# Causal Duration Analysis with Diff-in-Diff††thanks: We thank seminar
participants at Brown University and The University of Surrey, and those who
attended the presentation of this paper at the European Winter Meeting of the
Econometric Society 2023 for helpful comments and feedback. We would also like
to thank colleagues at UCL for their insights, particularly Christian
Dustmann, Liyang Sun, Dennis Kristensen, and Andrei Zeleneev, as well as
others who attended internal presentations of this work.

Ben Deaner and Hyejin Ku
University College London b.deaner<EMAIL_ADDRESS>
###### Abstract

In economic program evaluation, it is common to obtain panel data in which
outcomes are indicators that an individual has reached an absorbing state. For
example, they may indicate whether an individual has exited a period of
unemployment, passed an exam, left a marriage, or had their parole revoked.
The parallel trends assumption that underpins difference-in-differences
generally fails in such settings. We suggest identifying conditions that are
analogous to those of difference-in-differences but apply to hazard rates
rather than mean outcomes. These alternative assumptions motivate estimators
that retain the simplicity and transparency of standard diff-in-diff, and we
suggest analogous specification tests. Our approach can be adapted to general
linear restrictions between the hazard rates of different groups, motivating
duration analogues of the triple differences and synthetic control methods. We
apply our procedures to examine the impact of a policy that increased the
generosity of unemployment benefits, using a cross-cohort comparison.

Many important topics in applied economics involve durations. To name a few,
the impact of unemployment insurance on the length of unemployment spells
(Katz & Meyer, (1990), Hunt, (1995), Lalive et al., (2006), Lalive, (2007),
Card et al., (2007), Chetty, (2008), Schmieder et al., (2012), Schmieder et
al., (2016), Lichter & Schiprowski, (2021), and others), the effect of divorce
laws on marriage duration (Friedberg, (1998), Gruber, (2004), Wolfers,
(2006)), the strength of residency rules on the rate at which refugees pass
language tests (Arendt et al., (2024)), and the consequences of criminal
justice policies on the rate of recidivism or probation revocation (Schmidt &
Witte, (1989), Bhuller et al., (2020), Rose, (2021)). In settings like these,
available data often consist of panels in which the outcome is a binary
indicator that an individual has entered an absorbing state. For example, an
indicator that an individual has exited unemployment by a particular date.
Difference-in-differences is a popular tool for policy-evaluation with panel
data, but when the data take the form just described, the parallel trends
assumption generally fails.

To fix ideas, consider the case in which the outcome indicates exit from
unemployment. Suppose that some individuals receive an increase in
unemployment benefits at a particular point in time while others do not. The
foundational assumption of diff-in-diff is that, absent the policy of
interest, the difference in mean outcomes between the treated and untreated
groups would remain fixed. If a sufficiently large share of individuals
eventually exit unemployment, then mean outcomes will tend to converge over
time, even absent any treatment effect.111Apart from in the special case in
which mean outcomes are identical between the two groups. This entails a
failure of parallel trends and may result in severely biased and inconsistent
estimates of treatment effects.

In response, we consider alternative approaches based on insights from
duration analysis. Rather than assume parallel trends between mean potential
outcomes, we suppose that the difference between group-specific counterfactual
hazard rates is constant. This condition is consistent with the convergence of
counterfactual mean outcomes over time and thus the convergence does not imply
inconsistency of the corresponding causal estimates. The alternative
assumption motivates a simple fix. Instead of performing diff-in-diff using
mean outcomes, we apply the same procedure using a particular function of the
mean outcomes and the time period. We sidestep any estimation of the hazard
rates themselves, and our analysis entirely avoids the need to specify an
explicit model for the hazard function.

To be precise, in place of the mean outcome $E[Y_{i,t}|G_{i}=k]$, where $t$
indexes time periods, $i$ individuals, and $G_{i}$ is the group to which
individual $i$ belongs, we use the ‘time-average hazard’, denoted
$\bar{H}_{k,t}$, which can be written in terms of mean outcomes. This object
is the average of the hazard rate over the continuous period between times $1$
and $t$. Under our assumptions there is a fixed difference between the time-
average hazards of the different groups under the no-treatment counterfactual.
Thus we can perform difference-in-differences using this alternative object.
We may then invert the definition of the time-average hazard to recover
counterfactual mean outcomes and average treatment effects.

Note that the counterfactual mean outcome, understood as a function of time
since the start of a spell, is precisely the cumulative distribution function
of counterfactual durations. Thus our approach can produce estimates of the
whole distribution of counterfactual durations, rather than say, the mean
duration under a no-policy counterfactual.

Diagnostics like placebo tests and the standard test for pre-treatment
parallel trends can be adapted straight-forwardly to our setting. Where
standard tests use the mean outcome, we again use the time-average hazard
rate. Analogous with vanilla diff-in-diff, one can perform informal visual
inspections to assess whether parallel trends in time-average hazards holds in
the pre-treatment period.

Adjusting for covariates can be important for credibly identifying causal
effects in difference-in-differences. If there is covariate imbalance between
treatment and control groups in diff-in-diff, then parallel trends may fail,
even if it holds within each covariate stratum (say, within each demographic
subgroup). We adapt our hazard diff-in-diff approach to allow for such cases
by employing a simple propensity score weighting when we calculate the time-
average hazard. This avoids the difficulties of partial likelihood estimation
of proportional hazard models with discretised time periods.

Our approach extends beyond the assumption of a fixed difference between
hazard rates. Rather, we can accommodate any fixed linear relationship between
the hazard rates of different groups. Thus our approach applies if there is a
fixed difference in log hazard rates, which is equivalent to a particular
proportional hazards specification. In the case of multiple untreated groups
we can obtain a duration analogue of the triple differences estimator and of
the synthetic control method. As with our duration diff-in-diff approach,
estimation differs from standard approaches only in the use of transformed
mean outcomes.

We apply our methods to the setting of Lalive et al., (2006). The authors in
that study evaluate the impact of a policy that increased the generosity of
unemployment insurance benefits for unemployed Austrian workers. The authors
identify causal effects by exploiting the presence of individuals who were
ineligible for the benefit changes. They estimate a flexible parametric
duration model and from their estimates they recover causal effects.

In contrast, we identify causal effects using a cross-cohort comparison. We
employ our methods in order to estimate the impact of an extension to the
potential benefit duration (PBD). We adjust for the calendar date at which an
unemployment spell begins using our covariate re-weighting strategy. Thus our
estimates are robust to differential trends in job-seeking between individuals
who become unemployed in different parts of the year. We obtain similar
results to the authors of the original study, however we do so while avoiding
estimation and specification of the hazard function, and without the need for
numerical optimization of a likelihood. Moreover, the transparency of our
approach allows us to both visually and formally assess whether there are
parallel trends over the pre-treatment period. We find a statistically
significant positive impact of PBD on unemployment duration with strongly
positive estimates shortly following treatment which then taper off. We are
unable to reject parallel trends in hazard rates even at the $50\%$ level.

We evaluate the finite-sample performance of our methods in a simulation
study. The results also demonstrate the potential for standard diff-in-diff to
produce severely misleading estimates in duration settings. The simulation
results are available in Appendix A.

In sum, the present paper suggests a simple means of adapting existing
difference-in-differences and synthetic control methods to settings with
duration data. Whereas standard procedures extrapolate the relationship
between mean outcomes for different groups forward in time, we instead
extrapolate the relationship between these groups’ time-average hazard rates,
which are known functions of mean outcomes and therefore easily estimated from
the data. What is crucial here is that we retain the intuitive appeal of diff-
in-diff. One of the key benefits of diff-in-diff and related methods is that
one can visually assess whether the assumption of a stable linear relationship
holds in the pre-treatment period, and assess the magnitude of any deviation
from this condition. Because we simply shift the objects to which these
methods are applied, our approach allows researchers to perform similar visual
inspections, as required for effective causal event studies.

### Related Literature

We are not the first to suggest an extension of differences-in-differences to
duration settings. Proportional hazard models (Cox, (1972)) with a diff-in-
diff-type linear index are considered by Hunt, (1995), Wu & Wen, (2022), and
Lalive et al., (2006). Wu & Wen, (2022) show that parallel trends cannot hold
when the data are generated by the proportional hazards model. Hunt, (1995)
suggests an approximate partial likelihood estimation procedure for the
coefficients of the linear index in a proportional hazard diff-in-diff
specification, and Lalive et al., (2006) employ maximum likelihood estimation.
Wu & Wen, (2022) consider estimation in the two-period case. In both Wu & Wen,
(2022) and Hunt, (1995), interest is in the estimation of the coefficients on
the binary indicators in the linear index, rather than average treatment
effects.

The proportional hazard diff-in-diff model is a special case of the more
general linear restrictions that we consider in the present work. Our approach
avoids maximum likelihood estimation in favor of simple and transparent
imputation of time-average hazards that closely resembles classic diff-in-
diff. The simplicity and transparency of our approach is important not only in
that it facilitates practical application of our methods, but because it
allows us to both visually and formally test for pre-treatment parallel
trends, much as in standard diff-in-diff. Our preferred specification assumes
a fixed level difference in the hazard rates rather than a fixed ratio. This
has the advantage of allowing for a simple means of flexibly incorporating
covariates via propensity score weighting.

Also related to our approach is the literature on non-linear difference-in-
differences. These papers, usually motivated by a limited dependent variable,
specify a generalized linear model (GLM) in which the outcome is a non-linear
transformation of a linear index with a diff-in-diff form. A number of
empirical papers estimate the coefficients in a GLM diff-in-diff model. For
example, Gruber & Poterba, (1994) and Eissa, (1996). Puhani, (2011) considers
the interpretation of the coefficients in these models.

Motivation for GLM diff-in-diff models is discussed in Blundell et al.,
(2004), Blundell & Costa Dias, (2009), Lechner, (2011), and Wooldridge,
(2023). The general strategy in Blundell et al., (2004) and Wooldridge, (2023)
is to transform mean outcomes by inverting the link function in a GLM and to
perform diff-in-diff on the transformed means. Re-applying the link function
then recovers counterfactual mean outcomes and thus treatment effects. Their
specifications are motivated by latent variable models for the discrete
outcomes. Thus in those works, the link function is determined by an a priori
assumption that an unobserved noise term follows a known parametric
probability distribution. In our case, the form of link function follows from
the duration structure of the data. Works in which the link function is
estimated using sufficiently rich pre-treatment data include Ashenfelter &
Greenstone, (2004) and Athey & Imbens, (2006). The latter suggest a
nonparametric approach that is valid under weaker conditions than the GLM
diff-in-diff model.

In addition, we differ from Wooldridge, (2023) in the manner in which we
adjust for covariates. Rather that incorporate covariates in the linear index
inside of a link function, we instead suggest a propensity score weighting
approach that is valid under the assumption of parallel trends in covariate
stratum-specific hazard rates but allows trends to differ between strata.

By proposing a simple and transparent extension of diff-in-diff to duration
settings, we extend the ever-growing literature on difference-in-differences.
For recent surveys see for example Roth et al., (2023) and de Chaisemartin &
D’Haultfœuille, (2023).

