Title: Difference-in-Differences

Q: Identification assumptions of DiD
A: Exclusion restrictions (Stable Unit Treatment  Value Assumption (SUTVA), No anticipation, Initial conditions assumption, No dynamic effects); Parallel trends

Q: What is the “never-treated outcome” \(Y_{g,t}(0_t)\) in DID notation?
A: The potential outcome group \(g\) would have at time \(t\) if it remained untreated from period 1 through \(t\).

Q: State the Parallel Trends (PT) assumption formally
A: That the expected change in the untreated potential outcome is identical for all groups over time.
 For all \(t \ge 2\):
\(E\left[Y_{g,t}(0_t) - Y_{g,t-1}(0_{t-1})\right] \text{ is constant across } g.\)
It means:
- Group A’s expected untreated change from t-1 to t
- Group B’s expected untreated change from t-1 to t
- Group C’s expected untreated change from t-1 to t
are all equal, whatever that number is which implies:
\(E[\Delta Y_{g,t}(0)] = \text{constant across groups}\)

Q: What does “parallel trends on average” mean?
A: Only the average trend among treated groups needs to equal the average trend among control groups:
\(E\left[\frac{1}{G_1}\sum_{g:D_g=1} \Delta Y_{g,t}(0_t)\right] = E\left[\frac{1}{G_0}\sum_{g:D_g=0} \Delta Y_{g,t}(0_t)\right].\)

Q: When is “parallel trends on average” sufficient?
A: In many DID results (e.g., classical 2×2 or multi-period DID), identification relies only on equal average changes for treated vs. control groups, not group-by-group parallel trends.

Q: What is the purpose of a pre-trend test?
A: To test whether treated and control groups exhibited parallel outcome trends before treatment, providing evidence for or against Assumption PT.

Q: What is the standard recommendation from Bertrand et al. (2004)?
A: Cluster at the level of treatment assignment to account for within-cluster serial correlation.

Q: Why is clustering at the treatment level not automatically correct in a model-based framework?
A: Because treatment is conditioned upon; cross-group correlation must come from the behavior of potential outcomes, not treatment assignment

Q: Stable Unit Treatment  Value Assumption
A: That group g’s potential outcomes depend only on group g’s own treatment, not on treatments assigned to other groups.

Q: What phenomenon commonly violates SUTVA in DID settings?
A: Spatial spillovers—when treatment in some locations affects outcomes in nearby untreated locations.

Q: Why is SUTVA important for standard DID identification?
A: Because DID assumes untreated groups are valid controls; spillovers break this assumption by contaminating untreated potential outcomes.

Q: What is the No Anticipation (NA) assumption in DID?
A: It requires that a group’s outcome at time t does not depend on its future treatments.
or all groups g and all treatment paths \((d_1,\dots,d_T):Y_{g,t}(d_1,\dots,d_T) = Y_{g,t}(d_1,\dots,d_t).\)
Only past and current treatments may affect outcomes, not future ones.

Q: What does No anticipation assumption rule out?
A: Any behavioral or outcome changes before actual treatment, caused by anticipating the treatment.

Q: When is NA least plausible?
A: When treatment is announced well in advance or publicized, allowing groups to change behavior before implementation

Q: How do researchers handle situations where treatment is announced early and NA is violated?
A: They often redefine a (g,t) observation as treated starting at the announcement date, not the implementation date.

Q: Why is NA important in DID designs?
A: Without NA, pre-treatment outcomes may be contaminated by anticipatory effects, biasing DID estimates.

Q: What is the “initial conditions” assumption in DID?
A: It assumes that a group’s treatment before period 1 has no effect on outcomes observed from period 1 onward.

Q: How is the initial conditions assumption implied by the potential outcomes notation?
A: The notation \(Y_{g,t}(d_1,\dots,d_t)\) assumes only treatments from period 1 to \(t\) matter; it ignores any treatments before period 1.

Q: When is the initial conditions assumption potentially problematic?
A: When groups may have been exposed to treatment before period 1, since prior exposure could alter observed outcomes and violate identification.

Q: What is the No Dynamic Effects (ND) assumption in DID?
A: It requires that a group’s outcome at time t depends only on its current treatment, not on past treatments.
For all groups g and all treatment paths \((d_1,\dots,d_t): Y_{g,t}(d_1,\dots,d_t) = Y_{g,t}(d_t)\).

Q: When is Assumption ND plausible?
A: When the treatment effect is immediate and does not persist—e.g., markets where prices adjust quickly to taxes

Q: What simplification occurs under NA + ND with a binary treatment?
A: Each (g,t) has only two possible potential outcomes:
- Y_{g,t}(0) when untreated at t,
- Y_{g,t}(1) when treated at t.
This reduces DID to the standard Neyman–Rubin potential outcomes framework

Q: How do the No Anticipation (NA), Initial Conditions, and No Dynamic Effects (ND) assumptions differ?
A: They restrict different parts of the treatment timeline:
1. Initial Conditions:
Past before period 1
- Outcomes from period 1 onward do not depend on treatment exposure before the dataset begins.
2. No Anticipation (NA):
Future after time t
- The outcome at time t does not depend on future treatment a group will receive.
3. No Dynamic Effects (ND):
Past within the observed dataset
- The outcome at time t does not depend on past treatments (from periods 1 to t-1).
Together they restrict:
- Initial conditions → treatment before data start
- NA → treatment after current period
- ND → treatment in earlier observed periods

