Setup

Same staggered panel data continuous treatment design as Session 1:

• Two periods \(t=1,2\);
• No one treated at \(t=1\);
• Continuous dose \(D_i\) realized at \(t=2\)

Motivating Parallel Trends

The most common way to “more primitively” motivate the parallel trends assumption is as a combination of the following two assumptions (Ashenfelter and Card 1985; Angrist and Krueger 1999; Ghanem et al. 2024; Marx et al. 2025):

• Latent unconfoundedness says that we could recover \(\ATT(d \mid d)\) if we could find units in dose group \(d\) and untreated units with the same \(\eta_i\) and compare their outcomes
• The previous comparison is infeasible, though, because \(\eta_i\) is unobserved

Motivating Parallel Trends

The most common way to “more primitively” motivate the parallel trends assumption is as a combination of the following two assumptions (Ashenfelter and Card 1985; Angrist and Krueger 1999; Ghanem et al. 2024; Marx et al. 2025):

• Alternatively, you can view this as “selection into being treated on time-invariant unobservables”: \[ \indicator{D_i > 0} = m_0(\eta_i) + u_i \text{ with } u_i \independent \big(Y_{it=1}(0), Y_{it=2}(0)\big) \bigm| \eta_i \]
• No restrictions on selection into a particular dose at all

Motivating Parallel Trends

The most common way to “more primitively” motivate the parallel trends assumption is as a combination of the following two assumptions (Ashenfelter and Card 1985; Angrist and Krueger 1999; Ghanem et al. 2024; Marx et al. 2025):

• Under linearity of untreated potential outcomes, difference out \(\eta_i\) and then parallel trends holds immediately by latent unconfoundedness
• However, these assumptions do not imply strong parallel trends—notice that the assumptions do not restrict potential outcomes \(Y_{it=2}(d)\) for \(d>0\) at all.

Motivating Strong Parallel Trends

We can extend the notion of latent unconfoundedness as follows:

• Extends latent unconfoundedness to holds for all potential outcomes, not just untreated ones
• Up to \(\eta_i\) being unobserved, it is exactly the same assumption that you would see in the literature on continous treatment and dose response functions (Hirano and Imbens 2004)

Motivating Strong Parallel Trends

We can extend the notion of latent unconfoundedness as follows:

• “Selection into dose on time-invariant unobservables”: \[D_i = m(\eta_i) + v_i \text{ with } v_i \independent \big(Y_{it=1}(0), Y_{it=2}(d) \big) \bigm| \eta_i\]
• Conditional on \(\eta_i\), does not allow for units that experience dose \(d\) to have systematically better outcomes at dose \(d\) than units that experienced a different dose.

Motivating Strong Parallel Trends

We can also consider linear models for all potential outcomes:

• Additive separability for parallel trends
• Coefficient on \(\eta_i\) can vary with \(t\) and/or \(d\)
• No tricks—this is exactly the same setup we would have in a linear model for potential outcomes if \(\eta_i\) were observed

School Closures Example

Back to Session 1’s running example where \(dose\) = length of Covid school closure, \(outcome\) = test scores

• \(\eta_i\): school’s unobserved student ability

• \(\theta_{t=2,d}\): the ability-neutral part of the dose response, e.g., the component of lost instructional time/disruption that hits any school closed for length \(d\), regardless of its students’ baseline ability

• \(\beta_{t=2,d}\): how strongly baseline ability \(\eta_i\) translates into test scores, given closure length \(d\) — i.e., varies with \(d\) if high ability schools respond differently to different lengths of closures than low ability schools

  • Would be increasing in \(d\) if high ability schools are more resilient to long closures than low ability schools.

Does Strong Parallel Trends Hold in This Model?

Applying the same argument as in Session 1: \[ \begin{aligned} \E[\Delta Y \mid D=d_h] - \E[\Delta Y \mid D=d_l] &= \ATT(d_h|d_h) - \ATT(d_l|d_l) \\ &= \underbrace{(\theta_{t=2,d_h} - \theta_{t=2,d_l}) + (\beta_{t=2,d_h} - \beta_{t=2,d_l}) \E[\eta \mid D=d_h]}_{\textrm{Causal Response}} \\ &+ \underbrace{\beta_{t=2,d_l} \Big( \E[\eta \mid D=d_h] - \E[\eta \mid D=d_l] \Big)}_{\textrm{Selection Bias}} \end{aligned} \]

• Learning about \(\beta_{t=2,d_l}\) directly does not seem possible—e.g., \(\E[\Delta Y \mid D=d_l] - \E[\Delta Y \mid D=0]\) includes \(\beta_{t=2,d_l}\) but also differences in \(\E[\eta \mid D=d_l]\) and \(\E[\eta \mid D=0]\), which are unobserved

• Making assumptions about \(\beta_{t=2,d_l}\) would also be difficult to justify and infeasible to check in practice

Does Strong Parallel Trends Hold in This Model?

Applying the same argument as in Session 1: \[ \begin{aligned} \E[\Delta Y \mid D=d_h] - \E[\Delta Y \mid D=d_l] &= \ATT(d_h|d_h) - \ATT(d_l|d_l) \\ &= \underbrace{(\theta_{t=2,d_h} - \theta_{t=2,d_l}) + (\beta_{t=2,d_h} - \beta_{t=2,d_l}) \E[\eta \mid D=d_h]}_{\textrm{Causal Response}} \\ &+ \underbrace{\beta_{t=2,d_l} \Big( \E[\eta \mid D=d_h] - \E[\eta \mid D=d_l] \Big)}_{\textrm{Selection Bias}} \end{aligned} \]

• Instead, we will think about trying to determine the plausibility of “no selection” holding (i.e., \(\E[\eta \mid D=d_h] - \E[\eta \mid D=d_l] = 0\)).

