andnever−adopters(whoneveradoptregardless)—neithergroup′sadoptiondecisionismovedbytheinstrument,sotheycontributenothingtothecomplier−drivenvariationtheIVexploits.∗∗B∗∗iswrongbecausethatdescriptionmatchesthe∗∗Intention−to−Treat(ITT)∗∗effect—theraw8 revenue bump averaged over all emailed customers — not the IV-scaled estimate of $$40.
C is wrong because it describes always-adopters, whose adoption isn't affected by the invitation at all. The IV specifically isolates the marginal adopters, not those who would adopt unconditionally.
A useful study tip: when an IV question asks "who does this estimate apply to?", the answer under monotonicity is always the compliers — the group whose treatment status is switched by the instrument. - What fuzzy regression discontinuity estimate follows from these values?
Answer: A 10 percentage-point retention increase for cutoff compliers
When you encounter a fuzzy regression discontinuity design (RDD), the key insight is that crossing the cutoff doesn't guarantee treatment — it only changes the probability of receiving it. Because compliance is imperfect, you can't directly read the treatment effect from the outcome jump. Instead, you scale the outcome jump by the first-stage jump in treatment probability, essentially running an instrumental-variables calculation where the cutoff acts as the instrument.
The two jumps here are straightforward to compute. The first-stage jump in campaign receipt is 0.75−0.30=0.45. The reduced-form jump in retention is 0.665−0.620=0.045, or 4.5 percentage points. The fuzzy RDD estimate — the Local Average Treatment Effect for "compliers" near the cutoff — is:
LATE=First-stage jumpReduced-form jump=0.450.045=0.10
That's a 10 percentage-point retention increase for compliers, confirming answer C.
Answer A mistakes the raw reduced-form jump (4.5 pp) for the treatment effect, ignoring that only 45% of customers near the cutoff are switched into treatment by the recommendation. Answer B has no clean derivation from the given numbers — it doesn't correspond to either jump or their ratio. Answer D confuses the first-stage jump (0.45) with the treatment effect itself, essentially reporting the change in receipt rather than the scaled effect on retention.
A reliable tip: in fuzzy RDD questions, always identify two jumps — outcome and treatment probability — and remember the effect is their ratio, not their difference. - Why does this pattern create a serious concern for a regression discontinuity analysis of the bonus's effect on subsequent performance?
Answer: It suggests representatives may precisely sort around the cutoff, making near-threshold groups systematically different
Whenever you see a regression discontinuity (RD) question, anchor yourself to its core assumption: units just below and just above the cutoff must be as good as randomly assigned — differing only by chance, not by deliberate manipulation. This assumption is what allows you to attribute any jump in outcomes at the threshold to the treatment itself.
The pattern described — a suspicious spike just above the cutoff and a suspicious void just below — is the classic fingerprint of manipulation or "sorting." If representatives can strategically delay recording transactions, those who land just above the cutoff are not comparable to those just below. The ones above chose (or were able) to manipulate their timing; the ones below either couldn't or didn't. That self-selection means the two groups differ systematically in motivation, client relationships, or accounting flexibility — not just in whether they received the bonus. Your treatment and control groups are no longer exchangeable, and any estimated discontinuity reflects a mix of the bonus effect and those pre-existing differences.
Answer A is therefore correct. This is precisely the "sorting" or manipulation problem that invalidates the RD's identifying assumption.
Answer B is wrong because a concentration near the cutoff says nothing about whether receiving the bonus (the first stage) actually changes behavior — it speaks to who receives the bonus, not whether the bonus matters.
Answer C is wrong because nonlinearity is a separate methodological concern; the bunching pattern is about selection bias, not functional form.
Answer D is wrong because a fuzzy RD refers to imperfect compliance with treatment assignment, not to manipulation of the running variable itself.
Study tip: On RD questions, always ask two things: Is the running variable manipulable? And do you see bunching at the cutoff? If yes to both, sorting is your red flag.
- Which instrumental-variable assumption is most directly contradicted by this customer behavior?
Answer: Monotonicity, because the offer causes some customers to move opposite the intended treatment direction
When working with instrumental variables (IV), you need to verify four key assumptions: relevance, independence, monotonicity, and exclusion. This question tests whether you can identify which assumption breaks down when individuals respond to an instrument in the wrong direction.