Q: Why is Assumption PT equivalent to the never-treated outcome following a TWFE model? Explain the math intuitively.
A: Assumption PT says all groups would follow the same trend over time if they were never treated.
This implies the never-treated outcome can be written as a group effect + time effect + noise, which is exactly a TWFE model.
Step-by-step intuition:
1. Start with the PT assumption:
For any \(t \ge 2\):
\(E[Y_{g,t}(0_t) - Y_{g,t-1}(0_{t-1})]\) is the same for every group.
Meaning: everyone would move in parallel if untreated.
2. Accumulate changes over time:
The total expected change from period 1 to t is just the sum of period-by-period changes:
\(E[Y_{g,t}(0_t) - Y_{g,1}(0)]= \sum_{t'=2}^{t} E[Y_{g,t'}(0_{t'}) - Y_{g,t'-1}(0_{t'-1})]\)
Since each term is identical across groups, the whole sum is identical across groups.
3. Define what is constant across groups:
Let the common time effect be:
\(\gamma_t = E[Y_{g,t}(0_t) - Y_{g,1}(0)]\) Period 1 is chosen as the baseline or “reference point.”.
Let each group just differ by its starting point (its baseline level):
\(\alpha_g = E[Y_{g,1}(0)]\)
4. Rewrite expected outcomes:
Then:
\(E[Y_{g,t}(0_t)] = \alpha_g + \gamma_t\)
This is exactly the expected value in a two-way fixed effects (TWFE) model:
  - \(\alpha_g\): group fixed effect
  - \(\gamma_t\): time fixed effect
5. Add noise to match actual data:
Actual never-treated outcome differs from its expectation by a random deviation:
\(\varepsilon_{g,t} = Y_{g,t}(0_t) - E[Y_{g,t}(0_t)]\)
6. Final TWFE form:
\(Y_{g,t}(0_t) = \alpha_g + \gamma_t + \varepsilon_{g,t}, \qquad E[\varepsilon_{g,t}] = 0\)
Layman explanation:
- PT says: If no one were treated, all groups would follow the same “slope” over time.
- TWFE says: Each group has its own starting point (α), each year has its own shift (γ), and what’s left is noise.
- These are the same idea written in two different languages.
Therefore, PT holds if and only if the never-treated outcome can be written as a TWFE model.

Q: What is the broader idea behind the TWFE (Two-Way Fixed Effects) model, and how does it connect to DID assumptions?
A: The TWFE model assumes that outcomes can be decomposed into:
1. A group fixed effect \(\alpha_g\):
Each group starts at its own baseline level (e.g., richer counties start higher, poorer ones lower).
2. A time fixed effect \(\gamma_t\):
All groups share common shocks over time (e.g., national recessions, federal policy changes).
3. An idiosyncratic shock \(\varepsilon_{g,t}\):
Random fluctuations affecting only that group in that period.
Mathematically:
\(Y_{g,t}(0) = \alpha_g + \gamma_t + \varepsilon_{g,t}\)
TWFE means every group has its own starting point, but they all ride the same roller coaster over time—unless treatment pushes them off that path. DID estimates the size of that push

Q: What is the difference between “parallel trends for all groups” and “parallel trends on average”?
A: - Parallel trends for all groups: Every group must have the same untreated trend individually.
- Parallel trends on average: Only the average trend of treated groups must equal the average trend of control groups.
The second condition is weaker and is sufficient for many DID results

Q: State the “parallel trends on average” condition formally
A: For treated groups (\(D_g = 1\)) and control groups (\(D_g = 0)\):
\(E\left[ \frac{1}{G_1} \sum_{g:D_g = 1} \left( Y_{g,t}(0_t) - Y_{g,t-1}(0_{t-1}) \right) \right] = E\left[ \frac{1}{G_0} \sum_{g:D_g = 0} \left( Y_{g,t}(0_t) - Y_{g,t-1}(0_{t-1}) \right) \right]\)
This means treated and control groups have the same expected untreated trend on average.

Q: State Assumption IND (Independent Groups)
A: Potential outcome vectors are independent across groups, but may be serially correlated within group.
- Allows: Serial correlation within group.
- Does not allow (unconditionally): Cross-group dependence.
- But: Cross-group dependence may exist conditionally on macro shocks.

Q: In DID, what does it mean for treatment to be “non-absorbing”
A: A non-absorbing treatment is one where units can enter, exit, and re-enter treatment over time.
Formally, \(D_{g,t} = 1\) does not imply \(D_{g,t+1} = 1\).
Treatment is not permanent and does not follow the one-way, never-leave structure assumed in many staggered adoption DID designs.

Q: what is the issue with non-absorbing treatment in staggered DiD?
A: If treatment is non-absorbing, then:
- Event time cannot be defined cleanly
- Treatment cohorts may not exist
- Standard TWFE and event-study estimators can be invalid
- Identification requires methods that handle treatment switching

Q: What is the \((g,t)\)-specific treatment effect \(TE_{g,t}\) in DID, and how is it defined?
A: The \((g,t)\)-specific treatment effect measures the causal effect for group g at time t. It is:
\(TE_{g,t} = E\left[ Y_{g,t} - Y_{g,t}(0_t) \right]\)
Equivalently,
\(TE_{g,t} = E\big[ Y_{g,t}(0_{T_0}, 1_{t-T_0}) - Y_{g,t}(0_t) \big]\)
the effect of being treated for \(t - T_0\) periods versus remaining untreated.

Q: What is a “target parameter” in the DID literature?
A: A target parameter is the causal effect the researcher wants to learn, such as an ATT or a dynamic treatment effect.
It represents the true underlying causal quantity, independent of how it is estimated.

Q: What does “staggered treatment timing” mean in DiD?
A: In staggered DiD, different units become treated at different times, and treatment is absorbing (once treated, always treated).
This creates multiple treatment cohorts and multiple post-treatment periods, allowing the researcher to trace out dynamic effects over time.

Q: Why are multi-period DID designs fundamentally different from 2×2 DID?
A: They allow researchers to:
1. Estimate ATT(t) for each post-treatment period (treatment dynamics).
2. Evaluate pre-trends using multiple pre-treatment periods.
3. Handle more complex treatment timing (e.g., staggered adoption).
4. Aggregate or compare treatment effects across time.

Q: How is the observed outcome written when treatment happens only once?
A: For unit i at time t:
\(Y_{i,t} = D_i \, Y_{i,t}(1) + (1 - D_i) \, Y_{i,t}(0)\)
Under no anticipation:
- Before treatment →   \(Y_{i,t} = Y_{i,t}(0)\)
- After treatment → observe \(Y_{i,t}(1)\) if treated, otherwise  \(Y_{i,t}(0)\)

Q: What does an event study do in a DID setting?
A: An event study estimates treatment effects in each period before and after treatment, relative to a baseline, producing a full dynamic path of ATT(t) over event time.

Q: What is the target parameter ATT(t) in a 2×T event study?
A: \(ATT(t) = E[Y_{i,t}(1) - Y_{i,t}(0) \mid D_i = 1]\)
It measures the treatment effect on treated units at each post-treatment period \(t \ge g\).

Q: What kinds of questions do ATT(t) dynamics help answer?
A: hey reveal whether treatment effects:
- Accumulate over time
- Grow (e.g., health stock models)
- Require adjustment periods
- Persist or fade out
Dynamic ATTs identify treatment effect evolution.

Q: State the parallel trends assumption for event studies (PT-ES)
A: For all post-treatment periods \(t \ge g\):
\(E_\omega[Y_{i,t}(0) - Y_{i,g-1}(0) \mid D_i = 1] = E_\omega[Y_{i,t}(0) - Y_{i,g-1}(0) \mid D_i = 0]\)
This requires parallel untreated changes from the pre-treatment baseline in all post-treatment periods.