In our empirical application we employ a cross-cohort comparison in which the
time period for a given individual is relative to the start of their
unemployment duration. This is the same approach taken in Van Den Berg,
(2020). However in that work, the authors employ an identification strategy
based on regression discontinuity design for nonparametrically estimated
hazard rates.

There is a sizable literature on causal analysis using duration data (see
e.g., Abbring & Van Den Berg, (2003) and Abbring & Heckman, (2007)). In the
seminal paper of Abbring & Van Den Berg, (2003) and similar works, researchers
achieve identification under assumptions on the treatment process, its
relation to individual heterogeneity, and the separability of unobserved
heterogeneity in individual-level hazard rates. Our approach differs from this
in its foundation. Rather than begin with an individual-level duration model
incorporating heterogeneity, our analysis is premised upon an assumption
concerning group-level hazard rates. This is closer in spirit to standard
diff-in-diff which, while sometimes written as an individual-level model with
two-way fixed effects, can be understood as a method for imputing mean
counterfactual outcomes under a group-level parallel trends assumption. An
advantage of the group-level approach is that it can accommodate settings in
which there may be substantial spill-overs and interaction effects among
individuals in the same group, and in addition it applies to settings in which
only group-level data is available.

In some cases it may be possible to apply difference-in-differences using the
durations themselves as outcomes as in Lichter & Schiprowski, (2021). Consider
again the unemployment example and suppose some individuals are ineligible for
the increase in benefits. One might perform diff-in-diff by taking the
difference in the mean unemployment durations between those who became
unemployed before and after the reform and seeing how this varies with
eligibility for the benefits increase. This approach differs from ours both in
the settings to which it is applicable and in the causal objects it
identifies.

First, consider that this alternative strategy identifies causal effects using
variation in the start date of unemployment spells, whereas our method is
applicable even if all spells in the data begin on the same date. In addition,
suppose that the policy change applies to those in ongoing unemployment
spells, as is common in practice. Then the group of eligible individuals who
became unemployed prior to the reform will contain some treated individuals,
and dropping these from the sample would lead to selection bias. Our approach
avoids this problem.

Using durations as outcomes identifies distinct causal objects compared with
our approach. Suppose that the policy impacts not only time spent in
unemployment, but also who becomes unemployed. This compositional change
represents an additional channel through which the policy might impact
unemployment durations. Because we follow the same fixed set of individuals
over time, we isolate the behavioral response of individuals in ongoing
spells. Finally, our approach recovers a counterfactual cumulative
distribution of durations evaluated at certain points in its support, whereas
the alternative identifies the counterfactual mean of durations.

##  1 Motivation and Background

We sample binary outcomes $Y_{i,t}$ for individuals $i=1,...,n$ at periods
$t=1,..,T$. Each individual belongs to a group $G_{i}$ where group membership
is constant over time. An outcome of $1$ indicates that an individual has
entered an ‘absorbing state’ and so all future outcomes for that individual
are also equal to $1$. Individuals in group $1$ receive an intervention at
some point between periods $t^{*}-1$ and $t^{*}$ and we wish to assess the
impact of this intervention on the evolution of the outcomes of individuals in
that group.

Note that the data need not contain the exact lengths of spells. Rather, we
only need to know whether or not a spell has ended by a particular length of
time. For example, if the time increments are weeks, then we need only know
whether or not a given duration has ended by the $t$-th week for $t=1,...,T$,
not the exact moment at which it ended. While we focus on the case of discrete
time increments, our approach can be adapted straightforwardly to accommodate
time increments of varying lengths.

In order to define causal effects of the treatment, we consider a
counterfactual in which there is no intervention on group $1$. We denote by
$Y_{i,t}^{(0)}$ the outcome under this counterfactual at time $t$ for
individual $i$. We sometimes refer to $Y_{i,t}^{(0)}$ as an ‘untreated
potential outcome’, although this differs from the standard definition in that
the counterfactual is defined in terms of an intervention on group $1$ rather
than an individual-level treatment. We use the superscript ‘$(0)$’ to indicate
counterfactual values throughout this work.

Our primary object of interest is the time-$t$ average treatment effect for
individuals in the treated group where $t^{*}\leq t$. This is the average
difference between the outcome for a randomly sampled individual in the
treated group $1$ at time $t$, and that individual’s outcome in the
counterfactual world in which there is no intervention. This is defined as
follows:

$\tau_{t}=E[Y_{i,t}-Y_{i,t}^{(0)}|G_{i}=1]$

Note that $E[Y_{i,t}^{(0)}|G_{i}=1]$ is the counterfactual cumulative
distribution function (CDF) of the durations of individuals in group $1$
evaluated at $t$. Therefore, if treatment effects are identified, then so too
are the values of the counterfactual CDF of durations evaluated at each
discrete time increment.

To illustrate, consider two schools $1$ and $2$. We sample $n$ students each
of whom attends one of the two schools. If $G_{i}=k$ then individual $i$
attends school $k$. Data is available from periods $t=1,...,T$. The students
in each school have the opportunity to sit and pass an English proficiency
exam. If a student $i$ has passed the exam by time $t$ then $Y_{i,t}=1$ and
otherwise $Y_{i,t}=0$. We suppose that at a time between $t^{*}-1$ and
$t^{*}$, the students in school $1$ receive some educational intervention,
where $t^{*}$ is known.

The binary indicator $Y_{i,t}^{(0)}$ is equal to $1$ if and only if student
$i$ would have passed the test by time $t$ in a counterfactual world in which
there is never any intervention on school $1$. In this setting, the time-$t$
average treatment effect $\tau_{t}$ is the difference between the share of the
student population in school $1$ who have passed the test by time $t$ versus
the proportion who would have passed under the counterfactual in which there
is no intervention on school $1$.

Assumptions 1 and 2 formally impose some elementary properties of the factual
and counterfactual outcomes implicit in the discussion above.

######  Assumption 1 (Absorbing State).

$Y_{i,t}$ is a binary random variable and $Y_{i,t}=1$ implies $Y_{i,s}=1$ for
all $t\leq s$. The same holds for the potential outcomes $Y_{i,t}^{(0)}$.

######  Assumption 2 (No Anticipation/Spill-Overs).

i. $1<t^{*}$ and for all $t<t^{*}$, $Y_{i,t}=Y_{i,t}^{(0)}$, ii. For all
$t\geq t^{*}$, if $G_{i}>1$ then $Y_{i,t}=Y_{i,t}^{(0)}$.

Assumption 1 states that having an outcome of $1$ is absorbing state. This
means that if an individual has an outcome of $1$ at time $t$, then that
individual’s outcome is equal to $1$ in all future periods, and similarly for
potential outcomes. In the schools setting this follows simply from the
definition of the outcome: a student cannot un-pass the exam.

Assumption 2 imposes conditions on potential outcomes that are standard in
difference-in-differences. We assume that individuals do not anticipate
treatment, and so observed outcomes in periods strictly prior to $t^{*}$ are
identical to those in the counterfactual world in which there is no
intervention. A no-anticipation condition was introduced into the literature
on causal duration analysis by Abbring & Van Den Berg, (2003). In addition, we
assume there are no spill-overs between groups. That is, the treatment of
students in school $1$ has no impact on students in other schools. More
formally, the potential outcomes of students in other schools under the no-
treatment counterfactual are equal to their realized outcomes. However, this
does not rule out spill-overs between individuals in the same group.

###  1.1 Standard Diff-in-Diff and Related Methods

Difference-in-differences identifies causal effects under an assumption that
there is a fixed level difference between the mean outcomes of the treated and
untreated groups. Formally, this parallel trends condition imposes that there
is some constant $c$ so that the following equation holds in all periods.

$E[Y_{i,t}^{(0)}|G_{i}=1]-E[Y_{i,t}^{(0)}|G_{i}=2]=c$ (1.1)

In the schools example, the condition above states that the difference in mean
potential outcomes for the two schools is constant over time. Under
Assumptions 1 and 2, the condition identifies the average treatment effect
$\tau_{t}$ and motivates a simple estimator. Let $\bar{Y}_{k,t}$ be the sample
average outcome for individuals in group $k$ at time $t$. That is, for each
$t$ and $k$:

$\bar{Y}_{k,t}=\frac{1}{n_{k}}\sum_{i=1}^{n}1\\{G_{i}=k\\}Y_{i,t}$

Under Assumptions 1, 2, and parallel trends, an unbiased estimate $\hat{c}$ of
$c$ is given below, where $\\{\alpha_{s}\\}_{s=1}^{t^{*}-1}$ are some positive
weights that sum to $1$.

$\hat{c}=\sum_{s=1}^{t^{*}-1}\alpha_{s}(\bar{Y}_{1,s}-\bar{Y}_{2,s})$

An unbiased estimator $\hat{\tau}_{t}$ of the time-$t$ average treatment
effect is as follows.

$\hat{\tau}_{t}=(\bar{Y}_{1,t}-\bar{Y}_{2,t})-\hat{c}$

The estimator above can be expressed equivalently in terms of ordinary least
squares regression and can be adapted to include covariates. A number of
inference methods have been proposed in the literature. For example, the block
bootstrap method of Bertrand et al., (2004). With two periods of data (so that
$t^{*}=2$), the estimator above reduces to the simple difference-in-
differences below:

$\hat{\tau}_{2}=(\bar{Y}_{1,2}-\bar{Y}_{2,2})-(\bar{Y}_{1,1}-\bar{Y}_{2,1})$

Diff-in-diff is one example of a general class of methods that identify causal
effects by assuming that there exists a fixed linear relationship between the
counterfactual mean outcomes in different groups. That is, there exist
parameters $W_{1}$,$W_{2}$,…,$W_{K}$ so that the following holds in all
periods:

$E[Y^{(0)}_{i,t}|G_{i}=1]=W_{1}+\sum_{k=2}^{K}W_{k}E[Y^{(0)}_{i,t}|G_{i}=k]$
(1.2)

Imposing additional conditions on the coefficients yields alternative
identification approaches. With two groups, difference-in-differences
specializes the above by fixing $W_{2}=1$, in which case (1.1) holds with
$c=W_{1}$. Another case that fits into this framework is triple differences,
which corresponds to $K=4$, $W_{2}=W_{3}=1$ and $W_{4}=-1$. This approach is
applicable when the four groups correspond to different combinations of two
binary characteristics, and only those with one of the four combinations is
treated. For example, suppose individuals are drawn from two regions $A$ and
$B$ and only individuals that satisfy eligibility criteria and live in region
$A$ are treated. Then group $1$ may consist of eligible individuals in region
$A$, group $2$ of eligible individuals in region $B$, group $3$ of ineligible
individuals in region $A$, and group $4$ of ineligible individuals in region
$B$. In this case the condition reduces to the following for some $c$.

