1
$\begingroup$

Recently, I read two papers by Dasgupta,2019 and Dong,2019 examining the impact of staggered laws in different dependent variables. When having a really long discussion with people in the comment section here, I accidentally recognized that these two papers use different treatment/control samples, which seems to against the well-explained idea about the switching "on" and "off" of treatment-or-control status based on treatment year shown here (this is where the baseline regression being explained well) and here.

In short, @ThomasBilach's idea is:

Once the exposure period isn't well-defined we must regress the outcome on unit fixed effects, time fixed effects, and a treatment dummy which 'turns on' in any unit-time combination where the policy is in effect, 0 otherwise.

This is how Dasgupta, 2019 explains the sample selection in his paper in the following way:

the treated group comprises all firms that are headquartered in countries that have passed a leniency law by year t. The control group comprises firms in countries that never adopted a leniency law in our sample period and firms headquartered in countries that adopted a leniency law at some later point of time.

Although I am doubting whether we can plot a pre-trend analysis based on this description, however this explanation seems to align with Thomas Bilach's idea as above.

However, Dong, 2019 documented that

In our estimation, we rely on the staggered nature of the passage of leniency programs to identify their causal effect on firm margins. We follow the standard approach used in the literature, which relies on the staggered passage of laws in different geographic regions in US. This allows us to compare the change in the margins of firms that were affected by the law to the contemporaneous change in the margins of the control firms that were headquartered in countries that had not yet passed such a law.

This description is different the description by Dasgupta, 2019, and as a result, does not align with Thomas Bilach's description.

To be simplified: from Thomas Bilach's idea and Dasgupta, 2019, if the U.S. passes a laws in 1993 and Australia passes a law in 2004, it means that the U.S. can be a control for Australia, but this is not the case based on the description of provided by Dong, 2019.

So the main question is, it seems that Dong, 2019 is using the staggered DID or generalized DID but they seem not to follow this method. I am doubting if I am misinterpreting them because the two papers Dasgupta, 2019 and Dong, 2019 have the same author (Alminas).

$\endgroup$
3
  • $\begingroup$ @usεr11852 Thank you for helping me clarify my question, I just added the main question at the bottom of my post already. $\endgroup$
    – Louise
    Jun 2 at 0:28
  • 3
    $\begingroup$ In the future either tag my full name or just reference the post. I wouldn’t want people to just see “Bilach” and get confused. $\endgroup$ Jun 2 at 1:02
  • 2
    $\begingroup$ @ThomasBilach I am so sorry for that, it is my big mistake. I updated your full name already, I hope that I did not get on your nerves. $\endgroup$
    – Louise
    Jun 2 at 1:07
3
+50
$\begingroup$

First, I don't think I make the claim that the treatment is switching 'on' and 'off' in the referenced research. I simply state in other posts that the "generalized" difference-in-differences estimator may accommodate intermittent exposures. The papers you cite investigate the effects of a staggered treatment. Treated countries adopt at widely different times. Some start early. Some start late. However, none of the treatments 'turn off' over time according to my understanding, though this estimator may accommodate a reversal of treatment. In my understanding of Dasgupta's work, once a country adopts a leniency law it remains in effect for the entire duration of the panel.

Once you decompose the "generalized" DD estimator you'll find out it's actually a weighted average of (1) comparisons between early-adopters and late-adopters over the periods when the late-adopters have yet to be treated, (2) comparisons between early-adopters and late-adopters over the periods when the early adopters were already treated, and (3) comparisons between different timing groups (e.g., early-adopters or later-adopters) and the never-treated group, assuming you even have a group of never-receivers. Note how a treated entity doesn't just drop out of the model once it's treated at time $t$. Previously treated entities still serve as counterfactuals for those treated much later. So the variation comes from comparing treated firms with untreated firms, but also in the timing impact of the laws. It actually exploits all possible two-group/two-period (2x2) comparisons present in your data.