Q: Why does learning about long-run effects require stronger assumptions under PT-ES?
A: Because to identify ATT(t) for period t, PT must hold for every year up to t.
Long-run effects require parallel trends for many years, while short-run effects require fewer parallel periods.

Q: How do we identify ATT(t) under PT-ES and no anticipation?
A: Through a 2×2 DID using periods  \(g-1\) and \(t\):
\(ATT(t) = ( \bar{Y}_{D=1,t} - \bar{Y}_{D=1,g-1} ) - ( \bar{Y}_{D=0,t} - \bar{Y}_{D=0,g-1} )\)

Q: What is the sample estimator \(\widehat{ATT}(t)\) in a 2×T event study?
A: \(\widehat{ATT}(t) = (\bar{Y}^{\omega}_{1,t} - \bar{Y}^{\omega}_{1,g-1}) - (\bar{Y}^{\omega}_{0,t} - \bar{Y}^{\omega}_{0,g-1})\) where the ω superscript refers to the weighting scheme applied to compute group averages
\(\bar{Y}^{\omega}_{1,t} = \frac{\sum_{i: D_i = 1} \omega_i Y_{i,t}}{\sum_{i: D_i = 1} \omega_i}\), where \(\omega_i =\) weight for unit \(i\)

Q: How does TWFE estimate event study effects?
A: Run a regression with unit FE, time FE, and interactions between \(D_i\) and time dummies:
\(Y_{i,t} = \theta_t + \eta_i + \sum_{k \ne g-1} \beta_k (1\{i \in G\} \cdot 1\{t=k\}) + \varepsilon_{i,t}\)
Then \(\beta_t =\) ATT(t)
The omitted period is g-1
- You must omit one event-time indicator to avoid perfect multicollinearity.
- Conventionally, you omit event time –1, which corresponds to calendar time g–1, the last pre-treatment period.

Q: In a Callaway–Sant’Anna staggered DiD, is the baseline period (g–1) omitted like in a TWFE event-study regression?
A: No.
Unlike TWFE event-study regressions, Callaway & Sant’Anna do not omit the baseline period.
They estimate a group-time ATT for every (g, t), and under No Anticipation:
\(ATT(g,t) = 0 \quad \text{for all } t < g\)
so the baseline period \(t = g-1\) is not omitted — it is estimated to be zero by assumption, not by normalization.
TWFE drops the baseline for identification.
C&S keeps it but sets it to zero as implied by the potential outcomes model.

Q: How are event-study pre-trend estimates defined?
A: For k > 1:
\(\tau_{-k} = E_\omega[Y_{i,g-k} - Y_{i,g-1} \mid D_i = 1] - E_\omega[Y_{i,g-k} - Y_{i,g-1} \mid D_i = 0]\)
They measure differential untreated trends before treatment.
The null hypothesis is:
\(H_0: \tau_{-k} = 0 \quad \text{for all pre-periods } k\): No differential pre-trends (treated and control groups followed parallel trends before treatment)
(failing to reject is a good thing)

Q: Under No Anticipation, what do pre-trend coefficients represent?
A: Since all pre-treatment ATT(t) must equal zero, pre-trends measure pure differences in untreated trends — not treatment effects.

Q: Do pre-trend tests test the parallel trends assumption?
A: Not exactly.
Pre-trends test untreated trend similarity in earlier periods, but parallel trends must hold after treatment in the counterfactual untreated world, which is unobservable.
Thus PT-ES is not testable, only indirectly assessed.

Q: Why might pre-trends fail to reflect whether PT-ES holds?
A: Because:
1. Pre-trend differences far before treatment may not imply post-period violations.
2. Selection into treatment based on time-varying unobservables can produce pre-trend slopes unrelated to post-treatment counterfactual trends.
3. Low statistical power makes insignificant pre-trends uninformative.

Q: Why is PT-ES formally untestable?
A: Because PT-ES places restrictions on untreated potential outcomes after treatment. These outcomes are never observed, so we can only test pre-period analogues, which may not reflect post-period behavior.

Q: Why is low statistical power in event study pre-trend tests a problem?
A: Because insignificant pre-trends cannot distinguish between:
- truly parallel trends, vs.
- large but imprecisely estimated violations.
Thus “insignificant pre-trends” do not reliably imply PT holds.

Q: How do Rambachan & Roth (2023) propose using pre-trend information?
A: They bound post-treatment ATT(t) effect sizes under assumed limits on parallel-trend violations, using pre-trend estimates to set plausible bounds.
They construct identified sets and robust confidence intervals for ATT(t), accounting for possible PT violations.

Q: When are pre-trends especially uninformative about post-treatment parallel trends?
A: 1. When they are measured far before treatment starts.
2. When time-varying unobservables drive selection into treatment.
In such cases, pre-period patterns may differ from relevant post-period counterfactual trends.

Q: How can selection on time-varying unobservables distort pre-trends?
A: If units select into treatment based on changing unobservables, untreated outcomes may drift differently before treatment.
This can generate non-parallel pre-trends even when post-treatment parallel trends might still hold—or vice versa.

Q: Why is Assumption PT-ES (parallel trends for event studies) not testable?
A: Because PT-ES puts restrictions on untreated potential outcomes in post-treatment periods, which are never observed.
Pre-trends only inform us about trends in pre-treatment periods, i.e., the “wrong” time window.

Q: What is the martingale-type condition mentioned in relation to Ghanem et al. (2022)? (Conceptually)
A: They show that if selection depends on time-varying unobservables, a necessary condition for parallel trends is that untreated potential outcomes follow a martingale (loosely: conditional expectations don’t drift systematically).
When this fails, parallel trends cannot hold, regardless of the visual shape of pre-trends.

Q: When does parallel pre-trends become directly testable?
A: If we assume PT-ES holds both pre- and post-treatment, the DiD model becomes overidentified.
Then pre-trend restrictions are testable via overidentification tests (e.g., using \(τ_{k}\)’s), and violations directly refute the model.

Q: How do Bilinski & Hatfield (2018) suggest using pre-trends?
A: They propose picking a differential trend magnitude that would fully explain the estimated effect, then using that as the null in tests of pre-trends.
This shifts the question from “is the pre-trend zero?” to “could a plausible differential trend explain away the estimated effect?”