Monotonicity requires that the instrument moves all individuals in the same direction — if the instrument nudges anyone toward treatment, it should nudge everyone either toward or away from treatment, never the opposite. Here, receiving the free trial extension should increase the likelihood of purchasing. But the passage explicitly describes customers who would have purchased without the offer yet refuse to purchase when offered it — they move in the opposite direction. These are called "defiers," and their existence is a direct violation of monotonicity. That makes C the correct answer.
A is wrong because relevance doesn't require the instrument to work for every individual — it only requires a nonzero average effect across the population. A few defiers don't automatically destroy relevance.
B is tempting because customers who dislike aggressive selling may indeed have different baseline attitudes, which sounds like an independence problem. However, independence concerns whether the instrument is randomly assigned (here it is — the vendor randomly offers extensions), not whether subgroups have different preferences. The issue isn't assignment; it's behavioral response direction.
D misidentifies exclusion, which requires that the instrument affects outcomes only through the treatment channel. Refusing to purchase is part of the treatment decision itself, not a separate pathway — so exclusion isn't what's violated here.
Your study tip: remember defiers = monotonicity violation. If a question describes individuals doing the opposite of what an instrument intends, think monotonicity first.
- What is the central identification problem for the proposed RD estimate?
Answer: The outcome may jump because of either program, so the review effect cannot be isolated at the cutoff
Regression discontinuity designs rest on one core assumption: the only thing that changes sharply at the cutoff is the treatment being studied. When that assumption breaks down, the design loses its ability to isolate a single causal effect.
Here, two programs — manual review and government payment assistance — both activate at the exact same credit score threshold of 620. If you observe a jump in default rates at that cutoff, you cannot tell which program caused it. Both treatment statuses switch simultaneously for the same borrowers, making the two effects completely confounded. This is the classical compound treatment problem in RD designs, and it makes the proposed estimate uninterpretable as a measure of manual review alone. Answer B captures this precisely.
Answer A is wrong because predictive power of the running variable is actually required for RD to be meaningful — the whole point is that credit scores predict outcomes, and the discontinuity in treatment at the threshold is what identifies the causal effect. Predictiveness alone never disqualifies a running variable.
Answer C misidentifies the problem. "Fuzzy" RD refers to imperfect compliance with treatment assignment — some people near the cutoff do or don't receive treatment contrary to the rule. Having two programs share one threshold doesn't create fuzziness; it creates a compound treatment problem, which is a different and more fundamental issue.
Answer D is incorrect because RD does not require identical scores on both sides — it requires that borrowers just above and below are otherwise comparable, which is a continuity assumption, not an exact-matching requirement.
When you see multiple treatments sharing a single cutoff, immediately flag compound treatment confounding as the RD validity threat. - Assuming potential outcomes are continuous at the threshold, what is the sharp regression discontinuity estimate?
Answer: A 5-thousand-dollar local increase in monthly margin at the threshold
Regression discontinuity design (RDD) works by treating a cutoff as a natural experiment. Because assignment flips sharply at the threshold, you can isolate the causal effect of treatment by comparing outcomes just above the cutoff to outcomes just below it — where clients are essentially identical except for receiving support. The key formula is simple: τ^RDD=limx→c+E[Y∣X=x]−limx→c−E[Y∣X=x], meaning you subtract the control-side limit from the treated-side limit at the threshold.
Here, the local regression gives $46K immediately above the threshold and $41K immediately below, so the sharp RDD estimate is 46−41=$5K. That makes A correct — it captures the local causal effect at the cutoff, not a global average.
B is wrong because it uses the broad-sample averages ($50K vs. $35K, giving $15K). That comparison ignores selection bias — supported clients may simply be larger or healthier firms to begin with. RDD exists precisely to avoid this trap.
C confuses a level with a difference. The $46K figure is the treated-side margin itself, not the treatment effect. You must subtract the counterfactual (the control-side prediction) to isolate the causal impact.
D mixes global and local estimates: $50K−$41K=$9K pairs the broad treated average with the local control prediction, which is an apples-to-oranges comparison.
Study tip: In RDD questions, always look for the two local estimates at the cutoff — one on each side — and take their difference. Any answer using broad sample averages is almost certainly a distractor. - Using reminder assignment as an instrumental variable, what causal effect is identified?
Answer: An increase of 30 dollars in weekly profit for stores induced to adopt
Whenever you see a question involving an instrumental variable (IV), your goal is to isolate a causal effect on a subgroup — specifically, the units whose behavior was actually changed by the instrument. This is called the Local Average Treatment Effect (LATE), or the effect on "compliers."
