Appendix — Solutions — Problem Set 4.2 (Goodman-Bacon by Hand, and the Negative-Weights Crisis)

Full worked solutions to book/weeks/week-04/ps4.2.md, covering Chapter 4.2. Notation follows the Conventions: TWFE regression Y_{it} = \alpha_i + \lambda_t + \beta D_{it} + \varepsilon_{it}; absorbing staggered treatment D_{it} = \mathbf{1}\{t \ge G_i\} with cohort G_i (the period unit i first switches on, G_i = \infty for never-treated); genuine cell-level effect \text{ATT}_{it}; group-time effect \text{ATT}(g,t); event time e = t - g. The recurring theme of the key: under staggered timing with dynamic effects, the pooled \hat\beta is an exact weighted average of 2×2 DiDs (Goodman-Bacon) or of cell-level effects (de Chaisemartin–D’Haultfœuille), and the forbidden “later-vs-already-treated” comparison contaminates it; the cure is clean controls + transparent aggregation, implemented three ways by Callaway–Sant’Anna, Sun–Abraham, and Borusyak–Jaravel–Spiess.

The working world (carried across Problems 1–5): States E (G_E = 2), L (G_L = 4), U (never); years t = 1, \dots, 5; per-period effect \text{ATT}_{it} = -(e+1) with e = t - G_i; untreated potential outcome = 10 throughout (parallel trends holds perfectly). Realized Y_{it}:

t	E	L	U
1	10	10	10
2	9	10	10
3	8	10	10
4	7	9	10
5	6	8	10

The pooled TWFE coefficient on these 15 cells is \hat\beta^{\text{TWFE}} = -1.25 (given; reconstructed exactly in Problems 3 and 4). The true overall ATT — the average of all six treated cells’ effects (-1,-2,-3,-4,-1,-2) — is -13/6 \approx -2.17. Every arithmetic result below was verified in python3 (statsmodels TWFE; exact-fraction weight algebra).

Problem 1 — Why TWFE is biased: name the forbidden comparison (14 pts)

(a) [4 pts] Clean comparison between E and L: the window years 1–3, before L adopts. In years 1–3 State L is still untreated (D_{Lt} = 0 for t < 4), so L is a legitimate clean control for the early adopter E. Here L is the control (untreated-in-window) and E is the treated unit. This is a Goodman-Bacon Type-2 (“earlier-vs-later, before the later switches on”) comparison.

Forbidden comparison for L’s effect: the window years 4–5, after E has adopted. When L switches on in year 4, the TWFE regression needs a unit whose status did not change — and across years 4–5 the only other state besides the never-treated U is State E, which is already treated (D_{Et} = 1 since year 2). So E is wrongly pressed into service as the control for newly-treated L. E is contaminated because it is carrying its own treatment effect throughout the window — it is not a clean counterfactual for “what L would have done untreated.”

(b) [4 pts] Mechanism. A 2×2 DiD attributes to the treated unit (L) the change in L’s outcome minus the change in the control’s outcome over the window. When the control is already-treated E, the “change in E’s outcome over years 4–5” is not zero baseline drift — it is the change in the already-treated unit’s effect over the window. E’s per-period effect is still deepening, going from -2 at t=3 toward -3 at t=4 and -4 at t=5 — its outcome is falling fast for reasons that have nothing to do with L. The forbidden 2×2 therefore estimates L’s true effect minus the change in E’s still-growing effect. Because E is sliding downward faster than the freshly-treated L, L looks like it is rising relative to E, and the differenced quantity flips positive — a real treatment effect (E’s) masquerading as a counterfactual trend and getting subtracted from the thing we want.

(c) [4 pts] Two rescues, either one suffices:

No staggered timing (one common adoption date for all treated units). Then there are no already-treated units available to misuse as controls during anyone else’s switch-on — the forbidden comparison cannot be formed because no unit is treated before another’s adoption date. (This rescue removes the contaminated controls entirely.)
Homogeneous (constant) treatment effects — the same constant effect for every unit at every horizon. Then even when already-treated E is used as a control, the “change in E’s effect over the window” is zero (a constant does not change), so the contamination it injects vanishes and the forbidden 2×2 returns the right thing. (This rescue makes the contamination cancel.)

(d) [2 pts] Priya’s real problem has a treatment effect that builds over time (re-underwriting is slow, so disclosure bites harder in year three than year one) — a dynamic / heterogeneous-across-event-time effect, which violates rescue 2. The working world violates both rescues at once: timing is staggered (G_E = 2 \ne 4 = G_L, violating rescue 1) and the effect builds, -(e+1) growing in |e| (violating rescue 2). So it is the genuine danger case — exactly the recipe for the crisis.

Problem 2 — The four kinds of 2×2 and their values (18 pts)

All cell means read straight from the table.

(a) [6 pts] Treated-vs-never-treated (clean, Type 1).

(A) E vs U. Pre = \{1\}, post = \{2,3,4,5\}. \bar Y_{E,\text{post}} = \tfrac{9+8+7+6}{4} = 7.5,\quad \bar Y_{E,\text{pre}} = 10,\quad \bar Y_{U,\text{post}} = 10,\quad \bar Y_{U,\text{pre}} = 10. \widehat{\text{DiD}}_A = (7.5 - 10) - (10 - 10) = \mathbf{-2.5}.

(B) L vs U. Pre = \{1,2,3\}, post = \{4,5\}. \bar Y_{L,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{L,\text{pre}} = 10,\quad \bar Y_{U,\text{post}} = 10,\quad \bar Y_{U,\text{pre}} = 10. \widehat{\text{DiD}}_B = (8.5 - 10) - (10 - 10) = \mathbf{-1.5}.

Both are clean: U is genuinely untreated throughout, so each DiD is an honest estimate of the average treated-period effect for that cohort (E’s average effect over e=0,1,2,3 is -2.5; L’s average over e=0,1 is -1.5 — exactly the truth).

(b) [4 pts] Early-vs-late, before late adopts (clean, Type 2).

(C) E (treated) vs L (control). Pre = \{1\}, post = \{2,3\}. \bar Y_{E,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{E,\text{pre}} = 10,\quad \bar Y_{L,\text{post}} = 10,\quad \bar Y_{L,\text{pre}} = 10. \widehat{\text{DiD}}_C = (8.5 - 10) - (10 - 10) = \mathbf{-1.5}. Why L is a legitimate control here: in years 1–3 L has not yet adopted (t < G_L = 4), so D_{Lt} = 0 — L is not-yet-treated and therefore untreated throughout this window. A not-yet-treated unit is a clean control as long as the window ends before its own adoption.