Q: What are the three key lessions of the recent pre-trends literature?
A: 1. PT-ES itself is not testable, and pre-trends only measure pre-period differences in untreated trends.
They are informative but not equivalent to testing the actual post-period parallel trends assumption.
2. Statistical precision heavily shapes how informative pre-trends are.
Low-powered tests can fail to reject zero pre-trends and fail to reject large violations; they “don’t say much.”
3. By taking a stand on the plausible size of parallel trends violations and using methods that:
- Bound ATT(t) under assumed maximum violations (Rambachan & Roth, 2023), or
- Test whether a given violation magnitude could fully explain the estimated effect (Bilinski & Hatfield, 2018).

Q: In Rambachan & Roth (2023), how are post-period ATT(t)’s bounded?
A: They impose an upper bound on how large parallel-trends violations can be in post-periods (based on pre-trend magnitudes or external info).
Then they derive an identified set for ATT(t) and construct robust confidence intervals for that set using the covariance of the event-study estimates.

Q: What can researchers do when pre-trends suggest PT-ES fails?
A: Possible responses:
1. Assume PT holds conditional on covariates and include them appropriately.
2. Parametrically model non-parallel trends (e.g., unit-specific linear trends).
3. Use sensitivity analysis / bounds (e.g., Rambachan & Roth) rather than a strict PT assumption.

Q: What does it mean to condition on covariates to restore parallel trends?
A: It means assuming that, after controlling for covariates X_i
\(E[Y_{i,t}(0) - Y_{i,g-1}(0) \mid D_i=1, X_i] = E[Y_{i,t}(0) - Y_{i,g-1}(0) \mid D_i=0, X_i]\)
So conditional parallel trends holds, even if unconditional parallel trends does not.

Q: What is a “uniform” (or “simultaneous”) confidence band in an event study?
A: A band that covers the entire event-study path \{ATT(t)\} with a specified probability (e.g., 95%).
It accounts for multiple testing by using a sup-t critical value based on the maximum absolute t-stat across all t.

Q: How are simultaneous confidence bands for event studies commonly constructed?
A: - Bootstrapping (e.g., multiplier bootstrap), or
- Using the estimated variance-covariance matrix of all \(\hat\beta_t\) and simulating the sup-t distribution (e.g., Montiel Olea & Plagborg-Møller, 2018).
These yield critical values for the maximum t-statistic and thus uniform bands.

Q: What is \(ATT_{agg}\) in an event-study context?
A: A scalar summary of post-treatment effects:
\(ATT_{\text{avg}} = \frac{1}{T - (g-1)} \sum_{t=g}^{T} ATT(t)\)
the average treatment effect across all post-treatment periods.

Q: What is the simplest way to estimate \(ATT_{\text{avg}}\)?
A: Compute \(\widehat{ATT}_{\text{avg}}\) for each post period (via 2×2 DID or event-study regression), then average them:
\(\widehat{ATT}_{\text{avg}} = \frac{1}{T - (g-1)} \sum_{t=g}^{T} \widehat{ATT}(t)\)

Q: What is the common “shortcut” regression people use instead of aggregating ATT(t)’s directly? Why does it fail?
A: They run a regression with a single treatment dummy:
\(Y_{i,t} = \theta_t + \eta_i + \beta^{OLS} D_{i,t} + \varepsilon_{i,t}\) where
\(D_{i,t} = 1\{D_i = 1\} \cdot 1\{t \ge g\}\)
it fails because:
\(\beta^{OLS}\)is equivalent to:
1. Collapsing the data to average pre and average post outcomes,
2. Running a 2×2 DID on those averages.
This effectively subtracts the average pre-period differential trend from the average post ATT(t).
Unless PT-ES holds in all periods (pre and post),
\(beta^{OLS} \neq ATT_{\text{avg}}\)

Q: What assumptions are needed for \(\beta^{OLS}\) to equal \(ATT_{\text{avg}}\)?
A: You need parallel trends to hold in every period, including pre-treatment periods.
Only then is the average pre-period gap equal to the baseline g-1 gap, making the average post ATT(t) and  \(\beta^{OLS}\) line up.

Q: How does regression adjustment (RA) generalize from 2×2 DiD to event studies?
A: Instead of using a short difference \(\Delta Y_{i,2}\), you use long differences from the baseline g-1:
\(Y_{i,t} - Y_{i,g-1}\)
You model \(E_\omega[Y_{i,t} - Y_{i,g-1} \mid X_i, D_i=0]\) and adjust treated units based on this model for each post t.

Q: Is the propensity score model used for Inverse Probability Weighting (IPW) different in 2×2 vs 2×T?
A: No.
The IPW modeling of the treatment probability (e.g., \(P(D_i=1 \mid X_i)\)) is the same as in 2×2.
What changes is that you use long differences in outcomes across many post-periods.

Q: How does the doubly robust (DR) estimator extend to event studies?
A: For each post t, DR combines:
- RA: a model for \(E_\omega[Y_{i,t} - Y_{i,g-1} \mid X_i, D_i=0]\), and
- IPW: weights based on propensity scores.
It remains consistent if either the outcome model or the propensity model is correctly specified.

Q: What caution applies to using covariates in a TWFE spec with many periods?
A: All the pitfalls from the 2×2 TWFE + covariates case carry over and become more complex (e.g., bad controls, post-treatment controls, non-parallel trends).
One must be careful to include only covariates that help support conditional parallel trends without introducing bias.

Q: How does Callaway & Sant’Anna aggregate treatment effects across cohorts and time?
A: C&S compute:
\(ATT(g,t) \quad \text{for each cohort } g \text{ and time } t\)
then aggregate using explicit, choice-driven weights, e.g.:
- cohort size
- cohort share
- equally weighted across cohorts
- equally weighted across time
Their aggregation is modular and transparent:
\(ATT^{\text{overall}} = \sum_{g,t} w_{g,t} \, ATT(g,t)\)
Weights \(w_{g,t}\) are chosen by the researcher for interpretation.

Q: How does a TWFE model aggregate treatment effects across cohorts?
A: TWFE implicitly averages all cohort- and timing-specific treatment effects according to regression-implied weights, which:
- depend on variation in treatment timing,
- can be negative,
- often overweight late-treated groups, and
- can combine incomparable ATT(g,t)’s.
There is no researcher control over these weights.
Layman version:
C&S lets you pick the weights.
TWFE picks them for you, often badly.