The IV formula is straightforward: divide the reduced-form effect (instrument's effect on the outcome) by the first-stage effect (instrument's effect on the treatment). Here, the instrument (reminder) increases adoption by 0.20 and raises weekly profit by $6. So the LATE is:
0.20$6=$30
This $30 represents the causal effect of system adoption on weekly profit for the stores that adopted because of the reminder — the compliers. Answer B is correct.
Answer A ($1.20) multiplies the two numbers instead of dividing them — a simple arithmetic reversal of the IV formula with no conceptual basis.
Answer C ($6) confuses the reduced-form estimate with the IV estimate. The $6 is the effect of the reminder on profit across all stores, not the effect of adoption on profit. It doesn't isolate the causal impact of the treatment itself.
Answer D ($0.20) confuses the first-stage coefficient — how much the reminder moved adoption — with the causal effect on profit. That's the wrong quantity entirely.
Study tip: Memorize the IV ratio as "outcome effect over treatment effect." When the numbers seem small, dividing (not multiplying) often yields a surprisingly large causal estimate — that's the whole point of scaling by compliance rate. - Which additional finding would most directly undermine the exclusion restriction for this instrument?
Answer: Employees assigned early receive a productivity template unavailable to late assignees, even when they do not attend
When evaluating an instrument in a two-stage least squares setup, you need to verify two core conditions: relevance (the instrument affects the treatment) and the exclusion restriction (the instrument affects the outcome only through the treatment, not through any other channel). This question zeroes in on the exclusion restriction.
For early assignment to be a valid instrument, it must influence productivity solely by changing webinar attendance — nothing else. Answer A directly violates this: if early assignees receive a productivity template regardless of whether they actually attend, then early assignment has an independent pathway to productivity that bypasses attendance entirely. This means the instrument is "leaking" into the outcome through a backdoor channel, which is precisely what the exclusion restriction forbids. A is the correct answer.
Answer B describes selection bias — higher-productivity employees self-selecting into attendance — but this is a concern about endogeneity in the original regression, not about whether the instrument affects outcomes through non-attendance channels. It actually motivates using an instrument, not undermining one.
Answer C describes treatment effect heterogeneity across departments (a smaller first-stage in sales vs. accounting). This is a concern about the instrument's strength in subgroups, but it doesn't suggest the instrument affects productivity except through attendance.
Answer D shows a raw correlation between attendance and productivity, which again reflects the endogeneity problem the IV design is meant to solve. It says nothing about whether early assignment has pathways to productivity beyond attendance.
Study tip: When a question asks what "undermines the exclusion restriction," look for a scenario where the instrument directly touches the outcome without going through the treatment variable — that's always the right target.
- What is the most defensible conclusion about the proposed IV analysis?
Answer: The instrument is likely weak, making the IV estimate unstable even if assignment is exogenous
When evaluating an instrumental variable (IV) design, you need to assess two separate conditions: exogeneity (is the instrument truly independent of confounders?) and instrument strength (does the instrument actually move the endogenous variable?). This question tests whether you can distinguish between these two criteria.
The key diagnostic for instrument strength is the first-stage F-statistic. The widely used rule of thumb is F>10; values below this suggest a weak instrument. Here, F=2.1 falls dramatically short of that threshold, meaning the prompt barely predicts feature activation. When an instrument is weak, IV estimates become highly unstable — they have inflated variance and can be severely biased toward the OLS estimate. This confirms B as the correct answer.
A is wrong because random assignment guarantees exogeneity, not strength. Randomization tells you the instrument is uncorrelated with confounders, but it says nothing about whether the instrument actually causes variation in the treatment variable. You can have a perfectly exogenous but completely useless instrument.
C confuses two distinct concepts. A near-zero first-stage coefficient signals weakness, not exclusion restriction violations. Exclusion would be violated if the prompt affected outcomes through a channel other than feature activation — something you can't read from the first-stage coefficient alone.
D misinterprets the weak-instrument problem as evidence of no causal effect. The IV estimate is simply unreliable here; you cannot draw conclusions about treatment effects from a broken first stage.
Study tip: Always check the first-stage F-statistic before trusting any IV result. Random assignment ≠ strong instrument — these are separate properties you must verify independently.