(c) [4 pts] Late-vs-early, after early adopts (FORBIDDEN, Type 3).

(D) L (treated) vs E (control). Pre = \{2,3\}, post = \{4,5\}. \bar Y_{L,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{L,\text{pre}} = \tfrac{10+10}{2} = 10, \bar Y_{E,\text{post}} = \tfrac{7+6}{2} = 6.5,\quad \bar Y_{E,\text{pre}} = \tfrac{9+8}{2} = 8.5. \widehat{\text{DiD}}_D = (8.5 - 10) - (6.5 - 8.5) = (-1.5) - (-2.0) = \mathbf{+0.5}. Positive — even though disclosure lowered non-renewals in every treated cell. The driver: across the window State E’s outcome drops by 2.0 (8.5 \to 6.5), because E’s own treatment effect is still deepening (-2 \to -4). L’s outcome drops by only 1.5. So differencing L against the faster-falling already-treated E makes L look like it rose, and the 2×2 flips positive. The forbidden comparison subtracts E’s still-growing effect from L’s.

(d) [4 pts] Side by side:

2×2	treated	control	window	control status	DiD	clean / forbidden
A	E	U	\{1\}\!\to\!\{2,3,4,5\}	never-treated	-2.5	clean
B	L	U	\{1,2,3\}\!\to\!\{4,5\}	never-treated	-1.5	clean
C	E	L	\{1\}\!\to\!\{2,3\}	not-yet-treated (clean in window)	-1.5	clean
D	L	E	\{2,3\}\!\to\!\{4,5\}	already-treated	+0.5	forbidden

The entire source of bias is comparison D: it alone uses an already-treated unit (E) as the control. Its +0.5 pulls against the three negative clean DiDs. With enough weight on D (positive while the truth is negative), it drags \hat\beta toward zero, and — given enough weight, as in the chapter’s two-state world — past zero into the wrong sign.

Problem 3 — The Goodman-Bacon weights, and TWFE as a weighted average (22 pts)

(a) [8 pts] Plug \bar D_E = 4/5, \bar D_L = 2/5 into the four (unnormalized) weight expressions.

s_A \propto \bar D_E(1-\bar D_E) = \tfrac45\cdot\tfrac15 = \tfrac{4}{25}. s_B \propto \bar D_L(1-\bar D_L) = \tfrac25\cdot\tfrac35 = \tfrac{6}{25}. s_C \propto (1-\bar D_L)^2\cdot\frac{\bar D_E - \bar D_L}{1-\bar D_L}\cdot\frac{1-\bar D_E}{1-\bar D_L} = (\bar D_E - \bar D_L)(1-\bar D_E) = \big(\tfrac45-\tfrac25\big)\big(\tfrac15\big) = \tfrac25\cdot\tfrac15 = \tfrac{2}{25}. s_D \propto \bar D_E^{\,2}\cdot\frac{\bar D_L}{\bar D_E}\cdot\frac{\bar D_E - \bar D_L}{\bar D_E} = \bar D_L(\bar D_E - \bar D_L) = \tfrac25\cdot\big(\tfrac45-\tfrac25\big) = \tfrac25\cdot\tfrac25 = \tfrac{4}{25}.

Sum: S = \dfrac{4 + 6 + 2 + 4}{25} = \dfrac{16}{25}. Normalize (w_k = s_k/S):

w_A = \frac{4/25}{16/25} = \frac{4}{16} = \tfrac14 = 0.250,\qquad w_B = \frac{6}{16} = \tfrac38 = 0.375, w_C = \frac{2}{16} = \tfrac18 = 0.125,\qquad w_D = \frac{4}{16} = \tfrac14 = 0.250.

Check: 0.250 + 0.375 + 0.125 + 0.250 = 1.000. ✓

(b) [6 pts] Reconstruct \hat\beta as \sum_k w_k\,\widehat{\text{DiD}}_k using Problem-2 values (-2.5, -1.5, -1.5, +0.5): \hat\beta = \underbrace{\tfrac14(-2.5)}_{-0.625} + \underbrace{\tfrac38(-1.5)}_{-0.5625} + \underbrace{\tfrac18(-1.5)}_{-0.1875} + \underbrace{\tfrac14(+0.5)}_{+0.125}. Sum: -0.625 - 0.5625 - 0.1875 + 0.125 = \mathbf{-1.25}. ✓ Exactly the pooled \hat\beta^{\text{TWFE}} — this is Goodman-Bacon’s identity, an exact equality with no error term. (In fractions: -\tfrac58 - \tfrac9{16} - \tfrac3{16} + \tfrac18 = -\tfrac{20}{16} = -\tfrac54.)

(c) [4 pts] Reading the weights as a diagnostic. (i) The largest weight is w_B = 3/8 on the clean L-vs-never comparison — but note the forbidden comparison D carries a hefty w_D = 1/4, tied for second and equal to the clean A. The weighting is driven purely by treatment-timing variance, not by trustworthiness. (ii) Total weight on the forbidden comparison: w_D = 0.25. Its signed contribution is w_D \cdot \widehat{\text{DiD}}_D = 0.25 \times (+0.5) = +0.125. The true overall ATT is -13/6 \approx -2.17, but \hat\beta = -1.25 — attenuated toward zero by about 0.92 (exactly -13/6-(-5/4)=-11/12\approx-0.917). The forbidden term contributes +0.125 directly, and (more importantly) it forces the clean comparisons to be the averages over treated periods -2.5 and -1.5 rather than the deeper truth; the net effect is that \hat\beta understates the true effect by a wide margin even though, here, the sign survives.

(d) [4 pts] Delete U. With only States E and L, the pair (E, L) is the only pair, so the treated-vs-never blocks A and B vanish; only the within-pair sub-comparisons C and D remain. Renormalize over \{s_C, s_D\} = \{2/25, 4/25\}: w_C = \frac{2/25}{6/25} = \tfrac13,\qquad w_D = \frac{4/25}{6/25} = \tfrac23. \hat\beta = \tfrac13(-1.5) + \tfrac23(+0.5) = -0.5 + 0.333\overline{3} = \mathbf{-\tfrac16} \approx -0.167. (Verified directly against a TWFE regression on the two-state, five-year panel: -0.1\overline{6}.) The situation is strictly worse: removing the clean never-treated control U strips out the two clean treated-vs-never blocks, so the forbidden comparison’s weight jumps from 1/4 to 2/3 — it now dominates the average. The estimate collapses from -1.25 to -0.167, almost on top of zero. Lengthen the horizon (the chapter’s eight-year version, G_E = 2, G_L = 5, t = 1,\dots,8) and the forbidden comparison’s positive contamination grows enough to push \hat\beta all the way to +0.40 — a full sign flip. Losing the never-treated unit is precisely the condition that lets the forbidden comparison become the only game in town for the late cohort, which is what completes the disaster.