Q: Why are TWFE event-study coefficients biased when treatment effects vary across cohorts or over time?
A: Because TWFE pools all treated units as if they had the same effect path, forcing:
- early-treated cohorts to serve as controls for later-treated cohorts
- and vice versa.
Under heterogeneity, these “controls” are already treated, so TWFE subtracts treated potential outcomes from treated potential outcomes, producing:
- contaminated comparisons
- negative weights
- biased estimates
- incorrect dynamic patterns (e.g., “dip then rise” artifacts)

Q: Mechanically, why does TWFE deliver biased event-study coefficients under staggered adoption?
A: Because the TWFE regression estimates:
\(Y_{i,t} = \theta_t + \eta_i + \beta_t D_{i,t} + \varepsilon_{i,t}\)
treating already-treated units as controls for units treated later.
These comparisons identify:
\(E[Y_t(1) - Y_t(1)]\)
which collapses meaningful causal contrasts and generates non-causal “DID-on-treated” comparisons.
This creates sign reversals and spurious dynamics.

Q: What is the problem Sun & Abraham refer to as “forbidden comparisons”?
A: TWFE forms comparisons where:
- some “controls” are not actually untreated,
- some “pre-periods” for the comparison group are not truly untreated.
These comparisons do not recover any causal ATT(g,t) and contaminate every \beta_t

Q: What is an intuitive explanation for why TWFE fails under heterogeneity?
A: TWFE asks:
“Who hasn’t been treated yet? I’ll use them as controls.”
But in staggered adoption:
- early-treated units eventually get treated
- then TWFE still uses them to “control” for later-treated units
So TWFE compares treated apples to treated oranges, pretending they are untreated controls.
This destroys the causal interpretation.

Q: If your committee asks: “Why not just use a TWFE event study for staggered DiD?” what is the core answer?
A: Because TWFE event studies are not valid when treatment effects vary across cohorts or over time — which is almost always the case in policy applications.
TWFE:
- mixes treated units into the control group
- imposes equal effects across groups by functional form
- produces negative and incoherent weights
- yields biased and sometimes sign-flipped estimates
- cannot separately estimate cohort-specific dynamic effects
Callaway & Sant’Anna avoids these problems by:
- identifying ATT(g,t) cleanly
- using only never-treated or not-yet-treated comparison units
- aggregating effects transparently
- allowing treatment effect heterogeneity.

Q: Under what (rare) conditions does TWFE give valid dynamic effects in staggered DiD?
A: TWFE is valid only if:
1. Treatment effects are homogeneous:
ATT(g,t) = ATT(t) \quad \forall g
2. There is no anticipation
3. Parallel trends holds
4. No treatment reversals
In practice, heterogeneity almost always exists, so TWFE is usually invalid for causal interpretation.

Q: Why has C&S become the default for staggered DiD?
A: Because it:
- correctly handles heterogeneity
- avoids forbidden comparisons
- gives cohort-specific causal effects
- aggregates transparently
- aligns with potential outcomes reasoning
- passes placebo tests cleanly
- produces interpretable dynamics
It fixes every major failure mode of TWFE under staggered adoption.

Q: Define parametric methods in econometrics.
A: Parametric methods specify a functional form and a finite set of parameters. Example:
\(Y_{it} = \alpha_i + \gamma_t + \beta D_{it} + \varepsilon_{it}\)
They rely on assumptions about distributional shape and model structure.
Advantages: efficient if correct.
Disadvantages: biased if the model is misspecified.

Q: Define nonparametric methods in econometrics.
A: Nonparametric methods avoid strong functional-form assumptions and allow the data to determine relationships flexibly.
Examples: kernel estimators, matching, random forests, local polynomials.
Advantages: robust to misspecification.
Disadvantages: less efficient; can require large samples; harder to interpret.

Q: How do parametric and nonparametric approaches differ in DID?
A: - Parametric (e.g., TWFE):
Assumes linearity, constant effects (under heterogeneity this fails), and independence of FE structure.
- Nonparametric (e.g., C&S IPW or DR):
Relies less on functional form; directly estimates group-time ATT(g,t) using “not-yet-treated” controls.
Nonparametric methods generally produce more credible causal effects under staggered adoption.

Q: Define bootstrapping.
A: Bootstrapping repeatedly resamples the observed data with replacement to approximate the sampling distribution of an estimator.
Used to compute standard errors, confidence intervals, and test statistics without strong parametric assumptions.

Q: List common bootstrap variants used in econometrics.
A: 1. Nonparametric bootstrap: resample units with replacement.
2. Cluster bootstrap: resample clusters (e.g., counties).
3. Wild bootstrap / Wild cluster bootstrap: resample residual signs or multipliers for heteroskedastic/clustered settings.
4. Multiplier bootstrap: apply random weights to estimating equations; used in C&S (2021).
5. Weighted (Bayesian) bootstrap: assigns random exponential weights; useful in high-dimensional estimators.
6. Block bootstrap: resample time blocks for dependent data.

Q: Why is bootstrapping important in DID settings?
A: Because DID involves:
- serial correlation,
- grouped treatment assignment,
- multi-period dependence,
- complicated event-study covariance structures.
Standard asymptotic formulas can fail; bootstrapping provides reliable inference under complex dependence.

Q: Define the sup-t statistic in event-study inference.
A: The sup-t statistic is the maximum absolute t-statistic across all event-time coefficients:
\(\text{sup-}t = \max_{t} \left| \frac{\hat{\beta}_t}{\hat{\sigma}_t} \right|\)
Used to construct uniform (simultaneous) confidence bands for the entire event-study path.

Q: Why is the sup-t distribution used in event studies?
A: Because event studies estimate many ATT(t) values jointly.
Pointwise 95% confidence intervals do not ensure 95% confidence over the entire path.
The sup-t distribution provides correct simultaneous inference, adjusting for multiple testing.

Q: Why does modern DID use “not-yet-treated” units as controls?
A: Because they represent the correct counterfactual untreated state for each treated cohort.
Using already-treated units as controls (as TWFE does) violates the potential outcomes framework and biases ATT(g,t).

Q: How do Callaway & Sant’Anna differ from Sun & Abraham?
A: C&S (2021):
- Nonparametric, identification-based.
- Computes ATT(g,t) directly.
- Aggregation transparent.
- Handles heterogeneity naturally.
- Uses not-yet-treated controls.
Sun & Abraham (2020):
- Corrects TWFE via reweighting.
- Creates cohort-specific event-study estimates.
- Still regression-based.
- Requires explicitly constructing clean comparison sets.
C&S is conceptually cleaner; S&A is a correction for TWFE users.

