Difference-in-Differences - Business Analytics

1. What are the model's predicted post-period outcome for a treated branch and its difference-in-differences estimate, respectively?
   Answer: A predicted outcome of $47$ and an estimated treatment effect of $-6$ Whenever you see a Difference-in-Differences (DiD) regression, recognize that the model uses indicator variables and their interaction to isolate a treatment effect. The standard setup is $Y = \beta_0 + \beta_1 T + \beta_2 P + \beta_3(T \times P)$, where $\beta_3$ is the DiD estimate — it captures the effect unique to treated units in the post-period, beyond any general time trend or baseline group difference. Here, the model is $Y = 40 + 8T + 5P - 6(T \times P)$. For a treated branch ($T = 1$) in the post-period ($P = 1$), plug in directly: $Y = 40 + 8(1) + 5(1) - 6(1 \times 1) = 40 + 8 + 5 - 6 = 47$. The DiD estimate is simply the coefficient on the interaction term, which is $-6$. That makes B correct — a predicted outcome of $47$ and a treatment effect of $-6$. Choice A reports $53$, which ignores the interaction term entirely ($40 + 8 + 5 = 53$), and incorrectly labels $\beta_1 = 8$ as the treatment effect. Choice C uses $45$ and attributes the time trend coefficient $\beta_2 = 5$ as the treatment effect — both errors. Choice D produces $39$ by misapplying signs and mistakes $-14$ as the effect, likely by incorrectly combining multiple coefficients. Your key takeaway: in a DiD regression, always look at the interaction term coefficient — that alone is the causal treatment estimate. Never confuse $\beta_1$ (treated vs. control baseline gap) or $\beta_2$ (pre-to-post time trend) with the actual treatment effect.
2. Assuming the parallel-trends condition is appropriate, what is the difference-in-differences estimate of the system's effect on weekly sales?
   Answer: An increase of $20$ units, after removing the untreated-store change Whenever you see a question involving a treated group and an untreated group measured before and after some intervention, you're dealing with difference-in-differences (DiD) — a method designed to isolate a true causal effect by stripping away trends that would have happened anyway. The core formula is: $\text{DiD} = (\bar{Y}_{treated,post} - \bar{Y}_{treated,pre}) - (\bar{Y}_{untreated,post} - \bar{Y}_{untreated,pre})$ Plugging in the numbers: the treated stores changed by $250 - 200 = 50$ units, and the untreated stores changed by $210 - 180 = 30$ units. The DiD estimate is $50 - 30 = 20$ units — making C correct. Those 30 units of growth in untreated stores represent background trends (seasonality, market conditions, etc.) that also affected treated stores. Removing them isolates the system's true effect. A is wrong because it reports only the untreated-store change ($+30$), which captures the background trend — not the treatment effect at all. B is wrong because it reports only the raw before-after change in treated stores ($+50$) without subtracting the counterfactual trend; this overstates the effect by conflating natural growth with the system's impact. D is wrong because it adds the two changes ($50 + 30 = 80$... or perhaps misreads as $70$) rather than subtracting them — a fundamental misapplication of the DiD logic. A useful memory anchor: DiD is always a subtraction of two changes, not an addition or a single change in isolation. If you find yourself reporting just one group's movement, you haven't finished the calculation.
3. How does the spillover affect the basic difference-in-differences estimate of the treated stores' sales effect?
   Answer: It produces an estimate of $8$ units and therefore overstates the effect by $3$ units. Whenever you see a difference-in-differences (DiD) question involving spillovers, your job is to trace exactly what the comparison group's trend looks like — because DiD uses that trend as a stand-in for what would have happened to treated stores absent the treatment. The DiD estimator works by taking the treated group's change minus the comparison group's change: $\hat{\tau} = \Delta Y_{\text{treated}} - \Delta Y_{\text{comparison}}$. In this scenario, treated stores rise by $+5$ units. The comparison stores, however, lose $3$ units due to customer spillover — customers migrating to the convenient rapid-delivery stores. Their "true" counterfactual change was $0$, but DiD observes $-3$. Plugging in: $\hat{\tau} = 5 - (-3) = 8$. The method thus overstates the true effect of $5$ by $3$ units, making B correct. The key intuition: spillover artificially depresses the comparison group, making the treated group look even better by comparison than it truly is. A gets the arithmetic backwards — subtracting $3$ from $5$ gives $2$, which would only apply if the comparison group rose by $3$, not fell. C is wrong because spillovers do not cancel — they corrupt the comparison group's trend, which is precisely what DiD relies on. D misunderstands the estimator entirely; DiD uses the difference between both groups' changes, not the comparison group's change alone. Study tip: When spillovers push the comparison group down, DiD overstates the effect; when they push it up, DiD understates it. Sketch the formula and plug in the direction of the spillover every time.