Problem 4 — The negative-weights view: de Chaisemartin–D’Haultfœuille (16 pts)

(a) [4 pts] Weights sum to one: 0.25 + 0.25 + (-0.0625) + (-0.0625) + 0.3125 + 0.3125 = 1.0000.\;\checkmark Weighted average of cell effects: \sum w_{it}\text{ATT}_{it} = 0.25(-1) + 0.25(-2) + (-0.0625)(-3) + (-0.0625)(-4) + 0.3125(-1) + 0.3125(-2). Term by term: -0.25 - 0.50 + 0.1875 + 0.25 - 0.3125 - 0.625 = \mathbf{-1.25}. ✓ The same \hat\beta^{\text{TWFE}}, now reconstructed a third way (after the by-hand TWFE and the Goodman-Bacon 2×2 average). One number, three identical decompositions.

(b) [5 pts] The negative weights are w = -0.0625 on cells 3 and 4: State E in years 4 and 5, which are E’s event-time e = 2 and e = 3 cells — i.e., the early cohort’s late-period cells, the part of E’s treated history that overlaps L’s treated window. Bridge to Problem 2: these are exactly the cells where already-treated E served as the contaminated control in the forbidden Type-3 comparison D. In the Goodman-Bacon view, D used E’s years 4–5 as L’s control; in the de Chaisemartin–D’Haultfœuille view, those same cells receive negative cell weights. The two decompositions are the same disease seen through two lenses: pairing \to a forbidden 2×2; cell-by-cell \to a negative weight on the cells doing the forbidden control duty.

(c) [4 pts] The dCDH warning. Because all six \text{ATT}_{it} are strictly negative but two weights are negative, the weighted sum is not a sensible average of the effects — and in principle the sign of \hat\beta can be opposite to the sign of every individual effect. A weighted average with negative weights is not bounded between the min and max of the things it averages. Made concrete by the chapter’s neighbor world (eight years, no never-treated state): there every true cell effect is negative (disclosure helps everyone, every year), yet \hat\beta = +0.40 — the estimate says the policy raised non-renewals. All true effects negative; estimate positive.

(d) [3 pts] The diagnostic. Because w_{it} depends only on the design — who is treated when — and not at all on the (unknown) treatment effects, the researcher can compute every weight from the treatment-assignment pattern alone, before estimating a single effect. She counts how many weights are negative and how much total negative weight there is; if a meaningful share is negative, \hat\beta is uninterpretable and she should not report it. The ordering matters: computing weights first (from design) and effects second makes this a genuine pre-commitment check — she cannot be accused of fishing for a decomposition that excuses a result she already saw, because the weights were fixed by the adoption calendar before any outcome entered the calculation.

Problem 5 — Callaway–Sant’Anna: clean ATT(g,t) and event-time aggregation (18 pts)

(a) [4 pts] Meaning of the arguments. \text{ATT}(g,t) is the average treatment effect, at calendar time t, on the cohort that first adopted in year g (i.e., all units with G_i = g). The first argument g says which group (defined by its adoption year); the second t says when you are measuring. Symbolically, \text{ATT}(g,t) = \mathbb{E}\big[\,Y_{it}(g) - Y_{it}(\infty)\ \big|\ G_i = g\,\big], the expected gap, for the cohort-g units, between their realized (treated-from-g) outcome and their never-treated potential outcome, at time t. Event time is e = t - g (years since adoption); e = 0 is the first treated year. Eligible clean controls for cohort g at time t: units that are never-treated (G_i = \infty) or not-yet-treated at t (those with G_i > t, still untreated through the whole comparison window). Forbidden: any already-treated unit, i.e. any unit with g' \le t and g' \ne g — in particular an earlier cohort.

(b) [8 pts] The clean group-time grid. Baseline period for cohort g is g - 1.

Cohort E (g = 2), control = U (never), baseline t = 1: \widehat{\text{ATT}}(2,2) = (Y_{E,2} - Y_{E,1}) - (Y_{U,2} - Y_{U,1}) = (9-10) - (10-10) = \mathbf{-1}\quad(e=0,\ \text{true } -1) \widehat{\text{ATT}}(2,3) = (8-10) - (10-10) = \mathbf{-2}\quad(e=1,\ \text{true } -2) \widehat{\text{ATT}}(2,4) = (7-10) - (10-10) = \mathbf{-3}\quad(e=2,\ \text{true } -3) \widehat{\text{ATT}}(2,5) = (6-10) - (10-10) = \mathbf{-4}\quad(e=3,\ \text{true } -4) (For t = 2, 3 you may instead use the not-yet-treated L as control — Y_{L,t} = 10 there — and get the identical answer, since L is still untreated before year 4.)

Cohort L (g = 4), control = U (never), baseline t = 3 — never the already-treated E: \widehat{\text{ATT}}(4,4) = (Y_{L,4} - Y_{L,3}) - (Y_{U,4} - Y_{U,3}) = (9-10) - (10-10) = \mathbf{-1}\quad(e=0,\ \text{true } -1) \widehat{\text{ATT}}(4,5) = (8-10) - (10-10) = \mathbf{-2}\quad(e=1,\ \text{true } -2)

Every clean group-time estimate hits the true effect exactly, because each is a Type-1 (or Type-2) clean DiD against a genuinely untreated control — no forbidden Type-3 comparison is ever formed, so there is no contamination to bias the estimate. This is the unbiasedness TWFE lacked.

(c) [4 pts] Event-time aggregation e = t - g (equal cohort sizes → simple averages across cohorts sharing an e): \widehat{\text{ATT}}^{\text{es}}(0) = \tfrac{(-1) + (-1)}{2} = -1,\quad \widehat{\text{ATT}}^{\text{es}}(1) = \tfrac{(-2) + (-2)}{2} = -2, \widehat{\text{ATT}}^{\text{es}}(2) = -3\ (\text{only E}),\quad \widehat{\text{ATT}}^{\text{es}}(3) = -4\ (\text{only E}). Overall ATT (simple average of all six group-time effects): \frac{(-1) + (-2) + (-3) + (-4) + (-1) + (-2)}{6} = \frac{-13}{6} \approx \mathbf{-2.17}. Exactly the truth. Contrast with the broken pooled \hat\beta^{\text{TWFE}} = -1.25: the clean estimator is right (-2.17); TWFE got the sign right here but attenuated the magnitude by about 40%, understating how much the disclosure rule helped. (And in the no-never-treated world TWFE got the sign wrong entirely.)