Q: Compare C&S and Borusyak–Jaravel–Spiess (BJS).
A: C&S:
- Identification + averaging.
- Uses DID logic across cohorts.
- Nonparametric.
BJS:
- “Imputation” estimator.
- Predict untreated potential outcomes using never-treated or not-yet-treated units.
- Then imputes missing counterfactuals.
- Produces smooth dynamic paths; highly efficient.
C&S is conceptually clean; BJS is computationally efficient and less noisy.

Q: How do S&A and BJS differ?
A: Sun & Abraham:
- Regression-based
- Decomposition of TWFE
- Produces cohort-specific event-study coefficients
- Still relatively noisy in small samples
BJS:
- Builds the entire counterfactual outcome path
- Does not rely on regression residualization
- Can handle flexible designs, non-binary treatments, and missing data gracefully

Q: What is the Goodman-Bacon “Bacon Decomposition” in staggered DiD, and why does it matter?
A: The Bacon Decomposition (Goodman-Bacon, 2019) shows that the TWFE DiD estimator with staggered treatment timing can be written as a weighted average of all possible 2×2 DiD comparisons in the data.
These comparisons fall into three types:
1. Earlier-treated vs Later-treated (“ET vs LT”)
  - The early group is treated while the late group is still untreated → valid comparison.
2. Later-treated vs Earlier-treated (“LT vs ET”)
  - The late group becomes treated while the early group is already treated.
  - Comparing a newly treated group to an already-treated group is invalid under heterogeneity and introduces bias.
3. Treated vs Never-treated (“T vs N”)
  - Classic valid DID comparison.
TWFE collapses all these into:
\(\hat{\beta}^{TWFE} = \sum_{cells} w_c \cdot ATT_c\)
where the weights \(w_c\):
- are not necessarily positive,
- depend on group sizes and timing,
- overweight comparisons where groups have long differences in exposure.
Why it matters:
- If treatment effects vary across cohorts or over time (heterogeneous effects), the ET–LT and LT–ET comparisons produce biased and sometimes negative weights, causing TWFE to estimate nonsense results (e.g., wrong sign, non-monotonic event-study curves).
- Therefore, in staggered adoption, TWFE DiD does not recover the ATT.
Implication:
The Bacon decomposition is the key reason modern DID uses estimators like Callaway–Sant’Anna, Sun–Abraham, and Borusyak–Jaravel–Spiess, which avoid forbidden comparisons and recover proper ATT(g,t) values.

Q: How does staggered G×T DiD fundamentally differ from a single-timing 2×T event study?
A: In a 2×T event study, there is one treatment cohort (treated at time g) and one comparison group.
In staggered G×T DiD, every cohort has its own treatment date G_i, so each cohort has its own:
- pre-treatment window
- post-treatment window
- valid comparison groups
- parallel trends assumption
- set of ATT(g,t) parameters
Thus, staggered DiD is not “one event study”—it is many overlapping cohort-specific event studies, each requiring appropriate comparison groups and assumptions.
TWFE incorrectly averages these heterogeneous cohort effects, causing bias.

Q: What are the three main parallel trends assumptions in staggered G×T designs?
A: 1. PT-GT-Nev (parallel trends vs. never-treated only)
\(E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G=g] = E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G=\infty]\)
2. PT-GT-NYT (parallel trends vs. not-yet-treated)
\(E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G=g] = E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G>t]\)
3. PT-GT-all (parallel trends for all cohorts and periods)
\(E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G=g] = E_\omega[Y_{t}(0)-Y_{t-1}(0) \mid G=g'] \quad \forall g,g'\)
Notes:
- PT-GT-Nev is conservative (weaker assumption) but may have weak comparability.
- PT-GT-all is strongest—needed for Sun & Abraham, BJS (2024), etc.
- PT-GT-NYT is the middle ground and is the basis for Callaway & Sant’Anna (2021).

Q: Why does TWFE DiD break under staggered adoption?
A: Because TWFE:
1. Uses already-treated units as controls for later-treated units.
2. Imposes PT-GT-all, even if you didn’t want to.
3. Produces a weighted average of invalid 2×2 comparisons, including “late vs early treated.”
4. Allows negative weights (Bacon decomposition).
5. Blends dynamic effects and heterogeneity → biased and sign-flipped event studies.
Therefore, TWFE does not recover ATT(g,t) under treatment-effect heterogeneity.

Q: When should you not use “not-yet-treated” units as the comparison group in Callaway–Sant’Anna (2021)?
A: You cannot use not-yet-treated units if:
1. Groups treated soon after time t selected into treatment based on time-varying unobservables.
  - Example: states expanding Medicaid in 2016 might have decided based on rising mortality trends in 2014–15.
  - Then they do not mimic untreated potential outcomes for the 2014 cohort.
2. Their pre-treatment outcome trends are different from the treated cohort.
  - If pre-trends for a future-treated cohort differ from those of cohort g, they are invalid controls.
3. Anticipation or early behavioral adjustments occur in the future-treated group.
  - If units begin responding before treatment (e.g., policy announced early), they are no longer untreated counterfactual units.
4. A cohort’s untreated potential outcomes change because of impending treatment status.
  - Example: firms hire staff before minimum wage implementation → future-treated are not valid untreated units.
5. There is strategic timing or policy endogeneity in the adoption date.
  - If the timing g itself depends on recent outcomes, future-treated units’ trends do not represent untreated potential outcomes for earlier cohorts.
6. Policy exposure is correlated across cohorts (spillovers).
  - If a future-treated group is affected by earlier cohorts’ treatment, they are no longer untreated.
If future-treated groups show different pre-trends from cohort g before their treatment date → you cannot use them as controls for cohort g.

Q: Why do we need IPW, RA, or DR estimators in staggered DiD?
A: Because parallel trends may only hold after conditioning on covariates that predict untreated outcome growth.
Staggered DiD is a collection of 2×2 building blocks, each requiring:
\(E[ Y_t(0) - Y_{t-1}(0) \mid G=g, X ] = E[ Y_t(0) - Y_{t-1}(0) \mid G>t, X ]\)
If covariates matter and we don’t condition on them, identification of ATT(g,t) fails.
IPW, RA, and DR are methods that restore identification by constructing valid counterfactual trends conditional on X.