Now it's important to note that the causal estimand is plausibly unbiased if we assume constant treatment effects. However, if effects change over time, especially for the early-receivers, then it may completely offset the stability of the trends as the late-receivers become eligible for treatment. For example, the immediate effect of a law is likely different than the effects observed downstream. If we suspect strong treatment effect heterogeneity, then the "changes" in treatment effects from all the 2x2 comparisons get subtracted from the overall DD estimate. The result is actually a "variance-weighted" average of cross-group treatment effects where some of the weights may be negative. One of the major implications is your least squares estimate may place undue weight on entities with more variation in their treatment status. Thus, the entities exposed to a treatment very early may receive less weight than those treated later in the sample period. Andrew Goodman-Bacon (2019) delves into this decomposition in far more detail here.

The authors you cite may have circumvented this problem by subjecting the early- and late-adopter firms to different analyses. For example, you could try running a simple 2x2 DD equation on the subset of early- and late-adopter firms—separately. But given that the timing of leniency laws vary so widely across jurisdictions, I don't think it's a worthwhile endeavor.

I agree with you that their plots of the "group trends" is suspicious at first blush. It's hard to define the periods surrounding the event year when the adoption periods vary widely across treated countries. Is it possible to know when a control firm is 2 periods before their event if they never espoused the new law? Well, they state the following in Section 3 on page 2600:

[T]he control firms are all firms in the same industry in countries that had not passed a leniency law in the 7 years surrounding the event date.

In my estimation, they used firms in the non-adopter countries but in the same industry to create the control group trend. In other words, they're assuming the untreated firms in the same SIC3 industry would have adopted the law around the same time as the treated firms in the same SIC3 industry.

Typically in event study frameworks we plot the coefficient values and not the raw trends across treatment/control groups. Thus, it doesn't appear to be a formal "pre-trends" test in my opinion. Their assessment of the parallel evolution of the trends seems rather ad hoc in my estimation, but warranted given the staggered nature of their treatment.

$\endgroup$
17
  • 1
    $\begingroup$ In regard to your first comment, you're correct. The policy dummy 'turns on' (i.e., switches from 0 to 1) in their respective adoption periods. Any country not adopting a leniency law is coded 0 in all periods. Note we're not talking about leads or lags. Based upon my reading of the research, the treatment is permanent, at least during the sample period. The paper offers no indication that the treatment reverses (i.e., switches from 1 back to 0) in any country before 2012. $\endgroup$ Jun 3 at 18:18
  • 1
    $\begingroup$ The choice of the appropriate "event window" is somewhat arbitrary, but I'm sure the authors had their reasons. Typically, we care more about what's happening around the exposure period. In other words, we want to restrict attention to a specific "event window" where we can exploit the timing of the intervention. Effects should be more pronounced within this window. Is it worth plotting the effect 10 or even 20 periods after treatment? Maybe. But if effects decay shortly after treatment is administered, then the effects in the later periods may be less important. $\endgroup$ Jun 3 at 18:30
  • 1
    $\begingroup$ The adoption periods may overlap across countries. In fact, if a country stays in the treated condition after a leniency law goes into effect, then they must overlap. This assumes, of course, that the panel is balanced. $\endgroup$ Jun 3 at 18:48
  • 1
    $\begingroup$ In regard to their plot, they more than likely used some 'industry pairing' method and assumed the non-adopter firms would have taken a similar trajectory, but I can't be sure. If it's really bugging you, I often found it helpful to reach out to the authors directly. I've found that if I crafted a respectful e-mail asking about their research, most seem happy to help clear up any confusion. $\endgroup$ Jun 4 at 17:47
  • 1
    $\begingroup$ As for your other concern, it's accepted to keep a policy dummy 'turned on' if that policy is still in effect in subsequent periods. So if a country adopts a leniency law in 2003 and it remains in effect, then it 'turns on' in 2003 and stays on. Now, let's say some countries repeal it in 2008. Then those countries where the law was nullified now 'turn off' in 2008 and all subsequent periods. That policy dummy should reflect reality as closely as possible! $\endgroup$ Jun 4 at 17:57

Your Answer

By clicking “Post Your Answer”, you agree to our terms of service, privacy policy and cookie policy

Not the answer you're looking for? Browse other questions tagged or ask your own question.