4. Which statement best describes the difference-in-differences conclusion?
   Answer: A level specification estimates $10$, while a proportional-growth specification estimates zero, because each embeds a different counterfactual assumption about how trends should be measured. Whenever you see a difference-in-differences question involving regions with different baseline values, your first instinct should be to ask: what does "parallel trends" actually mean here — parallel in levels or parallel in growth rates? That assumption is everything. Under a level specification, you assume the two regions would have grown by the same absolute dollar amount. The treated region gained $120 - 100 = 20$, while the comparison region gained $60 - 50 = 10$. The estimated treatment effect is $20 - 10 = 10$. Under a proportional-growth specification, you assume both regions would have grown by the same percentage. Both actually grew by $20\%$, so the counterfactual is perfectly matched — the estimated effect is $0$. Answer C captures this exactly: two different counterfactual assumptions produce two different numerical conclusions, neither of which is inherently "correct" without external justification. Answer A is wrong because the two specifications do not agree — identical percentage growth only eliminates the effect under the proportional model, not the level model. Answer B is wrong on two counts: the level estimate is $10$, not the same under both models, and claiming absolute dollars are the "only valid" basis is an unjustified assertion — proportional specifications are entirely legitimate in many contexts. Answer D reverses the results entirely — the level specification yields $10$ (not zero), and the proportional specification yields $0$ (not $10$). The key study tip: always identify which parallel-trends assumption a DiD model embeds. A level model assumes equal absolute trends; a log or proportional model assumes equal percentage trends. The same data can tell completely different causal stories depending on that choice.
5. Based only on these pre-implementation revenue patterns, which comparison division is more supportive of a difference-in-differences design?
   Answer: Division A, because its revenue change matches the treated division's change despite different starting levels Whenever you see a question about difference-in-differences (DiD), the critical concept to evaluate is parallel trends — the assumption that the treated and control groups would have followed the same trajectory (not necessarily the same levels) in the absence of treatment. DiD does not require equal starting points; it requires equal changes over time. Look at the pre-period revenue changes: the treated division rises by $\$10$ (from $100$ to $110$). Division A also rises by $\$10$ (from $80$ to $90$), matching that trend exactly despite starting at a different level. Division B rises by only $\$3$ (from $100$ to $103$), showing a clearly different trajectory even though its starting level matches the treated division. This makes A the correct answer. Division A exhibits the same pre-period change as the treated group, which is precisely the evidence you need to support the parallel trends assumption underlying a valid DiD design. Answer B is tempting but wrong — it confuses level matching with trend matching. Equal starting levels tell you nothing about whether two groups move in parallel. Answer C compounds this error by claiming that lower initial revenue "guarantees" comparable future growth, which is economically unfounded; initial levels don't determine trajectory. Answer D makes the same fundamental mistake as B, asserting that equal initial levels are sufficient for the counterfactual trend — they are not. Study tip: On DiD questions, always ask "do the changes match?" not "do the levels match?" Parallel trends is about slopes, not intercepts.
6. Why should the analyst be cautious when interpreting the difference-in-differences estimate as a change in individual customer spending?
   Answer: The treated sample's composition changed, so lower average spending may reflect new members rather than customer-level changes. Whenever you see a difference-in-differences (DiD) question, ask yourself: are we comparing apples to apples? DiD estimates a treatment effect by assuming that any change in the treated group's average outcome — beyond what the control group experienced — reflects the treatment itself. This assumption breaks down when the composition of the treated group changes between periods. Here, the store redesign attracted many new, low-spending members in the post-period. If average spending falls (or rises less than expected) in treated stores, that shift could simply reflect this influx of budget-conscious newcomers — not any change in how existing customers behave. The DiD estimate is picking up a compositional change, not a causal effect on individual spending. That's exactly why D is correct: the treated sample's composition changed, so you cannot confidently attribute differences in average spending to customer-level behavioral changes. A is wrong because DiD does not require equal store sizes or equal member counts at baseline — it requires parallel trends, not identical scales. Misreading the parallel-trends assumption as a size-balance requirement is a common trap. B overstates the problem. Enrollment changes don't automatically invalidate DiD — they introduce a specific interpretation hazard. The design can still be executed; the analyst just needs to be careful about what the estimate actually measures. C describes a made-up requirement. There is no rule that the comparison group must mirror treatment-group operational changes to maintain validity. Enforcing that would defeat the purpose of a control group. Study tip: On any DiD question, always check whether the who being measured stays consistent across periods. If group membership changes, averages shift for compositional reasons — and your estimate no longer cleanly isolates the treatment effect.
7. Which statement correctly interprets the difference-in-differences estimate?
   Answer: The program reduced churn by $3$ percentage points beyond the decline observed among nonparticipants. Whenever you see a difference-in-differences (DiD) question, your goal is to isolate the program's true causal effect by stripping out trends that would have happened anyway. The core formula is: $(Change_{participants}) - (Change_{nonparticipants})$. Here, participants fell from $12\%$ to $8\%$, a decline of $4$ percentage points. But nonparticipants also improved — from $10\%$ to $9\%$, a decline of $1$ percentage point. That $1$ pp decline reflects a background trend unrelated to the program (perhaps seasonal behavior or a market-wide shift). To find the program's net effect, you subtract the background trend: $4 - 1 = 3$ percentage points. This confirms B is correct — the program reduced churn by $3$ pp beyond what would have occurred naturally. A is tempting because $4$ pp is a real number from the data, but it ignores the counterfactual. Without subtracting the background trend, you're giving the program credit for changes it didn't cause. C compares post-period churn levels between the two groups ($8\%$ vs. $9\%$), which is a simple cross-sectional comparison — it ignores where each group started and conflates pre-existing differences with program effects. D adds the two declines ($4 + 1 = 5$), which has no logical basis in DiD methodology; you subtract the control group's change, you don't add it. Your study tip: always draw a quick two-by-two table (Before/After × Treatment/Control) and compute the DiD manually. The control group's change is your "would have happened anyway" baseline — never ignore it.