$\big{(}E[Y_{i,t}^{(0)}|G_{i}=1]-E[Y_{i,t}^{(0)}|G_{i}=2]\big{)}-\big{(}E[Y_{i,t}^{(0)}|G_{i}=3]-E[Y_{i,t}^{(0)}|G_{i}=4]\big{)}=c$

Under Assumptions 1, 2, and (1.2), treatment effects are identified so long as
there are unique coefficients $W_{1}$, $W_{2}$, …, $W_{K}$ that satisfy (1.2)
in all pre-treatment periods, subject to any additional a priori constraints
on these parameters. The coefficients can be estimated by weighted least
squares:

$\\{\hat{W}_{k}\\}_{k=1}^{K}=\underset{\\{W_{k}\\}_{k=1}^{K}\in\mathcal{W}}{\arg\min}\sum_{t=1}^{t^{*}-1}\alpha_{t}(\bar{Y}_{1,t}-W_{1}-\sum_{k=2}^{K}W_{k}\bar{Y}_{k,t})^{2}$

Having estimated the parameters $\\{W_{k}\\}_{k=1}^{K}$, the average treatment
effect for $t\geq t^{*}$ may be estimated by plugging-in the coefficient
estimates and observed average outcomes into the linear model:

$\hat{\tau}_{t}=\bar{Y}_{1,t}-\hat{W}_{1}-\sum_{k=2}^{K}\hat{W}_{k}\bar{Y}_{k,t}$

The parameter space $\mathcal{W}$ may incorporate constraints. For example, if
$K=2$ then constraining $W_{2}=1$ yields precisely the diff-in-diff estimator
specified earlier in this section. A number of variations on the above are
available in the literature. Abadie & Gardeazabal, (2003) suggest a more
general method for estimating the parameters $\\{W_{k}\\}_{k=1}^{K}$. In place
of the mean outcomes in the objective they use vectors of group-specific
covariates which may include average outcomes. Abadie & Gardeazabal, (2003)
constrain the optimization problem so that ${W}_{1}=0$ and the remaining
coefficients are positive and sum to $1$. Doudchenko & Imbens, (2016) suggest
adding an elastic net penalty to the synthetic control objective.

A number of methods exist for selecting the weights
$\\{\alpha_{t}\\}_{t=1}^{t^{*}-1}$. For example, Abadie & Gardeazabal, (2003)
propose that the weights be chosen to minimize the objective above subject to
the constraint that they are weakly positive and sum to $1$ and Abadie et al.,
(2015) suggest choosing $\\{\alpha_{t}\\}_{t=1}^{t^{*}-1}$ by cross-
validation.

###  1.2 Consequences of the Diff-in-Diff Assumption

In the settings that we consider in this paper, the parallel trends assumption
(1.1) can be highly problematic. We consider cases in which the outcome is a
binary indicator that an individual has reached an absorbing state by a given
period. Therefore, the group mean outcome is the share of individuals in the
group who have reached the absorbing state. For reasons that we describe
below, these shares tend to converge over time, regardless of treatment. That
is, the magnitude of the difference in group-mean outcomes tends to decrease,
even if treatment has no effect. Standard diff-in-diff would erroneously
interpret such a decrease as evidence of a treatment effect, leading to biased
and inconsistent causal estimates.

Perhaps the most striking failure of parallel trends occurs when the shares in
the absorbing state grow too close to $1$. Recall that the shares must be
bounded above by $1$ and are weakly increasing over time. Consider the schools
example and suppose that at some time prior to $t^{*}$, $60\%$ of students in
school $1$ have passed and $40\%$ in school $2$, and by some time after
$t^{*}$, strictly more than $80\%$ of students in school $2$ have passed.
Under the assumption of counterfactual trends in mean outcomes, we must
immediately conclude that there is a negative treatment effect, even before
observing the post-treatment outcomes in the treated school. This is because
no more than $100\%$ of students in school $1$ can pass the test, and so the
gap in mean outcomes must be strictly lower in the post-treatment period than
the $20\%$ gap in the pre-treatment period.

The example above is the result of a ceiling parallel trends places on the
shares of individuals who can reach the absorbing state. Given that the shares
are bounded above by $1$, it follows from (1.1) that the counterfactual share
who reach the absorbing state can never exceed $1+c$ in school $1$, and $1-c$
in school 2. Similar restrictions hold under other linearity assumptions of
the form in (1.2).

Convergence of mean outcomes is likely to arise even in cases where the shares
do not reach the ceiling $1\pm c$. Consider that as the share of the
population who have reached the absorbing state increases, there are fewer
individuals left to enter the absorbing state. This means that if the share
who have reached the absorbing state is high, the increase in mean outcomes
will be small relative to the rate at which individuals who have not yet
reached the absorbing state arrive at that state.

To demonstrate, consider the schools example and suppose that in school $1$,
$80\%$ have passed the test by day $t$ and $60\%$ in school $2$. Thus the
share who have not passed by day $t$ is twice as high in school $1$ as in
school $2$. As such, for the difference in shares to remain the same up to the
next period, students in school $1$ who have not passed by day $t$ must be
twice as likely to pass on that day compared to those in school $2$. This
effect strengthens as the shares who have reached the absorbing state grow.
Suppose differences remain fixed and at some later period $t^{\prime}$, $90\%$
have passed in school $1$ and $70\%$ in school $2$. For differences to remain
fixed, the probability that a student in school $1$ who has not yet passed by
day $t^{\prime}$ passes that day must now be three times higher than for
school $2$. We formalize this point at the end of this section by showing that
the parallel assumption implies divergence of the counterfactual ‘hazard
rates’, that is, the rates at which individuals in the two groups who have not
yet reached the absorbing state reach that state.

For a graphical illustration, observe Figure 1.1(a) which shows population
mean factual and counterfactual outcomes under a duration model specified in
Appendix A. We use this same model for our simulation exercises. Factual mean
outcomes, i.e., shares of the population that have reached the absorbing
state, are plotted over time by solid lines, blue for group $1$ and red for
group $2$. The mean outcome for group 1 under a counterfactual of no
treatment, is plotted by the dashed blue line.

Figure 1.1: Deviations from Parallel Trends

(a) Mean Outcomes

(b) Time-AverageHazards

In the figure, we see that mean outcomes for group $1$ are greater than for
group $2$ in the initial period. Due to the duration nature of the setting,
the difference decreases over time under the counterfactual of no
intervention. In this example, the convergence is of a sufficient magnitude
that the average difference in the observable factual outcomes is smaller over
the post-treatment period than in the pre-treatment period. Therefore, in
expectation standard diff-in-diff will estimate a negative treatment effect.
However, the true treatment effect is positive, as seen by the the positive
gap between the solid and dashed blue lines. In fact, in this model the bias
of standard diff-in-diff is roughly four times the value of the true treatment
effect. For simulation evidence of the poor performance of standard diff-in-
diff under this model (and good performance of our proposed alternatives) see
Appendix A.

The discussion above suggests that whatever assumption we use to identify and
estimate causal effects should be compatible with the type of convergence
shown in Figure 1.1(a). In addition, we should avoid assumptions that imply
divergence between the hazard rates. As an alternative, we suggest analogues
of the diff-in-diff assumption that apply directly to the hazard rates.
Instead of assuming parallel trends in the shares who have reached the
absorbing state, we instead assume parallel trends (or some other fixed linear
relationship) in the hazard rates. Parallel trends in the hazard rates is
consistent with the convergence of counterfactual mean outcomes. Indeed, the
assumption holds in Figure 1.1(a) and thus the convergence in the figure does
not result in misleading inference under this assumption.

Finally, we provide a brief formal argument that shows the parallel trends
assumption implies divergence of counterfactual hazard rates. First we must
define these objects, for concreteness we do so in the context of the schools
example. Let $\Delta>0$ and consider the probability that, under the
counterfactual of no intervention, an individual in school $k$ passes the exam
between times $t$ and $t+\Delta$, conditional on having not passed prior to
$t$. If we scale this probability by $1/\Delta$, then the limit as the
increment $\Delta$ shrinks to zero is the counterfactual hazard rate for
school $k$. We denote the counterfactual hazard rate by $h^{(0)}_{k}(t)$ where
the superscript indicates that this is the hazard rate for the outcomes under
the no-intervention counterfactual. It is defined formally as follows:

$h^{(0)}_{k}(t)=\lim_{\Delta\downarrow
0}\frac{P(Y_{i,t+\Delta}^{(0)}=1|Y_{i,t}^{(0)}=0,G_{i}=k)}{\Delta}$

We can define the factual hazard rate $h_{k}(t)$ analogously by replacing
counterfactual outcomes with factual outcomes in the definition. In the
schools example, the counterfactual hazard rate measures the rate at which
students in school $k$ who have not passed the exam, pass the exam.

Suppose that $c$ is strictly positive and that for all $t$, we have
$h^{(0)}_{2}(t)>0$ and $E[Y_{i,t}^{(0)}|G_{i}=2]<1-c$. Then under the diff-in-
diff assumption (1.1) we have that for any $t$:

$\frac{h^{(0)}_{1}(t)}{h^{(0)}_{2}(t)}=\frac{1-E[Y_{i,t}^{(0)}|G_{i}=2]}{1-E[Y_{i,t}^{(0)}|G_{i}=2]-c}$

The right hand side grows with $t$ and it goes to infinity as the mean
counterfactual outcome for group $2$ approaches the upper bound $1-c$. So as
the share in group 2 who have reached the absorbing state approaches this
upper bound, the ratio of the hazard rates grows to infinity.

In the context of the schools example, as $t$ increases, the probability that
a student who has not passed in school $1$ passes within the next $\Delta$
increment of time, must grow infinitely large compared to the same quantity
for a student in school $2$. If $c$ is negative and
$E[Y_{i,t}^{(0)}|G_{i}=1]<1+c$, then the hazard ratio shrinks to zero as
$E[Y_{i,t}^{(0)}|G_{i}=1]$ approaches $1+c$.

A related point is made by Wu & Wen, (2022) who show formally that the
parameter estimated by diff-in-diff must evolve over time when data are
generated by a hazard model (apart from in certain degenerate cases).

The analysis above is concerning because it suggests that the hazard rates
exhibit aberrant behavior as the proportion of individuals who have entered
into an absorbing state grows large. The hazard rate is a primitive building
block of duration models, and it has a clear structural interpretation. If the
difference-in-differences assumption implies counter-intuitive and surprising
behavior of the hazard rates, then we should reject the assumption a priori.

##  2 Model and Identification

In light of the discussion above, we replace the standard parallel trends
assumption, or a more general restriction of a fixed linear relationship
between mean outcomes, with an analogous condition that applies directly to
the hazard rates. By restricting hazards rather than mean outcomes, we ensure
our modeling restrictions are consistent with the convergence of mean outcomes
between groups. As such, the convergence of mean outcomes need not bias causal
estimates based on our assumptions, in contrast to estimates from standard
diff-in-diff.

Throughout, we continue to take $k=1$ to be the unique treated group. Our ky
identifying assumption is that there exists a fixed linear relationship
between the counterfactual hazard rates of the treated and untreated groups.
Formally, we consider assumptions of the following form:

$h^{(0)}_{1}(t)=W_{1}+\sum_{k=2}^{K}W_{k}h^{(0)}_{2}(t)$ (2.1)

Imposing a priori constraints on the coefficients $W_{1},..,W_{K}$ yields a
range of alternative modeling assumptions. For example, in the two-group case,
setting $W_{2}=1$ we get a duration analogue of standard difference-in-
differences which is our preferred specification. We refer to identification
and estimation based on this condition as ‘hazard diff-in-diff’.