(d) [2 pts] In the two-state world (E, L only, no U), Callaway–Sant’Anna reports \widehat{\text{ATT}}(4, t) for State L as not identified / undefined — it refuses to compute it, because L’s only available comparison unit is the already-treated E, and the method forbids using an already-treated unit as a control. This refusal is a feature: when no clean counterfactual exists, the honest answer is “this effect is not identified,” not a fabricated number. TWFE, by contrast, did produce a number from the same two states (-0.167, nearly flipped) by silently forming the forbidden comparison — manufacturing an answer where the data contain none.

Problem 6 — Which estimator, and diagnosing a contaminated event study (12 pts)

(a) [3 pts] Sun–Abraham (2021) — the interaction-weighted (IW) estimator. It stays inside a single event-study regression, so it changes the least code. The mechanism: instead of one coefficient \beta_e per relative-time dummy, saturate the regression by interacting every relative-time dummy with every cohort indicator, estimating a separate coefficient \delta_{g,e} for each (cohort g, event-time e) pair against never-treated (or last-treated) controls, then aggregate the \delta_{g,e} to event-time effects with cohort-share weights (the “interaction weighting”). Because each cohort’s dynamics are estimated separately before averaging, no cohort’s effect at one event time can leak into another cohort’s coefficient at a different event time — the cohort bleed is shut off.

(b) [3 pts] Borusyak–Jaravel–Spiess (2024) — the imputation estimator, which they show is (under their assumptions) the efficient one. Three steps: (1) fit the two-way FE model Y_{it} = \alpha_i + \lambda_t + \varepsilon_{it} using only untreated cells (D_{it} = 0: all never-treated cells plus every adopter’s pre-adoption years); (2) impute each treated cell’s missing untreated outcome \hat Y_{it}(0) = \hat\alpha_i + \hat\lambda_t; (3) difference \hat\tau_{it} = Y_{it} - \hat Y_{it}(0) and average the \hat\tau_{it} with explicit weights. The \hat\alpha_i, \hat\lambda_t are uncontaminated because the treated cells are excluded from the fit — no treatment effect ever enters the estimation of the fixed effects that serve as the counterfactual, which is exactly what pooled TWFE failed to do (it fit on all cells, letting treated cells corrupt the FE that double as everyone’s control). Its pre-trend test is built from the untreated residuals, so it is not contaminated.

(c) [4 pts] Diagnosis. Priya is not seeing a real parallel-trends violation — she is seeing Sun–Abraham contamination of the naive event study. Under staggered timing with heterogeneous/dynamic effects, each estimated pre-period coefficient \hat\beta_e in a naive TWFE event study is polluted by treatment effects from other event times of other cohorts — the leads and lags bleed into one another through the same forbidden later-vs-already-treated comparisons. A coefficient nominally at e = -2 can pick up some other cohort’s e = +1 effect, manufacturing a slope in the pre-periods even when the true pre-trends are dead flat. So her “funny pre-trends” are an artifact of the estimator, not evidence her design is broken. What she should run: a heterogeneity-robust event study — Sun–Abraham IW, Callaway–Sant’Anna aggregated by event time, or Borusyak–Jaravel–Spiess — each of which estimates cohort dynamics in isolation against clean controls. What the corrected plot should show: if parallel trends really holds, the pre-period coefficients (e < 0) should sit near zero (a genuine placebo/pre-trend check), and only the post-period coefficients should trace the building disclosure effect.

(d) [2 pts] Spec-discipline upgrade (Conventions §4, extended). A staggered-DiD write-up must now state two choices a plain 2×2 did not need: (1) name the control group — are the clean comparisons against never-treated units, not-yet-treated units, or both (this matters because never-adopters may differ systematically, while not-yet-treated adopters are often a more credible counterfactual but shrink the control pool as cohorts switch on); and (2) name the aggregation weights — event-time average, calendar-time average, or a single overall ATT, and how cohorts were weighted into the headline number. The identifying assumption is parallel trends stated per cohort: each adopting cohort’s untreated potential outcome would have moved parallel to its clean control group’s, in every comparison window.

End of solutions for Problem Set 4.2. Three independent decompositions of the same pooled \hat\beta = -1.25 — by-hand TWFE, the Goodman-Bacon 2×2 average (weights \tfrac14,\tfrac38,\tfrac18,\tfrac14 on DiDs -2.5, -1.5, -1.5, +0.5), and the de Chaisemartin–D’Haultfœuille cell-weight sum (two weights negative) — all land on the identical number, and all trace the bias to one culprit: the forbidden later-vs-already-treated comparison (+0.5, the only positive piece). The Callaway–Sant’Anna clean grid recovers the true -13/6 \approx -2.17 exactly. Goodman-Bacon (2021), de Chaisemartin and D’Haultfœuille (2020), Sun and Abraham (2021), Callaway and Sant’Anna (2021), and Borusyak, Jaravel, and Spiess (2024) are four diagnostics and three cures for one disease.