8. Which conclusion is most defensible from these results?
   Answer: The rising placebo estimates suggest a preexisting differential trend that weakens the causal interpretation. Whenever you see a difference-in-differences question involving placebo tests, your focus should be on whether the parallel-trends assumption holds — meaning treated and control groups were moving together before any intervention. Placebo estimates let you check this by running fake "treatments" in pre-intervention periods where the true effect should be zero. Here, the placebo treated-minus-control changes are $1$, $8$, and $15$ units across January, February, and March — a steadily climbing sequence. This pattern tells you the treated group was already pulling away from the control group before April, which is exactly what a preexisting differential trend looks like. If parallel trends held, these placebo estimates should hover near zero with no systematic direction. Because they don't, the April estimate of $20$ units cannot be cleanly attributed to the training program — some or all of it may simply be the continuation of that pre-existing gap. Answer C is therefore the most defensible conclusion. Answer A is tempting but logically flawed: placebo estimates being smaller than the April estimate doesn't validate anything. What matters is whether pre-period estimates are near zero, not merely smaller than the post-period number. Answer B invents a mechanical subtraction rule ($20 - 15 = 5$) that has no basis in DiD methodology — you don't adjust by the last placebo figure alone. Answer D misreads what "parallel trends confirmed" would actually require; the placebo estimates not equaling the April figure is irrelevant — they need to be close to zero. As a study tip: when evaluating DiD validity, always ask "are the pre-treatment placebo estimates near zero and stable?" A rising or falling trend in pre-period gaps is a red flag, regardless of the post-treatment estimate's magnitude.
9. What is the most important consequence of the competitor closures for the difference-in-differences analysis?
   Answer: They undermine identification because their sales effect cannot be separated from the initiative's differential effect. Whenever you see a difference-in-differences (DiD) question, your central concern should be the parallel trends assumption: in the absence of the treatment, both groups would have followed the same trajectory. DiD estimates the treatment effect by calculating $(\bar{Y}_{treated,post} - \bar{Y}_{treated,pre}) - (\bar{Y}_{control,post} - \bar{Y}_{control,pre})$. This math only isolates the initiative's impact if no other differential shock hits one group but not the other during the study window. That's exactly what the competitor closures represent — a differential shock. They affect participating regions but not comparison regions, so any sales bump they generate gets folded into the post-period difference. You can't tell whether the sales increase came from the delivery initiative, the reduced competition, or some combination. D is correct because the closures' effect and the initiative's effect are perfectly confounded; they cannot be disentangled from the DiD estimate alone. A is wrong because DiD does not automatically purge every concurrent event — it only removes shocks that affect both groups equally. A region-specific event is precisely what breaks the design. B is wrong because the parallel trends assumption is about trends (equal slopes over time), not identical pre-period levels; different baseline sales are perfectly acceptable. C is wrong and represents a tempting trap: a larger post-period gap makes the initiative look more effective, but that's the problem, not a benefit — inflated differences produce biased, not improved, estimates. When reviewing quasi-experimental designs on your exam, always ask: Did anything else change for one group but not the other? If yes, identification is threatened.
10. What effect will the basic difference-in-differences calculation estimate under these conditions?
    Answer: An effect of $6$ units, understating the July effect because June is already affected Whenever you see a difference-in-differences (DiD) question, your job is to track what the estimator actually measures — not what the researcher intended to measure. DiD computes: $(Y_{treated,post} - Y_{treated,pre}) - (Y_{control,post} - Y_{control,pre})$. The pre-period is supposed to be "clean," but here it isn't. Because customers anticipate the campaign, treated-market sales are already elevated by $4$ units in June (the pre period). In July, they're elevated by $10$ units. The DiD estimator sees a treated-market increase of $10 - 4 = 6$ units from pre to post, and subtracts zero from the control side (controls are unaffected in both periods). So DiD estimates **$6$ units** — which is answer A. This understates the true July effect of $10$ units because the baseline (June) is already contaminated by anticipatory purchasing. Answer B is wrong because DiD cannot "see through" the corrupted pre-period; it mechanically differences whatever values exist in pre and post. Answer C would only be correct if DiD added the anticipation effect rather than subtracted it — but since June's elevation reduces the measured pre-to-post jump, the estimate goes down, not up. Answer D confuses the estimator's output with the size of the anticipation effect itself; $4$ units is what leaked into June, not what DiD reports. Study tip: Always ask whether the pre-period is truly unaffected. Anticipation effects, leakage, or pre-treatment contamination all bias DiD downward by inflating the baseline — a classic trap on business-analytics exams.

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