$h^{(0)}_{1}(t)-h^{(0)}_{2}(t)=c$ (2.2)

The condition (2.2) states that the level difference in hazard functions
between groups $1$ and $2$ is constant over time. The condition allows for
common shocks that impact the counterfactual hazards of individuals in both
the treated and untreated groups, so long as these shocks induce parallel
movements in the hazard rates. Moreover, the condition allows for the
possibility that the hazard rates evolve over time, increasing or decreasing
with the time spent in the $Y_{i,t}=0$ state.

If we instead assume $W_{1}=0$ and leave $W_{2}$ unrestricted then we recover
the proportional hazard restriction that characterizes models in Hunt, (1995)
and Wu & Wen, (2022):

$h^{(0)}_{1}(t)/h^{(0)}_{2}(t)=c$ (2.3)

The above restriction admits shocks to the counterfactual hazard rates and
allows for the possibility that the hazards evolve over time. In this case the
restriction is that the shocks and time trends leave the difference in the log
counterfactual hazard rates unchanged.

The general linear restriction also nests a hazard analogue of the triple
differences specification in Section 1.1.

$[h^{(0)}_{1}(t)-h^{(0)}_{2}(t)]-[h^{(0)}_{3}(t)-h^{(0)}_{4}(t)]=c$

We show that linear restrictions on the hazard rates allow for simple and
transparent identification and estimation methods that are close analogues of
the corresponding diff-in-diff and related methods.

###  2.1 Hazard Diff-in-Diff

We provide results that apply for general linear restrictions of the form in
(2.1). However, our primary interest is in the hazard diff-in-diff restriction
(2.2) and so we begin with this case. We suppose there are two groups $k=1,2$
and assume the level differences in hazard rates is fixed. The condition
(2.2), combined with Assumptions 1 and 2, identify counterfactual mean
outcomes and average treatment effects. What follows is a sketch of the
identification argument.

The first step is to rewrite the condition (2.2) in terms of the time-average
counterfactual hazard functions. Time-average hazards can be written in terms
of mean outcomes and are directly identified from the data. We denote the
time-average counterfactual hazard function for group $k$ at time $t$ by
$\bar{H}^{(0)}_{k,t}$, and the time-average factual hazard by $\bar{H}_{k,t}$.
The time-average hazard is, as the name suggests, the average over time of the
hazard rate. Formally, these objects are defined as follows:

$\bar{H}^{(0)}_{k,t}=\frac{1}{t-1}\int_{1}^{t}h^{(0)}_{k}(s)ds,\,\,\,\,\bar{H}_{k,t}=\frac{1}{t-1}\int_{1}^{t}h_{k}(s)ds$

From the condition (2.2) we obtain the equality below:

$\bar{H}^{(0)}_{1,t}-\bar{H}^{(0)}_{2,t}=c$ (2.4)

Key to our analysis is the observation that the time-average of the
counterfactual hazard rate can be written in terms of mean outcomes. This
follows from a standard result in duration analysis that the ‘cumulative
hazard function’ is equal to minus the log of the ‘survivor function’. For
$t>1$ we have:

$\displaystyle\bar{H}^{(0)}_{k,t}$
$\displaystyle=\frac{1}{t-1}ln\bigg{(}\frac{1-E[Y_{i,1}^{(0)}|G_{i}=k]}{1-E[Y_{i,t}^{(0)}|G_{i}=k]}\bigg{)}$
(2.5) $\displaystyle\bar{H}_{k,t}$
$\displaystyle=\frac{1}{t-1}ln\bigg{(}\frac{1-E[Y_{i,1}|G_{i}=k]}{1-E[Y_{i,t}|G_{i}=k]}\bigg{)}$
(2.6)

Note that the time-average factual hazard rate depends only on factual mean
outcomes, and therefore it can be directly and straight-forwardly estimated
from the observed outcomes. Moreover, under Assumptions 1 and 2, it is equal
to the time-average counterfactual hazard when $k\neq 1$, or when $k=1$ and
$t<t^{*}$.

In order to identify average treatment effects, we perform difference-in-
differences on the time-average hazards. Thus we obtain the time-average
counterfactual hazards for the treated group in the post-treatment period. We
can then recover the counterfactual mean outcomes in the post-treatment period
by inverting (2.5), and thus we identify average treatment effects.

This approach is illustrated graphically in Figure 1.1. In Figure 1.1(a) we
plot group-specific mean factual and counterfactual mean outcomes over time
from an underlying duration model that satisfies parallel trends in the hazard
rates (2.2). As we discuss in Section 1.2, the solid blue curve represents the
factual group $1$ mean outcome, the solid red line is the group $2$ mean
outcome, and the dashed blue line, the counterfactual group $1$ mean outcome.
Figure 1.1(b) shows the corresponding time-average hazards in the same colors
and styles.

The curves in 1.1(b) are related to those in 1.1(a) by the formulas (2.5) and
(2.6). Note that while parallel trends clearly fails in 1.1(a), the
counterfactual time-average hazards are parallel. By transforming the solid
curves in 1.1(a) we could obtain the factual time-average hazard in 1.1(b). By
extending the parallel trends in time-average hazards forward from the
treatment date, we could then impute counterfactual time-average hazards for
group $1$ in the post-treatment period, much as in standard diff-in-diff.
Then, having imputed post-treatment counterfactual hazards, we can invert the
transformation in order to recover the counterfactual mean outcomes for group
$1$ in Figure 1.1(a).

The more precise identification result is given in Proposition 1 below. This
result is a corollary of the more general Theorem 1 in the next subsection.

######  Proposition 1.

Suppose Assumptions 1 and 2 and (2.2) hold and define $\bar{H}_{k,t}$ as in
(2.6). Then for every $1<t<t^{*}$:

$c=\bar{H}_{1,t}-\bar{H}_{2,t}$ (2.7)

And for any $t^{*}\leq t$ the counterfactual mean outcome is given by:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1-(1-E[Y_{i,1}|G_{i}=1])exp\big{(}-(t-1)(\bar{H}_{2,t}+c)\big{)}$
(2.8)

The average treatment effect is then identified by:

$\tau_{t}=E[Y_{i,t}|G_{i}=1]-E[Y^{(0)}_{i,t}|G_{i}=1]$

The characterization in Proposition 1 motivates a simple plug-in estimator.
One can obtain estimates of the time-average hazards $\bar{H}_{k,t}$ by
replacing the group-specific mean outcomes in (2.6) with sample averages, and
thus estimate both $c$, the group-1 mean counterfactual outcome
$E[Y_{i,t}^{(0)}|G_{i}=1]$, and average treatment effects. We discuss
estimation and inference in Section 3.

The equation (2.7) shows that pre-treatment time-average hazard rates exhibit
parallel trends. Pre-treatment time-average hazards are estimable and so we
can visually inspect whether they appear to exhibit pre-treatment parallel
trends or carry out a formal test This is akin to the parallel trends test in
standard diff-in-diff.

###  2.2 General Linear Restrictions

We now turn to more general restrictions. We can identify counterfactual mean
outcomes and treatment effects under an assumption of the form in (2.1).
Identification follows from similar steps to those in Section 2.1. The general
linear restriction implies the following condition on the time-average
counterfactual hazard rates.

$\bar{H}^{(0)}_{1,t}=W_{1}+\sum_{k=2}^{K}W_{k}\bar{H}^{(0)}_{2,t}$ (2.9)

The quantities in the equation above are all directly identified in the pre-
treatment period. Thus we obtain $t^{*}-1$ equations from which we may
identify the parameters $\\{W_{k}\\}_{k=1}^{K}$. If there is a unique solution
then the parameters are identified. We can then identify counterfactual time-
average hazards for the treated group in the post-treatment period. Inverting
the equation (2.5) we recover counterfactual mean outcomes and thus identify
average treatment effects.

######  Theorem 1.

Suppose Assumptions 1 and 2 and (2.1) hold and define $\bar{H}_{k,t}$ as in
(2.6). Then for every $1<t<t^{*}$:

$\bar{H}_{1,t}=W_{1}+\sum_{k=2}^{K}W_{k}\bar{H}_{k,t}$ (2.10)

And for any $t^{*}\leq t$ the counterfactual mean outcome is given by:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1-\big{(}1-E[Y_{i,1}|G_{i}=1]\big{)}exp\big{(}-(t-1)(W_{1}+\sum_{k=2}^{K}W_{k}\bar{H}_{k,t})\big{)}$
(2.11)

Thus if (2.10) has a unique solution, then both $E[Y^{(0)}_{i,t}|G_{i}=1]$ and
$\tau_{t}$ are identified for all $t$.

Theorem 1 identifies treatment effects when the equations (2.10) have a unique
solution subject to any additional a priori constraints on the coefficients.
Note that we must have at least three periods of data. Under the fixed level
difference restriction in Section 2.1, uniqueness always holds. For the
proportional hazards constraint it suffices that the following holds for some
$t<t^{*}$:

$E[Y_{i,t}|G_{i}=2]\neq E[Y_{i,1}|G_{i}=2]$

If we do not constrain the coefficients $\\{W_{k}\\}_{k=1}^{K}$, then a
necessary condition for uniqueness is that $t^{*}>K$ and uniqueness is generic
whenever this holds.

Given a sufficient number of pre-treatment periods, the parameters in (2.10)
are over-identified. This suggests we can test the identifying restrictions
using say placebo tests or, in the special case in Subsection 2.1, a test for
parallel trends.

###  2.3 Incorporating Covariates

In difference-in-differences analysis it is common to adjust for covariates.
One motivation is that parallel trends may hold within each stratum of the
covariates but not in the aggregate (see e.g., Abadie, (2005)). For example,
suppose each individual belongs to one of two demographic strata A and B.
Outcomes are decreasing over time in stratum A but increasing in stratum B and
individuals in stratum A are more prevalent in the treated group that in the
untreated group. Then average outcomes in the treated group will tend to
decrease over time compared to the untreated group, even if trends are
parallel within each stratum.

The analysis in the previous subsection can be extended to cases in which
condition (2.9) holds only conditional covariates. One may simply apply the
analysis separately within each covariate stratum. This would yield
identification of conditional average treatment effects which could be
aggregated to obtain average treatment effects. However, to apply that
analysis to data would require estimation of conditional mean outcomes for
each group and period.

Fortunately, in the special case described below, the problem can be straight-
forwardly resolved by a form of propensity score weighting. Note that this
weighting approach only applies to the hazard diff-in-diff strategy and not to
the proportional hazard specification nor to general linear restrictions. The
simplicity of incorporating covariates in hazard diff-in-diff is a major
advantage over other specifications.

We suppose that there are two groups $k=1,2$ and for each individual $i$ we
observe individual-specific and time-invariant covariates $X_{i}$. We can
define group-specific counterfactual hazard rates within each stratum of the
covariates as follows. Let $h_{k}^{(0)}(t;x)$ denote the group $k$
counterfactual hazard rate at time $t$ for the sub-population for whom $X_{i}$
is equal to $x$.

$h_{k}^{(0)}(t;x)=\lim_{\Delta\downarrow
0}\frac{P(Y_{i,t+\Delta}^{(0)}=1|Y_{i,t}^{(0)}=0,G_{i}=k,X_{i}=x)}{\Delta}$

Suppose the hazard diff-in-diff assumption holds within each stratum of the
covariates and moreover, that the level difference does not depend on the
stratum. That is, the following equation holds for each $x$ in the support of
the covariates:

$h_{1}^{(0)}(t;x)-h_{2}^{(0)}(t;x)=c$ (2.12)

If there is imbalance in the distribution of the covariates between the
groups, then the condition above does not guarantee parallel trends for the
marginal hazards (2.2). However, by applying a weighting scheme we can recover
covariate balance and identify treatment effects.