# Solutions — Problem Set 4.2 (Goodman-Bacon by Hand, and the Negative-Weights Crisis) Full worked solutions to `book/weeks/week-04/ps4.2.md`, covering Chapter 4.2. Notation follows the Conventions: TWFE regression $Y_{it} = \alpha_i + \lambda_t + \beta D_{it} + \varepsilon_{it}$; absorbing staggered treatment $D_{it} = \mathbf{1}\{t \ge G_i\}$ with cohort $G_i$ (the period unit $i$ first switches on, $G_i = \infty$ for never-treated); genuine cell-level effect $\text{ATT}_{it}$; group-time effect $\text{ATT}(g,t)$; event time $e = t - g$. The recurring theme of the key: **under staggered timing with dynamic effects, the pooled $\hat\beta$ is an exact weighted average of 2×2 DiDs (Goodman-Bacon) or of cell-level effects (de Chaisemartin–D'Haultfœuille), and the forbidden "later-vs-already-treated" comparison contaminates it; the cure is clean controls + transparent aggregation, implemented three ways by Callaway–Sant'Anna, Sun–Abraham, and Borusyak–Jaravel–Spiess.** **The working world (carried across Problems 1–5):** States E ($G_E = 2$), L ($G_L = 4$), U (never); years $t = 1, \dots, 5$; per-period effect $\text{ATT}_{it} = -(e+1)$ with $e = t - G_i$; untreated potential outcome $= 10$ throughout (parallel trends holds perfectly). Realized $Y_{it}$: | $t$ | E | L | U | |:---:|:---:|:---:|:---:| | 1 | 10 | 10 | 10 | | 2 | 9 | 10 | 10 | | 3 | 8 | 10 | 10 | | 4 | 7 | 9 | 10 | | 5 | 6 | 8 | 10 | The pooled TWFE coefficient on these 15 cells is $\hat\beta^{\text{TWFE}} = -1.25$ (given; reconstructed exactly in Problems 3 and 4). The true overall ATT — the average of all six treated cells' effects $(-1,-2,-3,-4,-1,-2)$ — is $-13/6 \approx -2.17$. Every arithmetic result below was verified in `python3` (statsmodels TWFE; exact-fraction weight algebra). --- ## Problem 1 — Why TWFE is biased: name the forbidden comparison (14 pts) **(a)** [4 pts] **Clean comparison** between E and L: the window **years 1–3**, before L adopts. In years 1–3 State L is still untreated ($D_{Lt} = 0$ for $t < 4$), so L is a *legitimate* clean control for the early adopter E. Here **L is the control** (untreated-in-window) and E is the treated unit. This is a Goodman-Bacon Type-2 ("earlier-vs-later, before the later switches on") comparison. **Forbidden comparison** for L's effect: the window **years 4–5**, after E has adopted. When L switches on in year 4, the TWFE regression needs a unit whose status did not change — and across years 4–5 the only other state besides the never-treated U is **State E, which is already treated** ($D_{Et} = 1$ since year 2). So E is **wrongly pressed into service as the control for newly-treated L**. E is contaminated because it is carrying its *own* treatment effect throughout the window — it is not a clean counterfactual for "what L would have done untreated." **(b)** [4 pts] **Mechanism.** A 2×2 DiD attributes to the treated unit (L) the *change* in L's outcome minus the *change* in the control's outcome over the window. When the control is already-treated E, the "change in E's outcome over years 4–5" is not zero baseline drift — it is the **change in the already-treated unit's effect over the window**. E's per-period effect is *still deepening*, going from $-2$ at $t=3$ toward $-3$ at $t=4$ and $-4$ at $t=5$ — its outcome is falling fast for reasons that have nothing to do with L. The forbidden 2×2 therefore estimates *L's true effect minus the change in E's still-growing effect*. Because E is sliding downward faster than the freshly-treated L, L looks like it is *rising relative to E*, and the differenced quantity flips positive — a real treatment effect (E's) masquerading as a counterfactual trend and getting subtracted from the thing we want. **(c)** [4 pts] **Two rescues, either one suffices:** 1. **No staggered timing** (one common adoption date for all treated units). Then there are *no already-treated units* available to misuse as controls during anyone else's switch-on — the forbidden comparison cannot be formed because no unit is treated before another's adoption date. (This rescue *removes the contaminated controls entirely.*) 2. **Homogeneous (constant) treatment effects** — the same constant effect for every unit at every horizon. Then even when already-treated E is used as a control, the "change in E's effect over the window" is **zero** (a constant does not change), so the contamination it injects vanishes and the forbidden 2×2 returns the right thing. (This rescue *makes the contamination cancel.*) **(d)** [2 pts] Priya's real problem has a treatment effect that **builds over time** (re-underwriting is slow, so disclosure bites harder in year three than year one) — a **dynamic / heterogeneous-across-event-time effect**, which violates rescue 2. The working world violates **both** rescues at once: timing is staggered ($G_E = 2 \ne 4 = G_L$, violating rescue 1) *and* the effect builds, $-(e+1)$ growing in $|e|$ (violating rescue 2). So it is the genuine danger case — exactly the recipe for the crisis. --- ## Problem 2 — The four kinds of 2×2 and their values (18 pts) All cell means read straight from the table. **(a)** [6 pts] **Treated-vs-never-treated (clean, Type 1).** **(A) E vs U.** Pre $= \{1\}$, post $= \{2,3,4,5\}$. $$\bar Y_{E,\text{post}} = \tfrac{9+8+7+6}{4} = 7.5,\quad \bar Y_{E,\text{pre}} = 10,\quad \bar Y_{U,\text{post}} = 10,\quad \bar Y_{U,\text{pre}} = 10.$$ $$\widehat{\text{DiD}}_A = (7.5 - 10) - (10 - 10) = \mathbf{-2.5}.$$ **(B) L vs U.** Pre $= \{1,2,3\}$, post $= \{4,5\}$. $$\bar Y_{L,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{L,\text{pre}} = 10,\quad \bar Y_{U,\text{post}} = 10,\quad \bar Y_{U,\text{pre}} = 10.$$ $$\widehat{\text{DiD}}_B = (8.5 - 10) - (10 - 10) = \mathbf{-1.5}.$$ Both are clean: U is genuinely untreated throughout, so each DiD is an honest estimate of the average treated-period effect for that cohort (E's average effect over $e=0,1,2,3$ is $-2.5$; L's average over $e=0,1$ is $-1.5$ — exactly the truth). **(b)** [4 pts] **Early-vs-late, before late adopts (clean, Type 2).