Q: What is the intuition behind Regression Adjustment (RA) for ATT(g,t) in staggered DiD?
A: RA builds a model for the untreated change in outcomes among the comparison (not-yet-treated) group:
\(m(X) = E_\omega[Y_t - Y_{g-1} \mid G>t, X]\)
Then it estimates:
\(ATT_{RA}(g,t) = E[Y_t - Y_{g-1} \mid G=g] - E[ m(X) \mid G=g ]\)
Interpretation:
Predict what would have happened to group g using the comparison group’s conditional trend function, then subtract it from the treated group’s observed trend.
Key point: RA depends heavily on correct specification of the outcome model m(X)

Q: What is the intuition behind inverse probability weighting (IPW) for staggered DiD?
A: IPW reweights the comparison (not-yet-treated) group so that their covariate distribution matches that of the treated cohort g.
Define the “generalized propensity score”:
\(p_{g,t}(X) = P_\omega(G=g \mid X, \{G=g \text{ or } G>t\} = 1)\)
IPW estimator:
- Upweights treated units by
\(1/p_{g,t}(X)\)
- Upweights comparison units by
\(1/(1 - p_{g,t}(X))\)
So treated and comparison groups become comparable in expectation.
IPW avoids modeling outcomes but relies on correct estimation of the propensity score.
A weighted difference-in-means where weights force covariate balance between treated cohort g and not-yet-treated units.

Q: What is the intuition behind doubly robust DiD in the CS setting?
A: The DR estimator combines RA and IPW:
- RA models the untreated outcome trend
- IPW reweights comparison units to match covariates
The DR estimator is consistent if either:
1. the RA model is correctly specified or
2. the IPW propensity model is correctly specified.
Not both—just one.
\(ATT_{DR}(g,t) = E\Bigg[ w_{g}(G)\,(Y_t - Y_{g-1}) - w_{g,t}(G,X) \bigl( (Y_t - Y_{g-1}) - E[Y_t - Y_{g-1} \mid X, G>t]\bigr) \Bigg]\)
Interpretation:
Start with IPW estimator, adjust it using the prediction error from RA.
If either prediction function or weighting function is correct → unbiased.

Q: Does James Heckman’s work play a role in IPW or doubly-robust (DR) estimators?
A: Yes — but indirectly.
Heckman’s classic work established that you cannot compare treated vs. untreated outcomes without accounting for selection on observables and selection on unobservables.
His main contributions that matter for IPW/DR:
1. The importance of conditioning on covariates (X) to identify causal effects in non-experimental settings.
→ This underlies the logic behind both RA and IPW.
2. The selection model framework clarified that untreated potential outcomes must be made comparable across treated and control groups.
→ Modern IPW methods explicitly reweight controls so their covariate distribution matches treated units, which is philosophically aligned with Heckman’s “selection on observables” logic.
3. Heckman–Ichimura–Todd (1997, 1998) directly contributed to the foundations of:
  - Propensity score weighting
  - Semiparametric DiD estimators
Their work on nonparametric matching and weighting in DiD is a precursor to modern IPW/DR DiD methods.
4. The double robustness idea comes from the general semiparametric efficiency literature, but Heckman’s work on bias from misspecification and on combining models with weighting influenced modern approaches.
But:
Heckman did not invent IPW or DR, and modern DR DiD (e.g., Callaway–Sant’Anna (2021)) does not rely on Heckman selection models, nor on the Heckman correction.
Heckman’s role is conceptual and historical, not mechanical.

Q: How does DiD change when treatment intensity is continuous or multi-valued instead of binary?
A: Instead of treatment ∈ {0,1}, units receive a dose \(d \in \mathbb{R}\) or from a multi-valued set.
Potential outcomes now depend on treatment intensity, not just treatment status:
\(Y_{i,t}(d)\)
Causal effects must compare different doses or a dose vs. no treatment.
Identification and estimation require stronger assumptions because untreated potential outcomes now vary across many possible treatment levels.

Q: What is the standard two-period setup for continuous DiD?
A: - Period 1: All units untreated → \(Y_{i,1}(0)\)
- Period 2: Units receive different doses \(D_i = d\).
- Potential outcomes written as:
\(Y_{i,2}(d) \equiv Y_{i,2}(0,d)\)
Groups are defined by their treatment dosage in period 2, not just treated/untreated.

Q: Define the dose-specific ATT
A: \(ATT(d \mid d_1) = E[\,Y_2(d) - Y_2(0) \mid D = d_1 \,]\)
Interpretation:
The effect of dose d relative to zero, for units who actually received dose \(d_1\).
Special case:
If \(d_1 = d\), this is the ATT for units who received dose \(d\).

Q: Define the dose-specific ATE
A: \(ATE(d) = E[\,Y_2(d) - Y_2(0)\,]\)
Interpretation:
Average effect in the population, not conditional on receiving a specific dose.

Q: What is the “per-dosage” treatment effect?
A: \(ATT^p(d \mid d_1) = \frac{ATT(d \mid d_1)}{d}, \qquad ATE^p(d) = \frac{ATE(d)}{d}\)
The per-dosage effect takes a treatment effect for a given intensity d and expresses it per unit of the treatment.
Think of it this way:
- If a policy increases funding, pollution, tax credits, or rent caps by different amounts across units, the level treatment effect will naturally be bigger for units that received a bigger dose.
- That means comparing effects across units is hard because part of the effect is just “you got more of it.”

Q: Define the Average Causal Response (ACR) for continuous treatment
A: \(ACR_T(d\mid d_1) = \left.\frac{\partial}{\partial l} E[Y_2(l)\mid D=d_1]\right|_{l=d}\)
Population version:
\(ACR(d) = \frac{\partial}{\partial d} E[Y_2(d)]\)
Interpretation:
The marginal effect of increasing the dose slightly around level d.
Analogue of the marginal treatment effect in continuous treatment frameworks.

Q: How do we define ACR when treatment doses are discrete?
A: For discrete doses \(d_j\):
\(ACRT(d_j \mid d_k) = E[Y_t(d_j) - Y_t(d_{j-1}) \mid D = d_k]\)
Population analog:
\(ACRT(d_j) = E[Y_t(d_j) - Y_t(d_{j-1})]\)
This is the discrete difference between adjacent doses.

Q: How does parallel trends change under continuous or multi-valued DiD?
A: Binary PT only requires untreated outcomes evolve similarly.
Continuous-treatment DiD requires:
\(E[Y_2(d) - Y_1(0) \mid D=d_1] - E[Y_2(0)-Y_1(0)]\)
must reflect causal dose effects, while untreated potential outcomes at every dose must obey parallel trends.
This is stronger than in binary DiD because it applies to entire potential outcome curves.