To achieve this, we define a weight function $\omega$ on the support of the
covariates. In the case of continuous covariates one can replace the
conditional probabilities with conditional probability densities and obtain a
weighting of the kind introduced in DiNardo et al., (1996).

$\omega(x)=\frac{P(X_{i}=x|Y_{i,1}=0,G_{i}=1)}{P(X_{i}=x|Y_{i,1}=0,G_{i}=2)}$
(2.13)

By weighting individuals in the untreated group by $\omega(X_{i})$ we down-
weight those with values of the covariates that are more prevalent among
survivors in group $2$ than group $1$ in the initial period, and up-weight
those whose values were less prevalent. If the covariates have the same
distribution across groups in the initial period, then the weight function
reduces to $\omega(x)=1$.

The weighting function can be written equivalently in terms of a type of
propensity score (Rosenbaum & Rubin, (1983)). Let $p(x)$ be the probability
that an individual is in the treated group given they have covariate values
$x$ and they are not in the absorbing state in the initial period. Formally,
$p(x)$ is defined as follows:

$p(x)=P(G_{i}=1|Y_{i,t}=0,X_{i}=x)$

Then applying Bayes’ rule we obtain the following:

$\omega(x)=\frac{p(x)P(G_{i}=2|Y_{i,t}=0)}{\big{(}1-p(x)\big{)}P(G_{i}=1|Y_{i,t}=0)}$
(2.14)

With the weighting function $\omega$ in hand we can define the weighted time-
average hazard $\tilde{H}_{2,t}$ for the untreated group.

$\tilde{H}_{2,t}=\frac{1}{t-1}ln\bigg{(}\frac{1-E[Y_{i,1}|G_{i}=2]}{E[\omega(X_{i})(1-Y_{i,t})|G_{i}=2]}\bigg{)}$
(2.15)

Theorem 2 shows that an analogous result to Proposition 1 holds under the
covariate-specific parallel trends assumption (2.12). The only difference is
the use of the weighted time-average hazard for the untreated group in place
of the unweighted time-average hazard.

######  Theorem 2.

Suppose Assumptions 1 and 2 and (2.12) hold. Define $\bar{H}_{k,t}$ as in
(2.6) and $\tilde{H}_{2,t}$ as in (2.15). Then for every $1<t<t^{*}$:

$c=\bar{H}_{1,t}-\tilde{H}_{2,t}$ (2.16)

And for any $t^{*}\leq t$ the counterfactual mean outcome is given by:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1-\big{(}1-E[Y_{i,1}|G_{i}=1]\big{)}exp\big{(}-(t-1)(c+\tilde{H}_{2,t})\big{)}$
(2.17)

##  3 Estimation and Inference

The identification results in the previous section motivate plug-in estimates
of counterfactual mean outcomes and treatment effects. We first define an
estimate $\hat{H}_{k,t}$ of the time-average hazard $\bar{H}_{k,t}$ as
follows:

$\hat{H}_{k,t}=\frac{1}{t-1}ln\bigg{(}\frac{1-\bar{Y}_{k,1}}{1-\bar{Y}_{k,t}}\bigg{)}$
(3.1)

With the time-average hazard estimates in hand, the first result in Theorem 1
motivates regression estimates of the parameters $\\{W_{k}\\}_{k=1}^{K}$.
Using data from the pre-treatment periods we regress the estimate
$\hat{H}_{1,t}$ on the EstimatedTime-AverageHazards of the other groups. A
weighted, and possibly constrained, least-squares estimator is given below
where the weights are $\alpha_{t}$ for $t=2,..,t^{*}-1$ sum to unity.

$\\{\hat{W}_{k}\\}_{k=1}^{K}=\underset{\\{W_{k}\\}_{k=1}^{K}\in\mathcal{W}}{\arg\min}\sum_{t=1}^{t^{*}-1}\alpha_{t}(\hat{H}_{1,t}-W_{1}-\sum_{k=2}^{K}W_{k}\hat{H}_{k,t})^{2}$
(3.2)

The constraint set $\mathcal{W}$ can incorporate restrictions like positivity
of the weights, or that the intercept $W_{1}$ is equal to zero. One can amend
the weighted least squares objective to include a penalty (see Doudchenko &
Imbens, (2016) for discussion in the non-duration context).

Having obtained parameter estimates, the second result in Theorem 1 motivates
the following estimate of the time-$t$ average treatment effect:

$\hat{\tau}_{t}=\bar{Y}_{1,t}-1+\big{(}1-\bar{Y}_{1,1}\big{)}exp\big{(}-(t-1)(\hat{W}_{1}+\sum_{k=2}^{K}\hat{W}_{k}\hat{H}_{k,t})\big{)}$

In our practical application we use equal weights (i.e.,
$\alpha_{2},\alpha_{3},...$ all take the same value). More generally they may
be chosen either to a) place greater emphasis on those periods that are closer
to the intervention, or b) minimize the asymptotic variance of the estimates.

In the hazard diff-in-diff case examined in Section 2.1, the estimator reduces
to the formula below, where $\hat{c}$ is an estimate of $c$. This corresponds
to the imputation approach in Wooldridge, (2023).

$\displaystyle\hat{c}$
$\displaystyle=\sum_{t=2}^{t^{*}-1}\alpha_{t}(\hat{H}_{1,t}-\hat{H}_{2,t})$
(3.3) $\displaystyle\hat{\tau}_{t}$
$\displaystyle=\bar{Y}_{1,t}-1+\big{(}1-\bar{Y}_{1,1}\big{)}exp\big{(}-(t-1)(\hat{c}+\hat{H}_{2,t})\big{)}$
(3.4)

In the proportional hazard model, we constrain $W_{1}=0$ and obtain the
estimate of $W_{2}$, which we again denote by $\hat{c}$, and a corresponding
treatment effect estimate. Both are given below.

$\displaystyle\hat{c}$
$\displaystyle=\frac{\sum_{t=2}^{t^{*}-1}\alpha_{t}\hat{H}_{1,t}\hat{H}_{2,t}}{\sum_{t=2}^{t^{*}-1}\alpha_{t}\hat{H}_{1,t}^{2}}$
$\displaystyle\hat{\tau}_{t}$
$\displaystyle=\bar{Y}_{1,t}-1+\big{(}1-\bar{Y}_{1,1}\big{)}exp\big{(}-(t-1)\hat{c}\hat{H}_{2,t}\big{)}$

###  3.1 Estimation with Covariate Adjustment

In order to estimate treatment effects using the weighting scheme introduced
in Section 2.3, one must first estimate the weighting function $\omega$. We
suggest two alternatives.

The first estimator is based on (2.13) and is appropriate for discrete
covariates. In this case we simply replace the conditional probabilities in
the formula (2.13) with empirical frequencies. The estimate $\hat{\omega}(x)$
is defined for all $x$ for which there exists some individual $i$ in group $2$
for whom $X_{i}=x$ and $Y_{i,1}=0$, and is given below:

$\hat{\omega}(x)=\frac{n_{2}(1-\bar{Y}_{2,1})\sum_{i=1}^{n}1\\{G_{i}=1\\}1\\{X_{i}=x\\}(1-Y_{i,1})}{n_{1}(1-\bar{Y}_{1,1})\sum_{i=1}^{n}1\\{G_{i}=2\\}1\\{X_{i}=x\\}(1-Y_{i,1})}$
(3.5)

If some covariates are continuous or discrete with many support points, then
we suggest an approach based on the propensity formulation (2.14). Let
$\hat{p}(x)$ be an estimate of $P(G_{i}=1|Y_{i,t}=0,X_{i}=x)$. One could
obtain such an estimate using say, logistic regression of $1\\{G_{i}=1\\}$ on
$X_{i}$ using the sub-sample of individuals for whom $Y_{i,1}=0$. We can then
estimate the weights as follows:

$\hat{\omega}(x)=\frac{\hat{p}(x)(1-\bar{Y}_{2,1})n_{2}}{\big{(}1-\hat{p}(x)\big{)}(1-\bar{Y}_{1,1})n_{1}}$

Having obtained an estimate of the weight function, we use the following
estimate of the weighted time-average hazard function in (3.3) and (3.4).

$\hat{H}_{2,t}=\frac{1}{t-1}ln\bigg{(}\frac{1-\bar{Y}_{2,1}}{\frac{1}{n_{2}}\sum_{i=1}^{n}1\\{G_{i}=2\\}\hat{\omega}(X_{i})(1-{Y}_{i,t})}\bigg{)}$

###  3.2 Bootstrap Inference

Bertrand et al., (2004) propose the block bootstrap (Efron & Tibshirani,
(1994)) for conducting inference in vanilla diff-in-diff. The asymptotic
validity of the procedure rests on an assumption that the outcome histories of
different individuals are independent. However, the outcomes of a given
individual may exhibit arbitrary dependence over time. We suggest the use of
the block bootstrap for inference in the duration settings in this paper.
Implementation follows the same steps as for standard diff-in-diff with the
distinction that the bootstrap samples are used to construct our estimator of
the treatment effect rather than the usual diff-in-diff estimator.

To carry out block bootstrap inference, one independently resamples
individuals uniformly with replacement and forms a new sample using the
complete series of outcomes and covariates for each individual that is
resampled. For example, if individual $i$ is sampled in the $b$-the bootstrap
iteration, then that bootstrap sample will contain an individual whose outcome
history is $Y_{i,1},Y_{2,i},...,Y_{i,t}$.

Having obtained block bootstrap samples, one may then evaluate bootstrap
standard errors as well as pointwise and uniform confidence bands in the usual
way. In particular, for each bootstrap sample $b=1,...,B$, one computes the
estimate $\hat{\tau}_{t}$ using the bootstrap sample in place of the original
data, and thus obtains a bootstrap estimate $\hat{\tau}^{*}_{b,t}$.

The standard deviation $\hat{\sigma}_{t}$ of $\hat{\tau}^{*}_{b,t}$ over the
bootstrap samples $b=1,...,B$ is taken as the standard error for
$\hat{\tau}_{t}$. To form pointwise confidence intervals for ${\tau}_{t}$, let
$\hat{q}_{1-\alpha,t}$ be the $1-\alpha$-quantile of
$|\hat{\tau}^{*}_{b,t}-\hat{\tau}_{t}|/\hat{\sigma}_{t}$. Then a
$1-\alpha$-level confidence interval has the form below:

$CI_{1-\alpha,t}=[\hat{\tau}_{t}-\hat{q}_{1-\alpha}\hat{\sigma}_{t},\hat{\tau}_{t}+\hat{q}_{1-\alpha}\hat{\sigma}_{t}]$

The intervals described above are only designed to achieve correct pointwise
coverage. Suppose we form confidence intervals for $\tau_{t}$ for each of the
periods $t=t^{*},t^{*}+1,...,T$. Each of these intervals is specified so that
it covers the corresponding period’s average treatment effect with probability
approximately $1-\alpha$. However, the probability that every one of these
intervals contains its corresponding period’s treatment effect may be much
lower.