Background

In Callaway et al. (2025), we introduce a notion of “close comparison groups”

• Setting of that paper: binary treatment, multiple pre-treatment periods, multiple comparison groups, looking for a way to relax the parallel trends assumption, and we look for pockets of simple identification

• Groups that are “alike” in terms of pre-treatment levels of outcomes are “close comparison groups”

• If you can find such groups, you can get very robust identification of causal effects (i.e., robustness to the identification strategy)

CCGs Adapted to a Continuous Treatment Setting

As discussed above, difference-in-differences attempts to allow for selection on time-invariant unobservables by differencing them out.

But we can look at the level of pre-treatment outcomes to inform us about the distribution of unobservables across dose groups.

Same Pre-Treatment Mean Implies Same Mean of

For some dose group \(l\), its mean of untreated potential outcomes is given by:

Same Pre-Treatment Mean Implies Same Mean of

For some dose group \(l\), its mean of untreated potential outcomes is given by:

\[ \begin{aligned} \E[Y_{t=1} \mid D=l] &= \E[Y_{t=1}(0) \mid D=l] \hspace{150pt}\\ &= \theta_1 + \E[\eta \mid D=l] \end{aligned} \]

Implications

In a similar fashion to using pre-treatment periods to validate the parallel trends assumption, we can use pre-treatment periods to validate the “no selection”

• We can do this globally,
• Find regions where the pre-treatment mean is flat, or
• Find regions where the pre-treatment mean is flat conditional on covariates

It rationalizes interpreting those regions as being regions where strong parallel trends is plausible, and suggests that we can recover locally comparable causal effects in those regions, e.g., \(\ACR(d)\) in these regions.

Application

Same empirical setting as Session 1:

• Acemoglu and Finkelstein (2008)’s study of the 1983 Medicare PPS reform.
• Dose = hospital’s pre-reform Medicare share
• outcome = capital-labor ratio (depreciation share)
• In session 1, we mainly looked at average outcomes before and after the treatment, but here we will use adjacent years instead, using 1982 as the base period.
  • Treatment effects: 1982 vs. 1983, 1984, 1985, 1986
  • Plus two more placebos marching up to 1982: 1980 vs. 1981, 1981 vs. 1982

Results: ATT(d|d)

Results: ATT(d|d)

Results: ATT(d|d)

Results: ACR(d)

Results: ACR(d)

Results: ACR(d)

Pre-Test: ATT(d|d)

Pre-Test: ATT(d|d)

Pre-Test: ATT(d|d)

Pre-Test: ATT(d|d)

Two of three fail — 1980-81 is close to 0, but 1981-82 (\(\widehat{\ATT}=-0.22\)) and 1982-83 (\(\widehat{\ATT}=+0.20\)) are both significant, in opposite directions

• 1982-83 could reflect anticipation: PPS was legislated in April 1983, months before its October 1983 effective date
• 1981-82 has no such story — both years are firmly pre-treatment. This looks like genuine year-to-year instability, not just anticipation

Pre-Test: Same Pre-Treatment Levels

Next, we check for regions of close comparison groups

Pre-Test: Same Pre-Treatment Levels

Pre-Test: Same Pre-Treatment Levels

Pre-Test: Same Pre-Treatment Levels

Pre-Test: Same Pre-Treatment Levels

The flat region is remarkably stable across three separate years: roughly dose \(0.35\) to \(0.70\) in every one of 1980, 1981, and 1982

• This is what we’d expect if the flatness reflects a persistent hospital characteristic (\(\eta_i\)), not a fluke of any one year
• Use 1982’s (largest) flat region as a single canonical “close comparison group” definition, applied everywhere next

ACR(d): Close Comparison Region

Same ACR(d) curves as before, now with the canonical region (dose \(0.35\)-\(0.70\)) highlighted, plus its density-weighted average (i.e., a local \(\ACR\) in the close comparison region)

ACR(d): Close Comparison Region

ACR(d): Close Comparison Region

ACR(d): Close Comparison Region

ACR(d): Close Comparison Region

ACR(d): Close Comparison Region

ACR(d): Close Comparison Region

Summary of Application

It appears that:

1. Parallel trends seems to be violated in pre-treatment periods
2. Checking the levels of pre-treatment outcomes as a function of the dose suggested that there were pockets of no selection
3. Cross-dose comparisons are more likely to deliver causal effects in those pockets (i.e., a local version of strong parallel trends)
4. The estimates were noisy, but often negative. They don’t provide any evidence that the Medicare policy increased capital labor ratios.

Conclusion

Using pre-treatment periods to assess the plausibility of strong parallel trends is challenging because only untreated potential outcomes are observed in those periods.

However, the levels of outcomes in pre-treatment periods across different dose groups provides evidence about difference in the unobserved heterogeneity driving their outcomes.

If differences in observed pre-treatment levels of outcomes are small, it suggests that differences in unobservables are small too.

If differences in unobservables are small, then strong parallel trends is more plausible, and cross-dose comparisons of trends in outcomes can be interpreted as approximately causal in those regions.