** **(C) E (treated) vs L (control).** Pre $= \{1\}$, post $= \{2,3\}$. $$\bar Y_{E,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{E,\text{pre}} = 10,\quad \bar Y_{L,\text{post}} = 10,\quad \bar Y_{L,\text{pre}} = 10.$$ $$\widehat{\text{DiD}}_C = (8.5 - 10) - (10 - 10) = \mathbf{-1.5}.$$ **Why L is a legitimate control here:** in years 1–3 L has not yet adopted ($t < G_L = 4$), so $D_{Lt} = 0$ — L is *not-yet-treated* and therefore untreated *throughout this window*. A not-yet-treated unit is a clean control as long as the window ends before its own adoption. **(c)** [4 pts] **Late-vs-early, after early adopts (FORBIDDEN, Type 3).** **(D) L (treated) vs E (control).** Pre $= \{2,3\}$, post $= \{4,5\}$. $$\bar Y_{L,\text{post}} = \tfrac{9+8}{2} = 8.5,\quad \bar Y_{L,\text{pre}} = \tfrac{10+10}{2} = 10,$$ $$\bar Y_{E,\text{post}} = \tfrac{7+6}{2} = 6.5,\quad \bar Y_{E,\text{pre}} = \tfrac{9+8}{2} = 8.5.$$ $$\widehat{\text{DiD}}_D = (8.5 - 10) - (6.5 - 8.5) = (-1.5) - (-2.0) = \mathbf{+0.5}.$$ **Positive** — even though disclosure lowered non-renewals in every treated cell. The driver: across the window State E's outcome drops by $2.0$ ($8.5 \to 6.5$), because **E's own treatment effect is still deepening** ($-2 \to -4$). L's outcome drops by only $1.5$. So differencing L against the faster-falling already-treated E makes L look like it *rose*, and the 2×2 flips positive. The forbidden comparison subtracts E's still-growing effect from L's. **(d)** [4 pts] **Side by side:** | 2×2 | treated | control | window | control status | DiD | clean / forbidden | |:---:|:---:|:---:|:---:|:---|:---:|:---:| | A | E | U | $\{1\}\!\to\!\{2,3,4,5\}$ | never-treated | $-2.5$ | **clean** | | B | L | U | $\{1,2,3\}\!\to\!\{4,5\}$ | never-treated | $-1.5$ | **clean** | | C | E | L | $\{1\}\!\to\!\{2,3\}$ | not-yet-treated (clean in window) | $-1.5$ | **clean** | | D | L | E | $\{2,3\}\!\to\!\{4,5\}$ | **already-treated** | $+0.5$ | **forbidden** | The entire source of bias is **comparison D**: it alone uses an already-treated unit (E) as the control. Its $+0.5$ pulls *against* the three negative clean DiDs. With enough weight on D (positive while the truth is negative), it drags $\hat\beta$ toward zero, and — given enough weight, as in the chapter's two-state world — past zero into the wrong sign. --- ## Problem 3 — The Goodman-Bacon weights, and TWFE as a weighted average (22 pts) **(a)** [8 pts] Plug $\bar D_E = 4/5$, $\bar D_L = 2/5$ into the four (unnormalized) weight expressions. $$s_A \propto \bar D_E(1-\bar D_E) = \tfrac45\cdot\tfrac15 = \tfrac{4}{25}.$$ $$s_B \propto \bar D_L(1-\bar D_L) = \tfrac25\cdot\tfrac35 = \tfrac{6}{25}.$$ $$s_C \propto (1-\bar D_L)^2\cdot\frac{\bar D_E - \bar D_L}{1-\bar D_L}\cdot\frac{1-\bar D_E}{1-\bar D_L} = (\bar D_E - \bar D_L)(1-\bar D_E) = \big(\tfrac45-\tfrac25\big)\big(\tfrac15\big) = \tfrac25\cdot\tfrac15 = \tfrac{2}{25}.$$ $$s_D \propto \bar D_E^{\,2}\cdot\frac{\bar D_L}{\bar D_E}\cdot\frac{\bar D_E - \bar D_L}{\bar D_E} = \bar D_L(\bar D_E - \bar D_L) = \tfrac25\cdot\big(\tfrac45-\tfrac25\big) = \tfrac25\cdot\tfrac25 = \tfrac{4}{25}.$$ Sum: $S = \dfrac{4 + 6 + 2 + 4}{25} = \dfrac{16}{25}$. Normalize ($w_k = s_k/S$): $$w_A = \frac{4/25}{16/25} = \frac{4}{16} = \tfrac14 = 0.250,\qquad w_B = \frac{6}{16} = \tfrac38 = 0.375,$$ $$w_C = \frac{2}{16} = \tfrac18 = 0.125,\qquad w_D = \frac{4}{16} = \tfrac14 = 0.250.$$ Check: $0.250 + 0.375 + 0.125 + 0.250 = 1.000$. ✓ **(b)** [6 pts] **Reconstruct $\hat\beta$** as $\sum_k w_k\,\widehat{\text{DiD}}_k$ using Problem-2 values $(-2.5, -1.5, -1.5, +0.5)$: $$ \hat\beta = \underbrace{\tfrac14(-2.5)}_{-0.625} + \underbrace{\tfrac38(-1.5)}_{-0.5625} + \underbrace{\tfrac18(-1.5)}_{-0.1875} + \underbrace{\tfrac14(+0.5)}_{+0.125}. $$ Sum: $-0.625 - 0.5625 - 0.1875 + 0.125 = \mathbf{-1.25}$. ✓ Exactly the pooled $\hat\beta^{\text{TWFE}}$ — this is Goodman-Bacon's identity, an exact equality with no error term. (In fractions: $-\tfrac58 - \tfrac9{16} - \tfrac3{16} + \tfrac18 = -\tfrac{20}{16} = -\tfrac54$.) **(c)** [4 pts] Reading the weights as a diagnostic. (i) The **largest** weight is $w_B = 3/8$ on the clean L-vs-never comparison — but note the **forbidden** comparison D carries a hefty $w_D = 1/4$, *tied for second* and equal to the clean A. The weighting is driven purely by treatment-timing variance, not by trustworthiness. (ii) Total weight on the forbidden comparison: $w_D = 0.25$. Its signed contribution is $w_D \cdot \widehat{\text{DiD}}_D = 0.25 \times (+0.5) = +0.125$. The true overall ATT is $-13/6 \approx -2.17$, but $\hat\beta = -1.25$ — **attenuated toward zero by about $0.92$** (exactly $-13/6-(-5/4)=-11/12\approx-0.917$). The forbidden term contributes $+0.125$ directly, and (more importantly) it forces the clean comparisons to be the *averages over treated periods* $-2.5$ and $-1.5$ rather than the deeper truth; the net effect is that $\hat\beta$ understates the true effect by a wide margin even though, here, the sign survives. **(d)** [4 pts] **Delete U.** With only States E and L, the pair $(E, L)$ is the *only* pair, so the treated-vs-never blocks A and B vanish; only the within-pair sub-comparisons C and D remain. Renormalize over $\{s_C, s_D\} = \{2/25, 4/25\}$: $$w_C = \frac{2/25}{6/25} = \tfrac13,\qquad w_D = \frac{4/25}{6/25} = \tfrac23.$$ $$\hat\beta = \tfrac13(-1.5) + \tfrac23(+0.5) = -0.5 + 0.333\overline{3} = \mathbf{-\tfrac16} \approx -0.167.