In order to obtain a desired joint coverage probability, in place of the
critical value $\hat{q}_{1-\alpha,t}$ defined above, we instead take
$\hat{q}_{1-\alpha,t}$ to be the $1-\alpha$ quantile over $b=1,...,B$ of
$\max_{t^{*}\leq s\leq
T}|\hat{\tau}^{*}_{b,s}-\hat{\tau}_{s}|/\hat{\sigma}_{s}$ and otherwise form
the confidence bands as above.

A more formal description of the pointwise and uniform inference procedures is
given in Algorithm $1$ in the appendix.

###  3.3 Specification Testing

The condition (2.2) has testable implications. If the assumption holds in all
periods then the difference in pre-treatment time-average hazards must be
constant. This motivates a test analogous to the test for parallel trends in
standard difference in differences.

In both hazard and standard diff-in-diff, we recommend that researchers
proceed with caution when interpreting a failure to reject pre-treatment
parallel trends. Even if parallel trends hold over the pre-treatment period
this is no guarantee that they would have remained parallel into the post-
treatment period in the absence of treatment.

To motivate the test, note that from (2.4) and Assumptions 1 and 2, in all
periods $t=2,3,...,t^{*}-1$ we have:

$\delta_{t}=(\bar{H}_{1,t}-\bar{H}_{2,t})-(\bar{H}_{1,t^{*}-1}-\bar{H}_{2,t^{*}-1})=0$

In order to test whether the hazard rates are parallel in the pre-treatment
period, we construct uniform (over $t=2,..,t^{*}-1$) confidence bands for
$\delta_{t}$. In order to estimate $\delta_{t}$ we replace each population
time-average hazard $\bar{H}_{k,t}$ with the corresponding estimate
$\hat{H}_{k,t}$ specified in Section 2.1. We thus obtain an estimate
$\hat{\delta}_{t}$:

$\hat{\delta}_{t}=(\hat{H}_{1,t}-\hat{H}_{2,t})-(\hat{H}_{1,t^{*}-1}-\hat{H}_{2,t^{*}-1})$

We then construct uniform confidence bands for $\delta_{t}$ using the block-
bootstrap analogous to the construction in the previous subsection. The test
rejects if the uniform bands do not contain zero for all $t=2,...,t^{*}-1$.
Note that if covariate adjustment is used then the weights given in Section
3.1 must also be evaluated for each bootstrap sample. The procedure is
detailed in Algorithm 2 in the appendix.

An advantage of this method is that one can plot the estimates
$\hat{\delta}_{t}$ and the corresponding confidence bands. Thus the researcher
can observe the precision of the estimate $\hat{\delta}_{t}$ and can compare
this to the magnitudes of the time-average hazard estimates themselves. Thus a
researcher can make an informal assessment as to whether a failure to reject
parallel trends is a consequence of imprecise pre-treatment time-average
hazard estimates.

###  3.4 Asymptotic Validity

All of the procedures we have described can be written as generalized method
of moments estimators or sequential generalized method of moments estimators.
Thus, as the sample size grows (with $K$ and $T$ fixed) standard regularity
conditions ensure the consistency of our estimates and asymptotically correct
coverage of the bootstrap confidence intervals. These results are well-known
and so, following the example of Wooldridge, (2023), we omit a formal
statement here.

Nonetheless, it is important to note three caveats. First, standard
inferential results require identification of the nuisance parameters, which
means that there must be unique coefficients $\\{W_{k}\\}_{k=1}^{K}$ that
satisfy (2.10) subject to any priori constraint that
$\\{W_{k}\\}_{k=1}^{K}\in\mathcal{W}$. Second, if this constraint is an
inequality constraint and it binds, then treatment effect estimates may not be
differentiable functions of mean outcomes. In this case, asymptotic normality
generally fails and the bootstrap does not have correct coverage. Such
settings may call for alternative inference procedures of the form described
in Fang, (2019). Finally, for the estimation with covariate adjustment,
regular estimation generally requires that the weights $\omega(X_{i})$ be
bounded above, in which case the propensity scores must be bounded below away
from zero (see Khan & Tamer, (2010)).

##  4 Application: The Impact of Unemployment Insurance

We apply our methods to examine the impact of a policy change in Austria on
the 1st of August 1989 that increased the generosity of unemployment benefits
of eligible individuals. This setting was previously examined by Lalive et
al., (2006) and we use the data accompanying their paper. Lalive et al.,
(2006) use the data to estimate a piece-wise constant proportional hazards
model with a linear index that interacts eligibility for various aspects of
the policy with an indicator that the policy change has occurred. We instead
employ a cross-cohort study using our methods.

In our view, the primary benefit of our analysis over the original study is
its simplicity and transparency. Our approach allows us to avoid specifying a
particular parametric form for the hazard rates and numerical maximization of
the corresponding likelihood. It allows us to visually assess the presence of
deviations over the pre-treatment period from our foundational assumption of
parallel trends in the hazard rates, and to test the assumption formally. In
addition, we control for the calendar date at which unemployment spells begin
using the our weighting approach. This ensures that our estimates are robust
to differential trends between sub-populations who became unemployed on
different dates.

Following the policy change, individuals aged 40-49 who had has been employed
for at least 312 weeks out of the previous ten years became eligible for 39
weeks of benefits rather than the previous 30 weeks. Some individuals also
qualify for a (modest) increase in the replacement rate, which is the
proportion of expected earnings given to individuals receiving benefits. To
simplify our analysis we consider only the increase in the potential benefit
duration (PBD) rather than the change in the level of benefits. As such, we
exclude all individuals who qualify for the change in replacement rate from
our sample.

To construct our treated group, we collect all individuals in the data who
qualify for the extension of PBD from $30$ to $39$ weeks, excluding those who
qualify for the increased replacement rate. Of these individuals we retain
only those who became unemployed at or prior to the reform date, and less than
$30$ weeks after the reform date. The untreated group contains those
individuals who became unemployed at or prior to one year before the reform
date, and less than $335$ weeks before the reform date. The treated group
consists of $4,058$ individuals and the untreated group $4,207$.

For each individual, the time period $t$ is taken to be the number of days
since the beginning of their unemployment spell. Thus for an individual $i$,
the period-$t$ outcome $Y_{i,t}$ is an indicator of whether that individual
had exited unemployment at or prior to $t$ days after becoming unemployed.

We consider the treatment date to be the $30$ week mark. This is the point at
which benefits end for those in the untreated group. Benefits for treated
individuals last an additional $9$ weeks. Note that this may be problematic
for the no-anticipation assumption. Individuals in the treated group were
likely aware that their benefits would not end at $30$ weeks. Nonetheless, we
note that any reduction in the pressure to search for employment prior to this
date among the treated group would likely reduce the magnitude of our
estimated treatment effects.

Given the importance of seasonal variation on job search, there may be
differential trends in the rates of job-finding between individuals who became
unemployed on different calendar dates. As we discuss in Section 2.3, such
differential trends can be problematic if the distribution of the start dates
of unemployment spells differs between the two cohorts. For this reason we
apply the weighting scheme specified in (3.5) to re-balance these
distributions between the groups. This requires us to drop from the sample
individuals who became unemployed on a date on which no untreated individual
was made unemployed (there are $17$ such dates out of $240$).

Figure 4.1: Full Panel

(a) Average Outcomes

(b) EstimatedTime-AverageHazards

Figure 4.1(a) plots the weighted mean outcomes for the two groups. Recall that
the mean outcome is the proportion of individuals who have left unemployment
by a given day into their spell. The red curve is the mean outcome for the
untreated cohort and blue for the treated cohort. The series for the two
cohorts are relatively close, with some apparent divergence immediately
following day 210, which is marked with a vertical dashed line and is the
point at which benefits expire for individuals in the untreated cohort. Over
the period following the benefit extension the two curve eventually begin to
converge. The rightmost vertical solid line marks day 273, at which time
benefits expire for treated individuals.

Figure 4.1(b) contains the weighted time-average hazards for the two groups
with the same color coding as in Figure 4.1(a). Note that these are
logarithmic transformations of the values in Figure 4.1(a). We see that in the
initial weeks following unemployment the time-average hazard rates for both
groups increases steadily before stabilizing and declining. It then remains
relatively steady for both groups following $30$ weeks with a modest decline
for the untreated group.

There is very marked jump in the time-average hazard rate for untreated
individuals following the end of their benefit period. This may suggest a
sudden increase in job search intensity after unemployment benefits run out,
or it may reflect a deliberate delay in the start date of new employment until
exactly the date of benefit expiration. Notably, there also appears to be a
slight increase for the treated group at this same period despite the benefits
of these individuals persisting for an additional $9$ weeks. This may be
explained by imperfect knowledge of the reform.

Figure 4.2: Imputations

(a) Imputed Time-Average Hazards

(b) Imputed Average Outcomes

Following standard practice we apply our diff-in-diff approach using only
periods within a relatively narrow window around the treatment date. We
estimate the level difference between covariate weighted time-average hazards
using the observations no more than eight weeks prior to the treatment date
and we extrapolate forward no more than $125$ days after treatment. The point
eight weeks prior to the treatment date is marked by the leftmost solid black
vertical line in Figures 4.1(a) and 4.1(b).

Figure 4.2(a) shows the weighted time-average hazards over this period. The
dashed line indicates the imputed values for the treated cohort under the no-
treatment counterfactual. Note that within this window, pre-treatment parallel
trends appear plausible.

Figure 4.2(b) plots the mean outcomes over this same window. Again, the dashed
line plots the imputed mean outcomes for the treated group. The gray region
gives the $95\%$ pointwise confidence bands. These were calculated using the
bootstrap method described in Section 3.2. These are confidence bands for the
average treatment effect added to the factual average outcomes for the
untreated group.

Figure 4.3: Treatment Effects and Tests

(a) Treatment Effects

(b) Parallel Trends Test

In Figure 4.3(a) we plot the period-specific treatment effects. The treatment
effect is strongly negative immediately following treatment but tends to
decrease in magnitude over time. Notably, most of the steady reduction in
magnitude follows the expiry of benefits for untreated individuals, which
occurs at the time marked by the solid vertical line. The grays region are
$95\%$ pointwise and uniform confidence bands. A close inspection reveals that
the uniform bands do not contain zero at all periods, rather the upper band
lies just below zero for a brief period shortly after treatment. That is, we
find a statistically significant negative treatment effect.

Figure 4.3(b) visualizes our test for pre-treatment parallel trends. The green
curve plots the difference in time-average hazard estimates relative to the
value just prior to treatment. The vertical line indicates the treatment date.
We see that this curve is strongly negative following treatment (in line with
our negative treatment effect estimates), but is weakly positive prior to
treatment. The $50\%$ uniform confidence bands contain zero over the entire
pre-treatment period. This indicates a failure to reject pre-treatment
parallel trends in the time-average hazards even at the highly conservative
$50\%$ level.