Q: What assumptions identify the dose-specific ATT(d | d1)?
A: 1. No anticipation:
\(Y_1(d)=Y_1(0)\)
2. Parallel trends in untreated potential outcomes:
\(E[Y_2(0)-Y_1(0) \mid D=d_1] = E[Y_2(0)-Y_1(0)]\)
3. Treatment intensity independent of untreated trends conditional on X (if using covariates).
Under these assumptions, identification is analogous to binary DiD but applied dose-by-dose.

Q: Why does identifying ACR require stronger assumptions than ATT(d|d1)?
A: Because ACR(d) requires comparing potential outcomes at multiple non-zero doses.
This demands:
- parallel trends for all doses,
- smoothness/continuity of the dose–response function,
- no anticipation.
Thus ACR requires parallel trends in potential outcomes under every dose, not just under no treatment.

Q: What do Callaway, Goodman-Bacon & Sant’Anna contribute to continuous DiD estimation?
A: They propose nonparametric estimators for:
- the dose–response ATT curve d \mapsto ATT(d|d)
- aggregated causal parameters
- smoothed or binned versions of ATT(d|d1)
Their approach extends binary DiD by estimating:
\(E[Y_2 - Y_1 \mid D=d] - E[Y_2 - Y_1 \mid D=0]\)
They also provide inference procedures and show how to visualize dosage heterogeneity.

Q: What do de Chaisemartin et al. (2024) study in multi-valued DiD?
A: They consider the case where units can have different doses in both period 1 and period 2.
They exploit:
1. Stayers: units whose dose does not change across periods.
2. No-carryover: past doses don’t affect future outcomes.
They define causal effects comparing changers to stayers:
\(ATT^p(d \mid d_1) \quad \text{and aggregated versions like } E[ATT(d|D)\mid D>0]\)
Their framework generalizes the usual ATT(d) to multi-period, multi-dose settings

Q: Why do two-way fixed effects regressions fail for continuous treatments?
A: Because the TWFE coefficient on the continuous treatment:
\(Y_{it} = \alpha_i + \gamma_t + \beta D_{it} + \varepsilon_{it}\)
does not recover:
- ATT(d|d1),
- ATE(d),
- per-dosage effects,
- or ACR(d).
Instead, TWFE produces a weighted average of many causal contrasts, with:
- negative weights,
- bias terms,
- non-interpretable combinations of dose contrasts,
- contamination from units whose untreated potential outcomes differ across doses.
As Callaway et al. (2021) show:
TWFE cannot be mapped to a single meaningful causal parameter.

Q: How do researchers interpret continuous-treatment DiD estimates?
A: Estimate the dose–response ATT curve:
\(d \mapsto ATT(d)\)
and examine:
- monotonicity (increasing effects with larger doses)
- convexity/concavity
- thresholds or nonlinearities
- saturation points
This helps interpret heterogeneous treatment intensity effects.

Q: Why is continuous-treatment DiD still methodologically developing?
A: - causal identification across many doses is harder than binary DiD,
- parallel trends must hold across dose-specific potential outcomes,
- treatments may not be smooth or continuous in practice,
- TWFE fails dramatically,
- aggregation and interpretation require careful weighting,
- nonparametric estimation is complex and data-hungry.
Current literature (CGS 2021/24; dCDV 2024) provides foundations, but many open problems remain.

Q: Why can TWFE regressions generate negative weights on treatment effects in staggered DiD designs?
A: TWFE generates negative weights because it uses already-treated units as comparison groups whenever treatment is staggered. In staggered adoption:
- Later-treated units become “treated,”
- Earlier-treated units are already treated and therefore serve (incorrectly) as “controls” in the regression.
Even under valid parallel trends, this creates comparisons like:
\(E[\Delta Y | G=2] - E[\Delta Y | G=1]\)
where group 1 is already treated. When this quantity is algebraically decomposed, the TWFE estimand becomes:
\(\beta_{TWFE} = ATT(2,2) \;+\; w_1 ATT(1,1) \;-\; w_1 ATT(1,2)\)
The key point:
- The term ATT(1,2) (the effect for the early group in the late period) enters with a negative sign, unless treatment effects are constant over time.
- This negative weighting is a mechanical property of OLS with staggered treatment, not a violation of assumptions.
Thus, TWFE averages together many 2×2 comparisons—some valid, some using already-treated units—with weights determined by OLS variance structure. When treatment effects are heterogeneous (across groups or over time), these negative weights distort β and can even flip the sign relative to the true average effect.
This is why TWFE can be severely biased in staggered adoption settings and why modern DiD literature recommends using estimators (e.g., Callaway–Sant’Anna, Sun–Abraham, Borusyak–Jaravel–Spiess) that avoid these contaminated comparisons.

Q: Explain the differences between:
1. Dose-specific ATT(d | d₁)
2. Per-dosage effect
3. Average Causal Response (ACR(d))
4. ATE(d) and other dose-aggregated parameters
A: 1. Dose-specific ATT(d | d₁)
\(ATT(d|d_1) = E[Y_2(d) - Y_2(0) \mid D = d_1]\)
- “Effect of receiving dose d vs 0”
- But measured among units who actually received dose d_1.
- If d_1 = d, it’s the ATT for units treated at level d.
- Measures level effects (bigger dose → mechanically bigger effect).
2. Per-dosage effect
\(ATT^p(d|d_1) = \frac{ATT(d|d_1)}{d}\)
- Normalizes the effect per one unit of treatment.
- Answers: “How effective is each additional unit of treatment?”
- Removes the scaling issue: large doses naturally produce large effects.
Use when comparing effectiveness, not total impact.
3. Average Causal Response (ACR(d))
\(ACR(d) = \frac{\partial}{\partial d} E[Y_2(d)]\)
For discrete doses:
\(ACR(d_j | d_k) = E[Y_2(d_j) - Y_2(d_{j-1}) \mid D = d_k]\)
- A marginal effect: “What happens if we increase the dose slightly from d?”
- Measures the local slope of the dose–response function.
- Not normalized by dose; it is the instantaneous marginal return to the treatment.
Use when the question is about incremental changes:
“How much does a small increase in treatment intensity change outcomes?”
4. ATE(d)
 and dose-aggregated effects
\(ATE(d) = E[Y_2(d) - Y_2(0)]\)
- Population-level version of ATT(d).
- Answers: “What is the effect if everyone got dose d?”
- Useful for counterfactual simulation and policy design.
There are also aggregated dose–response averages, such as:
\(E[ATT(D \mid D)] \quad \text{or} \quad \frac{E[ATT(D|D)]}{E[D]}\)
Used when researchers want one scalar summary of heterogeneous dose effects.