DP2024-22

Instrumented Difference-in-Differenceswith Heterogeneous Treatment Effects*

RIEB Junior Research Fellow

S h o M I YA J I

July 9, 2024

* This Discussion Paper won the Kanematsu Prize (FY 2023).

Instrumented Difference-in-Differences with heterogeneous
treatment effects∗
Sho Miyaji†
July 8, 2024

Abstract
Many studies exploit variation in the timing of policy adoption across units as an instrument for treatment, and use instrumental variable techniques. This paper formalizes
the underlying identification strategy as an instrumented difference-in-differences (DIDIV). In a simple setting with two periods and two groups, our DID-IV design mainly
consists of a monotonicity assumption, and parallel trends assumptions in the treatment
and the outcome. In this design, a Wald-DID estimand, which scales the DID estimand of
the outcome by the DID estimand of the treatment, captures the local average treatment
effect on the treated (LATET). In contrast to Fuzzy DID design considered in de Chaisemartin and D’Haultfœuille (2018), our DID-IV design does not ex-ante require strong
restrictions on the treatment adoption behavior across units, and our target parameter,
the LATET, is policy-relevant if the instrument is based on the policy change of interest
to the researcher. We extend the canonical DID-IV design to multiple period settings withthe staggered adoption of the instrument across units, which we call a staggered DID-IV
design. We propose an estimation method in staggered DID-IV design that is robust
to treatment effect heterogeneity. We illustrate our findings in the setting of Oreopoulos (2006), estimating returns to schooling in the United Kingdom. In this application,
the two-way fixed effects instrumental variable regression, which is the conventional approach to implement a staggered DID-IV design, yields a negative estimate, whereas ourestimation method indicates the substantial gain from schooling.

Keywords: difference-in-differences, instrumental variable, local average treatment effect, returns to education
JEL Classification: C21, C23, C26∗

This paper won the Kanematsu Prize from the Research Institution for Economics and Business Administration, Kobe University, in 2023. This paper also won the Best Young Scholar Award at SETA (Symposium
on Econometrics and Applications) Conference, Taipei, in 2024. I am grateful to my advisors, Daiji Kawaguchi
and Ryo Okui for their continued guidance and support. I am also thankful to Alberto Abadie, Shakeeb Khan,
Masamune Iwasawa, Shoya Ishimaru, Shosei Sakaguchi, Takahide Yanagi, and three anonymous referees of
the Kanematsu Prize for their insightful comments. The author gratefully acknowledges the support of JSPS
KAKENHI Grant Number JP 24KJ0817. All errors are my own.
†
Graduate School of Economics, The University of Tokyo, 7-3-1 Hongo, Bunkyoku, Tokyo 113-0033, Japan;
Email: shomiyaji-apple@g.ecc.u-tokyo.ac.jp.