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##  Appendix A Simulation Study

In order to assess the finite-sample performance of our procedure and to
demonstrate the potential for large biases in standard diff-in-diff in
duration settings, we implement a Monte Carlo simulation. We simulate
observations from a data-generating process that obeys our identifying
assumptions. The untreated counterfactual hazards for groups $1$ and $2$ are
as follows:

$\displaystyle h^{(0)}_{1}(t)$
$\displaystyle=\big{(}1+\sqrt{t/T}-\frac{1}{2}(t/T-1/2)^{2}+c\big{)}/(T-1)$
$\displaystyle h^{(0)}_{2}(t)$
$\displaystyle=\big{(}1+\sqrt{t/T}-\frac{1}{2}(t/T-1/2)^{2}\big{)}/(T-1)$

The hazard rate for the observed outcomes of individuals in group $1$ (i.e.,
outcomes in the factual world in which an intervention occurs at time $t^{*}$)
is given below:

$\displaystyle h_{1}(t)$
$\displaystyle=\big{(}1+\sqrt{t/T}-\frac{1}{2}(t/T-1/2)^{2}+c+\beta 1\\{t\geq
t^{*}\\}\big{)}/(T-1)$

The probability that an individual who has yet to pass the exam passes between
the discrete intervals $t-1$ and $t$ can be found by integrating and
transforming the hazard rate as below:

$P(Y_{t+1,i}=1|Y_{i,t}=0,G_{i}=k)=1-exp\big{(}-\int_{t}^{t+1}h_{k}(s)ds\big{)}$

And similarly for counterfactual outcomes. Thus we can draw factual and
counterfactual outcomes using the switching probabilities above. In practice
we evaluate the integral on the right-hand side numerically.

Table 1: Simulation Parameters $n$ | $T$ | $t^{*}$ | $E[Y_{i,1}|G_{i}=1]$ | $E[Y_{i,1}|G_{i}=2]$ | $c$ | $\beta$
---|---|---|---|---|---|---
$100,\,500,\,1000,\,5000,\,10,000$ | $20$ | $11$ | $0.4$ | $0.2$ | $0.5$ | $1$

The parameter values in our simulations are given in Table 1. With these
parameters the population shares of individuals in groups $k=1,2$ with an
outcome of $1$ under both the factual intervention and the no-intervention
counterfactual are displayed in Figure A.1(a) which is identical to Figure 1.1
in the main body of the paper. The counterfactual and factual time-average
hazards are illustrated in Figure A.1(b).

Figure A.1: Data Generating Process

(a) Mean Outcomes

(b) Time-Average Hazards

Figure A.1(a) demonstrates that the treatment effect is positive and that the
counterfactual shares for the two groups converge over time. Given our
particular choice of simulation parameters, this convergence occurs primarily
in the post-treatment period with trends in the pre-treatment period almost
parallel. This suggests that a test for pre-treatment parallel trends in mean
outcomes is unlikely to reject despite a failure of parallel trends in the
post-treatment period.

Figure A.1(b) shows that the counterfactual time-average hazards are parallel,
which contrasts with the counterfactual mean outcomes which converge.

We apply the estimation and inference procedures in Section 2. We set the
weights all equal, i.e., $\alpha_{t}=\frac{1}{t^{*}-2}$ for
$t=2,3,...,t^{*}-1$, and $\gamma_{t}=\frac{1}{t^{*}-1}$ for
$t=1,2,...,t^{*}-1$. For the block bootstrap we use $10,000$ bootstrap
replications.

Figure A.2 contains estimates of the average treatment effects at different
periods along with uniform confidence bands evaluated using the procedure in
Section 2. These are from a single simulated dataset. For comparison, Figure
A.3 shows standard difference-in-differences estimates and the corresponding
block-bootstrap uniform confidence bands.

Figure A.2: Duration Diff-in-Diff Effect Estimates

(a)

(b)

(c)

Figure A.3: Standard Diff-in-Diff Effect Estimates

(a)

(b)

(c)

While the estimates in Figures A.2 and A.3 are from a single simulated
dataset, it is of note that even in large samples the standard diff-in-diff
treatment effect estimates appear to be biased downwards. This is not
surprising. In the absence of the intervention, Figure 1.a shows that the
difference between group $2$ and group $1$ mean outcomes shrinks over the
post-intervention period. Thus standard diff-in-diff will tend to
underestimate the post-treatment difference between the mean outcomes and thus
underestimate the average treatment effect. By contrast the estimates based on
our method appear to be consistent.

Figure A.4 contains estimates, each from a single Monte Carlo simulated
dataset, of the time-average hazards for various choices of the sample size
$n$. Immediately below we plot the corresponding estimates $\hat{\delta}_{t}$
of $\delta_{t}$ and associated uniform confidence bands. As we discuss in
Section 2, one can test pre-treatment parallel trends in the hazard rates by
observing whether or not these confidence bands contain zero in every period.
Thus the test would reject in the simulation with $n=500$.

Figure A.4: Time-Average Hazard Estimates

(a)

(b)

(c)

(d)

(e)

(f)

We simulate $10,000$ datasets. Table 2 below contains mean absolute biases,
mean squared errors, and the uniform and average (over time) pointwise
coverage of the uniform and pointwise confidence bands respectively. The table
contains the same numbers for the standard diff-in-diff method.

Table 2: Simulation Performance

Duration Difference-in-Differences
---
$n$ |  Absolute Bias |  Mean-Squared Error |  Confidence Band Coverage (Uniform) |  Confidence Band Coverage (Pointwise) |  Parallel Trends Test Rejects
$100$ |  0.00367 |  0.00164 |  0.963 |  0.961 |  0.052
$500$ |  0.00060 |  0.00031 |  0.953 |  0.952 |  0.049
$1000$ |  0.00033 |  0.00015 |  0.950 |  0.950 |  0.052
$5000$ |  0.00007 |  0.00003 |  0.945 |  0.947 |  0.053
$10000$ |  0.00005 |  0.00002 |  0.945 |  0.949 |  0.057
Standard Difference-in-Differences
$n$ |  Absolute Bias |  Mean-Squared Error |  Confidence Band Coverage (Uniform) |  Confidence Band Coverage (Pointwise) |  Parallel Trends Test Rejects
$100$ |  0.07221 |  0.00861 |  0.668 |  0.727 |  0.089
$500$ |  0.07205 |  0.00617 |  0.062 |  0.212 |  0.251
$1000$ |  0.07191 |  0.00586 |  0.001 |  0.056 |  0.446
$5000$ |  0.07196 |  0.00563 |  0.000 |  0.000 |  0.987
$10000$ |  0.07199 |  0.00560 |  0.000 |  0.000 |  1.000

Results are from $10,000$ simulation draws. Confidence bands are $95\%$-level.
Coverage of the uniform bands is uniform coverage, i.e., the share of
simulation draws in which the bands contained the true treatment effects for
all $t=t^{*},t^{*}+1,...,T$. Coverage of the pointwise bands is the share of
simulations in which the interval for period $t$ contained the true treatment
effect averaged over $t=t^{*},t^{*}+1,...,T$. The final column contains the
share of simulated datasets in which the duration and standard parallel trends
tests rejects, where the test is based on the block bootstrap as specified in
Section 2.3.

As one would expect, the duration diff-in-diff method, which is motivated by a
correctly specified model, greatly outperforms the standard diff-in-diff
procedure, which is based on a misspecified model. Encouragingly, both the
uniform and pointwise confidence bands appear to have approximately correct
coverage. Similarly, the duration parallel trends test has approximately
correct size. The standard test for parallel trends (based on the block
bootstrap) does show power greater than size, that is, the test that pre-
treatment trends in mean outcomes are parallel rejects with greater frequency
than $5\%$. However, the rejection frequency is fairly low apart from in large
samples.

##  Appendix B Bootstrap Inference Details

Below we provide a formal description of our bootstrap inference procedures.
Algorithm 1 provides instructions for constructing pointwise and uniform
confidence bands for the period-specific treatment effects proposed in Section
3.2. Algorithm 2 details the parallel trends test in Section 3.3.

Algorithm 1 Block Bootstrap Inference

1: For each $t=t^{*},,...,T$ evaluate the estimator $\hat{\tau}_{t}$ as in
Section 3.1.

2: for $b=1,2,...,B$ do

3: Independently draw a sequence of $n$ natural numbers uniformly from
$\\{1,2,...,n\\}$. Denote the sequence by
$\\{j_{b}(1),j_{b}(2),...,j_{b}(n)\\}$.

4: For each $t=t^{*},...,T$ evaluate the estimator $\hat{\tau}_{t}$ using
${Y}_{t,j_{b}(i)}$ in place of ${Y}_{i,t}$, ${G}_{t,j_{b}(i)}$ in place of
${G}_{i,t}$, and ${X}_{j_{b}(i)}$ in place of ${X}_{i}$ wherever they appear
in the formula. Call the resulting estimator $\hat{\tau}^{*}_{b,t}$.

5: end for

6: Calculate bootstrap standard errors $\hat{\sigma}_{t}$ for $t=t^{*},...,T$
as the standard deviation of the sample
$\\{\hat{\tau}^{*}_{b,t}\\}_{b=1}^{B}$.

7: For each $t=t^{*},...,T$ let the pointwise level $1-\alpha$ critical value
$\hat{q}_{1-\alpha,t}$ be the $1-\alpha$ quantile of
$\\{|\hat{\tau}^{*}_{b,t}-\hat{\tau}_{t}|/\hat{\sigma}_{t}\\}_{b=1}^{B}$. For
uniform critical values, instead use the $1-\alpha$ quantile of
$\\{\max_{t^{*}\leq s\leq
T}|\hat{\tau}^{*}_{b,s}-\hat{\tau}_{s}|/\hat{\sigma}_{s}\\}_{b=1}^{B}$ (note
this does not depend on $t$).

8: Form confidence bands by
$CI_{1-\alpha,t}=[\hat{\tau}_{t}-\hat{q}_{1-\alpha,t}\hat{\sigma}_{t},\hat{\tau}_{t}+\hat{q}_{1-\alpha,t}\hat{\sigma}_{t}]$

Algorithm 2 Specification testing

1: For each $t=2,...,t^{*}-1$ and $k=1,2$ evaluate the estimator
$\hat{H}_{k,t}$ with formula given in Section 2.1. Using these estimates
evaluate the difference-in-differences below:
$\hat{\delta}_{t}=(\hat{H}_{1,t}-\hat{H}_{2,t})-(\hat{H}_{1,t^{*}-1}-\hat{H}_{2,t^{*}-1})$

2: for $b=1,2,...,B$ do

3: Independently draw a sequence of $n$ natural numbers uniformly from
$\\{1,2,...,n\\}$. Denote the sequence by
$\\{j_{b}(1),j_{b}(2),...,j_{b}(n)\\}$.

4: For $k=1,2$ and each $t=t^{*},...,T$ evaluate the estimator $\hat{H}_{k,t}$
using ${Y}_{t,j_{b}(i)}$ in place of ${Y}_{i,t}$, ${G}_{t,j_{b}(i)}$ in place
of ${G}_{i,t}$, and ${X}_{j_{b}(i)}$ in place of ${X}_{i}$ wherever they
appear in the formula. Call the resulting estimator $\hat{H}^{*}_{b,k,t}$.
Using these, evaluate the following quantity:
$\hat{\delta}_{b,t}=(\hat{H}_{b,1,t}^{*}-\hat{H}_{b,2,t}^{*})-(\hat{H}_{b,1,t^{*}-1}^{*}-\hat{H}_{b,2,t^{*}-1}^{*})$

5: end for

6: Calculate bootstrap standard errors $\hat{\sigma}_{t}$ for
$t=2,...,t^{*}-2$ as the standard deviation of the sample
$\\{\hat{\delta}^{*}_{b,t}\\}_{b=1}^{B}$.