$$ (Verified directly against a TWFE regression on the two-state, five-year panel: $-0.1\overline{6}$.) The situation is **strictly worse**: removing the clean never-treated control U strips out the two clean treated-vs-never blocks, so the forbidden comparison's weight *jumps from $1/4$ to $2/3$* — it now dominates the average. The estimate collapses from $-1.25$ to $-0.167$, almost on top of zero. Lengthen the horizon (the chapter's eight-year version, $G_E = 2$, $G_L = 5$, $t = 1,\dots,8$) and the forbidden comparison's positive contamination grows enough to push $\hat\beta$ all the way to **$+0.40$** — a full sign flip. Losing the never-treated unit is precisely the condition that lets the forbidden comparison become the *only* game in town for the late cohort, which is what completes the disaster. --- ## Problem 4 — The negative-weights view: de Chaisemartin–D'Haultfœuille (16 pts) **(a)** [4 pts] **Weights sum to one:** $$0.25 + 0.25 + (-0.0625) + (-0.0625) + 0.3125 + 0.3125 = 1.0000.\;\checkmark$$ **Weighted average of cell effects:** $$\sum w_{it}\text{ATT}_{it} = 0.25(-1) + 0.25(-2) + (-0.0625)(-3) + (-0.0625)(-4) + 0.3125(-1) + 0.3125(-2).$$ Term by term: $-0.25 - 0.50 + 0.1875 + 0.25 - 0.3125 - 0.625 = \mathbf{-1.25}$. ✓ The same $\hat\beta^{\text{TWFE}}$, now reconstructed a *third* way (after the by-hand TWFE and the Goodman-Bacon 2×2 average). One number, three identical decompositions. **(b)** [5 pts] **The negative weights** are $w = -0.0625$ on **cells 3 and 4**: State **E** in years **4 and 5**, which are E's event-time $e = 2$ and $e = 3$ cells — i.e., the **early cohort's late-period cells**, the part of E's treated history that overlaps L's treated window. **Bridge to Problem 2:** these are *exactly* the cells where already-treated E served as the contaminated control in the forbidden Type-3 comparison D. In the Goodman-Bacon view, D used E's years 4–5 as L's control; in the de Chaisemartin–D'Haultfœuille view, those same cells receive *negative* cell weights. The two decompositions are the same disease seen through two lenses: pairing $\to$ a forbidden 2×2; cell-by-cell $\to$ a negative weight on the cells doing the forbidden control duty. **(c)** [4 pts] **The dCDH warning.** Because all six $\text{ATT}_{it}$ are strictly negative but two weights are negative, the weighted sum is *not* a sensible average of the effects — and in principle the **sign of $\hat\beta$ can be opposite to the sign of every individual effect.** A weighted average with negative weights is not bounded between the min and max of the things it averages. Made concrete by the chapter's neighbor world (eight years, no never-treated state): there *every* true cell effect is negative (disclosure helps everyone, every year), yet $\hat\beta = +0.40$ — the estimate says the policy *raised* non-renewals. All true effects negative; estimate positive. **(d)** [3 pts] **The diagnostic.** Because $w_{it}$ depends only on the **design** — who is treated when — and not at all on the (unknown) treatment effects, the researcher can **compute every weight from the treatment-assignment pattern alone, before estimating a single effect.** She counts how many weights are negative and how much total negative weight there is; if a meaningful share is negative, $\hat\beta$ is uninterpretable and she should not report it. The ordering matters: computing weights *first* (from design) and effects *second* makes this a genuine **pre-commitment check** — she cannot be accused of fishing for a decomposition that excuses a result she already saw, because the weights were fixed by the adoption calendar before any outcome entered the calculation. --- ## Problem 5 — Callaway–Sant'Anna: clean ATT(g,t) and event-time aggregation (18 pts) **(a)** [4 pts] **Meaning of the arguments.** $\text{ATT}(g,t)$ is the average treatment effect, at **calendar time $t$**, on the cohort that **first adopted in year $g$** (i.e., all units with $G_i = g$). The first argument $g$ says *which group* (defined by its adoption year); the second $t$ says *when you are measuring*. Symbolically, $$\text{ATT}(g,t) = \mathbb{E}\big[\,Y_{it}(g) - Y_{it}(\infty)\ \big|\ G_i = g\,\big],$$ the expected gap, for the cohort-$g$ units, between their realized (treated-from-$g$) outcome and their never-treated potential outcome, at time $t$. **Event time** is $e = t - g$ (years since adoption); $e = 0$ is the first treated year. **Eligible clean controls** for cohort $g$ at time $t$: units that are **never-treated** ($G_i = \infty$) or **not-yet-treated** at $t$ (those with $G_i > t$, still untreated through the whole comparison window). **Forbidden:** any already-treated unit, i.e. any unit with $g' \le t$ and $g' \ne g$ — in particular an *earlier* cohort. **(b)** [8 pts] **The clean group-time grid.** Baseline period for cohort $g$ is $g - 1$. *Cohort E ($g = 2$), control = U (never), baseline $t = 1$:* $$\widehat{\text{ATT}}(2,2) = (Y_{E,2} - Y_{E,1}) - (Y_{U,2} - Y_{U,1}) = (9-10) - (10-10) = \mathbf{-1}\quad(e=0,\ \text{true } -1)$$ $$\widehat{\text{ATT}}(2,3) = (8-10) - (10-10) = \mathbf{-2}\quad(e=1,\ \text{true } -2)$$ $$\widehat{\text{ATT}}(2,4) = (7-10) - (10-10) = \mathbf{-3}\quad(e=2,\ \text{true } -3)$$ $$\widehat{\text{ATT}}(2,5) = (6-10) - (10-10) = \mathbf{-4}\quad(e=3,\ \text{true } -4)$$ (For $t = 2, 3$ you may instead use the not-yet-treated L as control — $Y_{L,t} = 10$ there — and get the identical answer, since L is still untreated before year 4.) *Cohort L ($g = 4$), control = U (never), baseline $t = 3$ — **never** the already-treated E:* $$\widehat{\text{ATT}}(4,4) = (Y_{L,4} - Y_{L,3}) - (Y_{U,4} - Y_{U,3}) = (9-10) - (10-10) = \mathbf{-1}\quad(e=0,\ \text{true } -1)$$ $$\widehat{\text{ATT}}(4,5) = (8-10) - (10-10) = \mathbf{-2}\quad(e=1,\ \text{true } -2)$$ Every clean group-time estimate hits the true effect **exactly**, because each is a Type-1 (or Type-2) clean DiD against a genuinely untreated control — no forbidden Type-3 comparison is ever formed, so there is no contamination to bias the estimate. This is the unbiasedness TWFE lacked. **(c)** [4 pts] **Event-time aggregation** $e = t - g$ (equal cohort sizes → simple averages across cohorts sharing an $e$): $$\widehat{\text{ATT}}^{\text{es}}(0) = \tfrac{(-1) + (-1)}{2} = -1,\quad \widehat{\text{ATT}}^{\text{es}}(1) = \tfrac{(-2) + (-2)}{2} = -2,$$ $$\widehat{\text{ATT}}^{\text{es}}(2) = -3\ (\text{only E}),\quad \widehat{\text{ATT}}^{\text{es}}(3) = -4\ (\text{only E}).