11Introduction

Instrumental variable (IV) strategies are widely used for causal inference across many fields
in economics. Despite its popularity, empirical researchers commonly face two challenges in
employing the IV method in practice. The first challenge is the internal validity of the IV
estimate; in general, it is difficult to find an instrument that is randomized across units inpractice, especially in observational studies. The second challenge is the external validity of theIV estimate; under heterogeneous treatment effects, a linear IV estimand captures the averagetreatment effect, for those who are affected by the instrument, and this local average treatment
effect (LATE) may not be policy-relevant if the instrument does not represent the policy change
of interest to the researcher (Heckman and Vytlacil (2001), Heckman and Vytlacil (2005)).
To enhance at least the external validity of the IV estimate, many studies have exploited
variation in the timing of policy adoption across units as an instrument for treatment, anduse instrumental variable techniques. For example, Duflo (2001) estimates returns to schoolingin Indonesia, leveraging variation arising from the new school construction program acrossregions and cohorts as an instrument for education attainment. As another example, Blacket al. (2005) estimates the causal link between parents’ and children’s education attainment,using variation occurring from the different timing of implementation of school reform acrossmunicipalities and cohorts as an instrument for parents’ education attainment. The important
point here is that the underlying identification strategy behind these studies is inconsistent
with IV designs: the instrument based on these policy changes is not randomized across units
in reality, thereby potentially threatening the internal validity of the IV estimate. Rather, theunderlying identification strategy is similar to difference-in-differences (DID) designs, underwhich we identify the effect of the policy shock (treatment) on the outcome, exploiting thevariation of that policy change across units and over time.
In this paper, we formalize the underlying identification strategy as an instrumented differencein-differences (DID-IV). We define the target parameter and identifying assumptions in this design, and develop a credible estimation method that is robust to treatment effect heterogeneity
in multiple time periods settings. Importantly, this design does not require the randomization
assumption of the instrument. In this design, we can achieve the internal and external validityof the IV estimate if the parallel trends assumptions in the treatment and the outcome areplausible in a given application, and the instrument is based on the policy shift of interest to
the researcher.
First, we consider a simple setting with two periods and two groups: some units are notexposed to the instrument over two periods (unexposed group), whereas some units become
exposed at the second period (exposed group). In this setting, our target parameter is the
local average treatment effect on the treated (LATET); this parameter measures the treatment
effects, for those who belong to an exposed group and are induced to treatment by instrument in the second period. Our DID-IV design mainly consists of a monotonicity assumption,and parallel trends assumptions in the treatment and the outcome between exposed and unexposed groups. This framework comes from a simple and motivating observation: in the
two-group/two-period (2 × 2) settings, a popular estimand, which we call the Wald-DID estimand, scales the DID estimand of the outcome by the DID estimand of the treatment between
the two groups. Indeed, we show that the Wald-DID estimand captures the LATET under 2×2
DID-IV designs.
In DID-IV designs, the interpretation of the parallel trends assumption in the outcome
is less clear than that of the parallel trends assumption in DID designs because it does notdepend on the untreated outcome, but depends on the outcome under no exposure to the1instrument, which we call an unexposed outcome. Motivated by this observation, we next
clarify the interpretation of the parallel trends assumption in the outcome in DID-IV designs.