7: For each $t=2,...,t^{*}-2$ let the pointwise level $1-\alpha$ critical
value $\hat{q}_{1-\alpha}$ be the $1-\alpha$ quantile of $\\{\max_{2\leq s\leq
t^{*}-2}|\hat{\delta}^{*}_{b,s}-\hat{\delta}_{s}|/\hat{\sigma}_{s}\\}_{b=1}^{B}$.

8: Form confidence bands by
$CI_{1-\alpha,t}=[\hat{\tau}_{t}-\hat{q}_{1-\alpha}\hat{\sigma}_{t},\hat{\tau}_{t}+\hat{q}_{1-\alpha}\hat{\sigma}_{t}]$

9: Reject pre-treatment parallel trends if for any $2\leq t\leq t^{*}-2$, the
interval $CI_{1-\alpha,t}$ does not contain zero.

##  Appendix C Proofs

###### Proof of Proposition 1.

Recall the definition of $h_{k}^{(0)}(t)$:

$\displaystyle h_{k}^{(0)}(t)$ $\displaystyle=\lim_{\Delta\downarrow
0}\frac{P(Y_{i,t+\Delta}^{(0)}=1|Y_{i,t}^{(0)}=0,G_{i}=k)}{\Delta}$
$\displaystyle=\frac{1}{1-E[Y_{i,t}^{(0)}|,G_{i}=k]}\lim_{\Delta\downarrow
0}\frac{P(Y_{i,t+\Delta}^{(0)}=1,Y_{i,t}^{(0)}=0|G_{i}=k)}{\Delta}$

Given $Y_{i,t}^{(0)}=1$ is an absorbing state by Assumption 1, we have:

$P(Y_{i,t+\Delta}^{(0)}=1,Y_{i,t}^{(0)}=0|G_{i}=k)=E[Y_{i,t+\Delta}^{(0)}|G_{i}=k]-E[Y_{i,t}^{(0)}|G_{i}=k]$

And so:

$\displaystyle h_{k}^{(0)}(t)$ $\displaystyle=\lim_{\Delta\downarrow
0}\frac{E[Y_{i,t+\Delta}^{(0)}|G_{i}=k]-E[Y_{i,t}^{(0)}|G_{i}=k]}{(1-E[Y_{i,t}^{(0)}|G_{i}=k])\Delta}$
$\displaystyle=\frac{\frac{d}{dt}E[Y_{i,t}^{(0)}|G_{i}=k]}{1-E[Y_{i,t}^{(0)}|G_{i}=k]}$
$\displaystyle=-\frac{d}{dt}ln\big{(}1-E[Y_{i,t}^{(0)}|G_{i}=k]\big{)}$

So by the fundamental theorem of calculus:

$ln\big{(}1-E[Y_{i,t}^{(0)}|G_{i}=k]\big{)}=ln\big{(}1-E[Y_{i,1}^{(0)}|G_{i}=k]\big{)}-\int_{1}^{t}h_{k}^{(0)}(r)dr$

Set $k=1$ in the above and then subtract the same equation with $k=2$, we get:

$ln\bigg{(}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1]}{1-E[Y_{i,t}^{(0)}|G_{i}=2]}\bigg{)}=ln\bigg{(}\frac{1-E[Y_{i,1}^{(0)}|G_{i}=1]}{1-E[Y_{i,1}^{(0)}|G_{i}=2]}\bigg{)}-\int_{1}^{t}[h_{1}^{(0)}(r)-h_{2}^{(0)}(r)]dr$

Substituting in (2.2) then solving for $c$ we get:

$c=(t-1)^{-1}ln\bigg{(}\frac{1-E[Y_{i,1}^{(0)}|G_{i}=1]}{1-E[Y_{i,1}^{(0)}|G_{i}=2]}\bigg{)}-(t-1)^{-1}ln\bigg{(}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1]}{1-E[Y_{i,t}^{(0)}|G_{i}=2]}\bigg{)}$

Or equivalently:

$c=\frac{1}{t-1}ln\bigg{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=2]-1}{E[Y_{i,1}^{(0)}|G_{i}=2]-1}\bigg{)}-\frac{1}{t-1}ln\bigg{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=1]-1}{E[Y_{i,1}^{(0)}|G_{i}=1]-1}\bigg{)}$
(C.1)

Under Assumption 2 we have that for every $t<t^{*}$ and $k=1,2$,
$E[Y_{i,t}^{(0)}|G_{i}=k]=E[Y_{i,t}|G_{i}=k]$. Substituting gives the first
result. Solving (C.1) for $E[Y_{i,t}^{(0)}|G_{i}=1]$ we get:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1+(E[Y_{i,t}^{(0)}|G_{i}=2]-1)\bigg{(}\frac{E[Y_{i,1}^{(0)}|G_{i}=1]-1}{E[Y_{i,1}^{(0)}|G_{i}=2]-1}\bigg{)}exp\big{(}-(t-1)c\big{)}$

Using Assumption 2 we have $E[Y_{i,1}^{(0)}|G_{i}=1]=E[Y_{i,1}|G_{i}=1]$ and
for $1\leq t$ $E[Y_{i,t}^{(0)}|G_{i}=2]=E[Y_{i,t}|G_{i}=2]$, and
$E[Y_{i,1}^{(0)}|G_{i}=2]=E[Y_{i,1}|G_{i}=2]$. Substituting we get:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1+(E[Y_{i,t}|G_{i}=2]-1)\bigg{(}\frac{E[Y_{i,1}|G_{i}=1]-1}{E[Y_{i,1}|G_{i}=2]-1}\bigg{)}exp\big{(}-(t-1)c\big{)}$

Applying definitions and simplifying then gives the result.

∎

###### Proof of Theorem 1.

From the proof of Proposition 1 we have:

$-ln\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=k]-1}{E[Y_{i,1}^{(0)}|G_{i}=k]-1}\big{)}=\int_{1}^{t}h_{k}^{(0)}(r)dr$

Since this holds for all $k$ we get:

$\displaystyle-
ln\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=1]-1}{E[Y_{i,1}^{(0)}|G_{i}=1]-1}\big{)}+\sum_{k=2}^{K}W_{k}ln\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=k]-1}{E[Y_{i,1}^{(0)}|G_{i}=k]-1}\big{)}$
$\displaystyle=$
$\displaystyle\int_{1}^{t}\big{(}h_{1}^{(0)}(r)-\sum_{k=2}^{K}W_{k}h_{k}^{(0)}(r)\big{)}dr$

Substituting $W_{1}=h_{1}^{(0)}(r)-\sum_{k=2}^{K}W_{k}h_{k}^{(0)}(r)$ we get:

$-ln\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=1]-1}{E[Y_{i,1}^{(0)}|G_{i}=1]-1}\big{)}=(t-1)W_{1}-\sum_{k=2}^{K}W_{k}ln\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=k]-1}{E[Y_{i,1}^{(0)}|G_{i}=k]-1}\big{)}$

Under Assumption 2 we have that for $t<t^{*}$, and $k=1,...,K$,
$E[Y_{i,t}^{(0)}|G_{i}=k]=E[Y_{i,t}|G_{i}=k]$. Substituting gives the first
result. Solving for $E[Y_{i,t}^{(0)}|G_{i}=1]$ we get:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1+(E[Y_{i,1}^{(0)}|G_{i}=1]-1)\prod_{k=1}^{K}\big{(}\frac{E[Y_{i,t}^{(0)}|G_{i}=k]-1}{E[Y_{i,1}^{(0)}|G_{i}=k]-1}\big{)}^{W_{k}}exp\big{(}-(t-1)W_{1}\big{)}$

Using Assumption 2 we have $E[Y_{i,1}^{(0)}|G_{i}=1]=E[Y_{i,1}|G_{i}=1]$ and
for $1\leq t$ $E[Y_{i,t}^{(0)}|G_{i}=2]=E[Y_{i,t}|G_{i}=2]$, and
$E[Y_{i,1}^{(0)}|G_{i}=2]=E[Y_{i,1}|G_{i}=2]$. Using this and the above we
then have for $t^{*}\leq t$:

$E[Y_{i,t}^{(0)}|G_{i}=1]=1+(E[Y_{i,1}|G_{i}=1]-1)\prod_{k=1}^{K}\big{(}\frac{E[Y_{i,t}|G_{i}=k]-1}{E[Y_{i,1}|G_{i}=k]-1}\big{)}^{W_{k}}exp\big{(}-(t-1)W_{1}\big{)}$

Applying definitions and simplifying then gives the result.

∎

###### Proof of Theorem 2.

Recall that:

$h_{1}^{(0)}(t;x)=c+h_{2}^{(0)}(t;x)$

Following the same steps as in Theorem 1 but within a single stratum of the
covariates we get:

$ln\bigg{(}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1,X_{i,1}=x]}{1-E[Y_{i,1}^{(0)}|G_{i}=1,X_{i,1}=x]}\bigg{)}=(1-t)c+ln\bigg{(}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=2,X_{2,i}=x]}{1-E[Y_{i,1}^{(0)}|G_{i}=2,X_{2,i}=x]}\bigg{)}$

Applying the exponential function to both sides we get:

$\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1,X_{i,1}=x]}{1-E[Y_{i,1}^{(0)}|G_{i}=1,X_{i,1}=x]}=exp\big{(}(1-t)c\big{)}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=2,X_{2,i}=x]}{1-E[Y_{i,1}^{(0)}|G_{i}=2,X_{2,i}=x]}$
(C.2)

Define $\omega(x)$ as follows:

$\omega(x)=\frac{P(X_{i,1}=x|G_{i}=1,Y_{i,1}^{(0)}=0)}{P(X_{2,i}=x|G_{i}=1,Y_{i,1}^{(0)}=0)}$

Then from (C.2) and with some applications of Bayes’ rule we see that:

$\displaystyle\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1,X_{i,1}=x]}{1-E[Y_{i,1}^{(0)}|G_{i}=1]}P(X_{i,1}=x)$
$\displaystyle=$ $\displaystyle
exp\big{(}(1-t)c\big{)}\frac{E[\omega(X_{2,i})(1-Y_{i,t}^{(0)})|X_{2,i}=x,G_{i}=2]}{1-E[Y_{i,1}^{(0)}|G_{i}=2]}P(X_{2,i}=x)$

Summing over the values of $x$ and then taking logs, we get the following:

$\displaystyle-\frac{1}{t-1}ln\bigg{(}\frac{1-E[Y_{i,t}^{(0)}|G_{i}=1]}{1-E[Y_{i,1}^{(0)}|G_{i}=1]}\bigg{)}=$
$\displaystyle
c-\frac{1}{t-1}ln\big{(}\frac{E[\omega(X_{2,i})(1-Y_{i,t}^{(0)})|G_{i}=2]}{1-E[Y_{i,1}^{(0)}|G_{i}=2]}\big{)}$

Applying definitions gives the result.

∎