$$ **Overall ATT** (simple average of all six group-time effects): $$\frac{(-1) + (-2) + (-3) + (-4) + (-1) + (-2)}{6} = \frac{-13}{6} \approx \mathbf{-2.17}.$$ Exactly the truth. Contrast with the broken pooled $\hat\beta^{\text{TWFE}} = -1.25$: the clean estimator is **right** ($-2.17$); TWFE got the sign right here but **attenuated the magnitude by about 40%**, understating how much the disclosure rule helped. (And in the no-never-treated world TWFE got the sign wrong entirely.) **(d)** [2 pts] In the two-state world (E, L only, no U), Callaway–Sant'Anna reports $\widehat{\text{ATT}}(4, t)$ for State L as **not identified / undefined** — it *refuses to compute it*, because L's only available comparison unit is the already-treated E, and the method forbids using an already-treated unit as a control. This **refusal is a feature**: when no clean counterfactual exists, the honest answer is "this effect is not identified," not a fabricated number. TWFE, by contrast, *did* produce a number from the same two states ($-0.167$, nearly flipped) by silently forming the forbidden comparison — manufacturing an answer where the data contain none. --- ## Problem 6 — Which estimator, and diagnosing a contaminated event study (12 pts) **(a)** [3 pts] **Sun–Abraham (2021)** — the interaction-weighted (IW) estimator. It stays inside a single event-study regression, so it changes the least code. The mechanism: instead of one coefficient $\beta_e$ per relative-time dummy, **saturate** the regression by interacting every relative-time dummy with every cohort indicator, estimating a separate coefficient $\delta_{g,e}$ for each (cohort $g$, event-time $e$) pair against never-treated (or last-treated) controls, then aggregate the $\delta_{g,e}$ to event-time effects with **cohort-share weights** (the "interaction weighting"). Because each cohort's dynamics are estimated *separately* before averaging, no cohort's effect at one event time can leak into another cohort's coefficient at a different event time — the cohort bleed is shut off. **(b)** [3 pts] **Borusyak–Jaravel–Spiess (2024)** — the imputation estimator, which they show is (under their assumptions) the *efficient* one. Three steps: (1) **fit** the two-way FE model $Y_{it} = \alpha_i + \lambda_t + \varepsilon_{it}$ using **only untreated cells** ($D_{it} = 0$: all never-treated cells plus every adopter's pre-adoption years); (2) **impute** each treated cell's missing untreated outcome $\hat Y_{it}(0) = \hat\alpha_i + \hat\lambda_t$; (3) **difference** $\hat\tau_{it} = Y_{it} - \hat Y_{it}(0)$ and average the $\hat\tau_{it}$ with explicit weights. The $\hat\alpha_i, \hat\lambda_t$ are uncontaminated **because the treated cells are excluded from the fit** — no treatment effect ever enters the estimation of the fixed effects that serve as the counterfactual, which is exactly what pooled TWFE failed to do (it fit on *all* cells, letting treated cells corrupt the FE that double as everyone's control). Its pre-trend test is built from the untreated residuals, so it is not contaminated. **(c)** [4 pts] **Diagnosis.** Priya is *not* seeing a real parallel-trends violation — she is seeing **Sun–Abraham contamination of the naive event study**. Under staggered timing with heterogeneous/dynamic effects, each estimated pre-period coefficient $\hat\beta_e$ in a naive TWFE event study is **polluted by treatment effects from *other* event times of *other* cohorts** — the leads and lags bleed into one another through the same forbidden later-vs-already-treated comparisons. A coefficient nominally at $e = -2$ can pick up some other cohort's $e = +1$ effect, manufacturing a slope in the pre-periods even when the true pre-trends are dead flat. So her "funny pre-trends" are an *artifact of the estimator*, not evidence her design is broken. **What she should run:** a heterogeneity-robust event study — Sun–Abraham IW, Callaway–Sant'Anna aggregated by event time, or Borusyak–Jaravel–Spiess — each of which estimates cohort dynamics in isolation against clean controls. **What the corrected plot should show:** if parallel trends really holds, the pre-period coefficients ($e < 0$) should sit **near zero** (a genuine placebo/pre-trend check), and only the post-period coefficients should trace the building disclosure effect. **(d)** [2 pts] **Spec-discipline upgrade (Conventions §4, extended).** A staggered-DiD write-up must now state two choices a plain 2×2 did not need: (1) **name the control group** — are the clean comparisons against *never-treated* units, *not-yet-treated* units, or both (this matters because never-adopters may differ systematically, while not-yet-treated adopters are often a more credible counterfactual but shrink the control pool as cohorts switch on); and (2) **name the aggregation weights** — event-time average, calendar-time average, or a single overall ATT, and how cohorts were weighted into the headline number. The identifying assumption is **parallel trends stated per cohort**: each adopting cohort's untreated potential outcome would have moved parallel to its clean control group's, in every comparison window. --- *End of solutions for Problem Set 4.2. Three independent decompositions of the same pooled $\hat\beta = -1.25$ — by-hand TWFE, the Goodman-Bacon 2×2 average (weights $\tfrac14,\tfrac38,\tfrac18,\tfrac14$ on DiDs $-2.5, -1.5, -1.5, +0.5$), and the de Chaisemartin–D'Haultfœuille cell-weight sum (two weights negative) — all land on the identical number, and all trace the bias to one culprit: the forbidden later-vs-already-treated comparison ($+0.5$, the only positive piece). The Callaway–Sant'Anna clean grid recovers the true $-13/6 \approx -2.17$ exactly. Goodman-Bacon (2021), de Chaisemartin and D'Haultfœuille (2020), Sun and Abraham (2021), Callaway and Sant'Anna (2021), and Borusyak, Jaravel, and Spiess (2024) are four diagnostics and three cures for one disease.*