Specifically, we first uncover the selection mechanism behind DID-IV designs; we show that in
DID-IV settings, time also plays the role of instrument, that is, time also affects one’s treatment
choices over time in the absence of the policy shock. Following to the terminology in Imbens andAngrist (1994), we divide the population into time groups defined by the potential treatment
choices without instrument during the two periods: time always-takers, time never-takers, timecompliers, and time defiers. For instance, the time compliers do not adopt the treatment in
the first period, but become adopt it in the second period without instrument. We then showthat the average time trend in the unexposed outcome equals a weighted average of the indirect
effect of time on the outcome through treatment in each time group. We call this an expected
time gain, and show that the parallel trends assumption in the outcome in DID-IV designs
requires the same expected time gain between exposed and unexposed groups.
de Chaisemartin and D’Haultfœuille (2018) (hereafter, ”dCDH” in this section) also consider
the same setting in this article, but formalize 2 × 2 DID-IV designs differently, calling themFuzzy DID designs. The main difference between this article and dCDH lies in the definition oftarget parameter: we focus on the LATET, whereas dCDH focus on the switcher local averagetreatment effect on the treated (SLATET); this parameter measures the treatment effects, forthose who belong to an exposed group and start to receive the treatment in the second period.
Accordingly, the identifying assumptions in dCDH are also different from those in this article.
Furthermore, dCDH argue that the Wald-DID estimand identifies the SLATET under Fuzzy
DID designs if the treatment effect is stable over time, and propose the alternative estimands
that are free from the strong restriction on treatment effect heterogeneity.
Motivated by the disagreement between this article and dCDH, we next compare DID-IV
designs to Fuzzy DID designs, and point out the issues inherent in Fuzzy DID designs. First,
we show that dCDH’s identifying assumptions ex-ante impose the strong restrictions on thetreatment adoption behavior across units. It turns out that these restrictions are asymmetricbetween exposed and unexposed groups, and difficult to defend from the institutional knowledgeof the problem in a given application. Next, under these restrictions, we show that dCDH’s
target parameter, the SLATET, can be decomposed into a weighted average of two different
causal parameters: one parameter measures the treatment effects among the sub-population of
the compliers and the other parameter measures the treatment effects among the time compliers,
who are affected by time but not affected by instrument. This decomposition result for the
SLATET has two concerning implications. First, the interpretation of the SLATET is less clear
than that of the LATET in DID-IV designs. Second, the SLATET may not be policy-relevant
even when the instrument is based on the policy change of interest to the researcher because
this parameter is always contaminated by the treatment effects among the time compliers.
We also revisit the ”issue” raised by dCDH regarding the use of the Wald-DID estimand,and demonstrate that while their argument is correct, it is misguided. Specifically, we firstshow that their argument stems from their reliance on the parallel trends assumption in DID
designs. We then argue that this assumption is unsuitable for DID-IV settings for three reasons.
First, this assumption generally fails to capture the average time trends of the outcome evenin an unexposed group. This is because in DID-IV settings, units are allowed to receive thetreatment in the absence of the policy shock (instrument). Second, in most applications of
the DID-IV method, it is generally infeasible to impute the untreated potential outcomes (e.g.,
Duflo (2001), Black et al. (2005)). For instance, in Black et al. (2005), this assumption requiresthat the data contain the units with zero education attainment, which is unrealistic in practice.
Finally, in DID-IV settings, we can not directly test this assumption using the pre-exposed2

period data in general. Indeed, we show that the placebo test proposed by dCDH is incomplete
for assessing the plausibility of this assumption.
Next, we extend the canonical DID-IV design to multiple period settings with the staggered
adoption of the instrument across units. In this setting, units start exposed to the instrument
at a particular point in time and remain exposed to that instrument afterward. Indeed, inmost DID-IV applications, researchers exploit variation in the timing of policy adoption acrossunits in more than two periods, instrumenting for the treatment with the natural variation.
The instrument is constructed, for instance from the staggered adoption of school reforms
across municipalities or across countries (e.g. Oreopoulos (2006), Lundborg et al. (2014), andMeghir et al. (2018)), the phase-in introduction of head starts across states (e.g. Johnson andJackson (2019)), or the gradual adoption of broadband internet programs across municipalities(e.g. Akerman et al. (2015), Bhuller et al. (2013)). We refer to the underlying identification
strategy as a staggered DID-IV design, and establish the target parameter and identifying
assumptions. Specifically, in this design, we first partition units into mutually exclusive andexhaustive cohorts by the initial exposure date of the instrument. We then define our target
parameter as the cohort specific local average treatment effect on the treated (CLATT); thisparameter is a natural generalization of the LATET in 2 × 2 DID-IV designs, and measures thetreatment effects, for those who belong to cohort e and are the compliers at a given relative
period l from the initial exposure to the instrument. Finally, we extend the identification
assumptions in 2 × 2 DID-IV designs to multiple period settings and state the interpretationof each assumption.
We extend our DID-IV designs in several directions. We first show that our DID-IV framework can be applied when we have a non-binary, ordered treatment. We also consider extensions
to repeated cross sections, and triple DID-IV designs. Lastly, we consider the case when we
introduce the treatment path in potential outcomes in 2 × 2 DID-IV designs.
Finally, we propose a regression-based method to consistently estimate our target parameter in staggered DID-IV designs under heterogeneous treatment effects. In practice, when researchers implicitly rely on a staggered DID-IV design, they usually implement this design via
two-way fixed effects instrumental variable regressions. In companion paper (Miyaji (2024)),
however, we show that in more than two periods, the TWFEIV estimand generally fails tosummarize the treatment effects under staggered DID-IV designs. Specifically, Miyaji (2024)shows that under staggered DID-IV designs, the TWFEIV estimand is a weighted average ofall possible CLATTs, but some weights can be negative if the effect of the instrument on thetreatment or the outcome is not stable over time. Our proposed method avoids this issue andis robust to treatment effect heterogeneity. Our estimation procedure consists of two steps.
First, we subset the data which contain only two cohorts and two periods. Next, in each dataset, we run the TWFEIV regression. We call this a stacked two stage least squares (STS) regression and ensure its validity. Following to Callaway and Sant’Anna (2021), we also propose
the weighting scheme to summarize the treatment effects under staggered DID-IV designs. In
our weighting scheme, the weight reflects the share of compliers in a given relative period l incohort e. We also discuss the procedure of pretrends tests to check the validity of the parallel
trends assumptions in the treatment and the outcome in DID-IV designs.
We illustrate our findings with the setting of Oreopoulos (2006) who estimate returns toschooling in the United Kingdom, exploiting variation in the timing of implementation of school
reforms between Britain and North Ireland as an instrument for education attainment. In
this application, we first assess the plausibility of DID-IV identification assumptions implicitly
imposed by Oreopoulos (2006). We then estimate the TWFEIV regression in the author’s
setting. We find that the TWFEIV estimate is strictly negative and not significantly different
3from zero. Actually, the TWFEIV regression performs the ”bad comparisons” (c.f. GoodmanBacon (2021)) in the author’s setting: we treat the already exposed units as controls during theperiods after both regions were affected by the policy change. Finally, we use our estimation
method to reassess returns to schooling in the U.K. We find that our STS estimates are all
positive in each relative period after the school reform, and our weighting scheme yields a moreplausible estimate than the TWFEIV estimate. Specifically, our weighting estimate indicatesthe roughly 20% gain from schooling in the U.K.
Overall, this paper provides a new econometric framework by combining the IV techniqueswith DID designs. Our DID-IV design can be applied to various empirical settings. First, it
can cope with the general adoption process of the treatment when we are interested in theeffect of the treatment on the outcome in DID designs. For instance, consider the case thatsome units already receive the treatment in period 0 before the policy shock, which distributes
the treatment in period 1. In this setting, the canonical DID design is infeasible in practiceunless we ex-ante discard these units from the data. On the other hand, our DID-IV design
can be directly applied to this setting, allowing us to identify the LATET. In other words, we
can view that DID-IV is DID with the noncompliance of the assigned treatment.
Second, our DID-IV design can yield valid counterfactuals to estimate the treatment effectwhen we have no control group under DID designs. For instance, suppose that the treatment is
education attainment and we are interested in returns to schooling as in Duflo (2001). In thissetting, the canonical DID design generally fails to construct the control group, as the data
would not contain the units with zero education attainment in reality. On the other hand, our
DID-IV design can partition units into exposed and unexposed groups depending on whether
the unit is exposed to the policy shock (instrument). Once these groups are created under
this design, one can identify the LATET by comparing the evolution of the treatment and theoutcome between the two groups.
Finally, our DID-IV design can overcome the endogeneity issue in empirical work. In practice, due to the endogenous adoption of the treatment over time, researchers often fail to
identify the treatment effect via simple linear regressions or two-way fixed effects regressions
in panel data settings. In our DID-IV design, one can cope with the common identification
challenge by leveraging variation in the timing of policy adoption across units as an instrument
for treatment. Importantly, in this design, the identifying variation does not come from therandom assignment of the policy shock across units; it mainly comes from the parallel trends
assumption in the treatment and the outcome over time. This identification strategy would
be less demanding than IV designs in some applications, enhancing the internal and external
validity of the IV estimate in practice.
The rest of the paper is organized as follows. The next subsection discusses the related
literature. Section 2 establishes DID-IV designs in a simple setting with two periods and twogroups. Section 3 formalizes the target parameter and identifying assumptions in staggered
DID-IV designs. Section 4 contains extensions. Section 5 presents our estimation method.
Section 6 presents our empirical application. Section 7 concludes. All proofs are given in the
Appendix.
1.1

Related literature

Our paper is related to a recent DID-IV literature (de Chaisemartin (2010); Hudson et al.
(2017); de Chaisemartin and D’Haultfœuille (2018)). We contribute to this literature in threeimportant ways.
The first contribution of this paper is to investigate the detailed connections between DIDIV and Fuzzy DID designs proposed by de Chaisemartin and D’Haultfœuille (2018) (henceforth,
4

”dCDH” in this section). In econometrics, a pioneering work formalizing 2 × 2 DID-IV designs
is de Chaisemartin (2010), who shows that the Wald-DID estimand identifies the local averagetreatment effect on the treated (LATET) under parallel trends assumptions in the treatment
and the outcome, and a monotonicity assumption. Hudson et al. (2017) also consider 2×2 DIDIV designs with non-binary, ordered treatment settings. Build on the work in de Chaisemartin(2010), however, de Chaisemartin and D’Haultfœuille (2018) formalize 2 × 2 DID-IV designs
differently and call them Fuzzy DID designs; the settings are the same between the two designs,
but the target parameter and identifying assumptions are different from each other.
In this paper, we first formalize 2 × 2 DID-IV designs and complement de Chaisemartin(2010) and Hudson et al. (2017). Specifically, we introduce the path of the instrument in
2 × 2 DID-IV designs and uncover the ”hidden assumption” in the previous literature. This
assumption requires the no anticipatory behavior of the treatment adoption before the exposure
to the instrument. We also investigate the selection mechanism behind 2 × 2 DID-IV designs,
and clarify the interpretation of the parallel trends assumption in the outcome.
Given our identification results and the terminology developed in this paper, we then compare DID-IV to Fuzzy DID designs, and point out the issues inherent in Fuzzy DID designs.
Specifically, we show that the identifying assumptions in Fuzzy DID designs ex-ante requires
the strong restrictions on the treatment adoption behavior across units, and the target parameter in Fuzzy DID designs can be decomposed into a weighted average of two different causal
parameters. The discussion organizes the relationship between the two designs in the previous literature, which essentially treat the same setting, and indicate the relative advantages of
DID-IV over Fuzzy DID.
The second contribution of this paper is to extend 2 × 2 DID-IV designs to multiple period
settings with the staggered adoption of the instrument across units. In practice, in order toestimate the treatment effects, empirical researchers often leverage variation in the timing ofpolicy adoption across units as an instrument for treatment in more than two periods (e.g.,
Black et al. (2005), Lundborg et al. (2014), and Johnson and Jackson (2019)). No previous
studies, however, extend 2 × 2 DID-IV designs to such important settings. Our staggered DIDIV designs ensure the theoretical validity of the underlying identification strategy behind thesestudies, and allow the practitioners to estimate the local average treatment effect on the treatedeven when the treatment adoption is endogenous over time.
Finally, this paper provides a credible estimation method in staggered DID-IV designs underheterogeneous treatment effects. When empirical researchers implicitly rely on the staggered
DID-IV design in practice, they commonly implement this design via TWFEIV regressions (e.g.
Black et al. (2005), Lundborg et al. (2014)). In companion paper (Miyaji (2024)), however, weshow that the TWFEIV estimand potentially fails to summarize the treatment effects understaggered DID-IV designs if the effect of the instrument on the treatment or the outcome evolves
over time. Our proposed estimation method would serve as an alternative to the TWFEIV
estimator and make DID-IV designs more credible in a given application.
Our paper is also related to a recent and growing DID literature. Several recent papers
have pointed out the issue of implementing DID designs via two-way fixed effects regressions
or its dynamic specifications in the presence of heterogeneous treatment effects (Athey and
Imbens (2022); Borusyak et al. (2021); Callaway and Sant’Anna (2021); de Chaisemartin
and D’Haultfœuille (2020); Goodman-Bacon (2021); Imai and Kim (2021); Sun and Abraham(2021)). All of these papers have documented that regression coefficients by the conventional
approaches may fail to properly summarize treatment effects under DID designs. Some of these
papers have proposed an alternative estimation method that delivers a sensible estimand and isrobust to treatment effect heterogeneity. None of these papers, however, have explicitly consid5

ered the causal interpretation of the TWFEIV estimand when researchers exploit variation in
the timing of policy adoption across units as an instrument for the treatment. In this paper, weformalize the rationale behind using the TWFEIV regression as an instrumented difference-indifferences design, and provide a reliable estimation method in this design in multiple periods
settings. Built on the work in this paper, Miyaji (2024) studies the properties of the TWFEIV
estimand under staggered DID-IV design and point out the issue of implementing this design
via TWFEIV regressions.

2

DID-IV in two time periods

In this section, we formalize an instrumented difference-in-differences (DID-IV) in two-period/twogroup settings. We first establish the target parameter and identifying assumptions in thisdesign. We then uncover the selection mechanism behind this design, and clarify the interpretation of the parallel assumption in the outcome. We next describe the relationship between
DID and DID-IV, indicating that DID-IV is DID with the noncompliance of the assigned treatment. At the end of this section, we also describe the connections between DID-IV and Fuzzy
DID proposed by de Chaisemartin and D’Haultfœuille (2018).
2.1

Set up

We introduce the notation we use throughout section 2. We consider a panel data setting withtwo periods and N units. For any random variable R, we denote S(R) to be its support. For
each i ∈ {1, . . . , N } and t ∈ {0, 1}, let Yi,t denote the outcome, and Di,t ∈ {0, 1} denote thetreatment status: Di,t = 1 if unit i receives the treatment in period t and Di,t = 0 if unit i does
not receives the treatment in period t. Let Zi,t ∈ {0, 1} denote the instrument status: Zi,t = 1
if unit i is exposed to the instrument in period t and Zi,t = 0 if unit i is not exposed to the
instrument in period t. Throughout section 2, we assume that {Yi,0 , Yi,1 , Di,0 , Di,1 , Zi,0 , Zi,1 }Ni=1
are independent and identically distributed (i.i.d).
We introduce the path of the treatment and the instrument. Let Di = (Di,0 , Di,1 ) be thetreatment path and Zi = (Zi,0 , Zi,1 ) be the instrument path. We assume that no one is exposedto the instrument in period t = 0: Zi,0 = 0 for all i. Hereafter, we refer to this as a sharp
assignment of the instrument. We denote Ei ∈ {0, 1} to be the group variable: Ei = 1 ifunit i is exposed to the instrument in period t = 1 (exposed group) and Ei = 0 if unit i is
not exposed to the instrument in period t = 1 (unexposed group). In contrast to the sharp
assignment of the instrument, we allow the general adoption process for the treatment: weassume that the treatment path can take four values with non-zero probability, that is, we have{(0, 0), (0, 1), (1, 0), (1, 1)} ∈ S(D).
In practice, researchers are interested in the effect of a treatment Di,t on an outcome Yi,t , andthe instrument Zi,1 typically represents a program or a policy shock, which occurs in periodt = 1 and encourages people to adopt the treatment. For instance, Duflo (2001) estimates
returns to schooling in Indonesia, using a new school construction program across regions as
an instrument for education attainment.
Next, we introduce the potential outcomes framework. Let Yi,t (d, z) denote the potential
outcome in period t when unit i receives the treatment path d ∈ S(D) and the instrument
path z ∈ S(Z). Similarly, let Di,t (z) denote the potential treatment status in period t whenunit i receives the instrument path z ∈ S(Z). Hereafter, we refer to Di,t ((0, 0)) as unexposed
treatment and Di,t ((0, 1)) as exposed treatment.
We make a no carryover assumption on the potential outcomes Yi,t (d, z).
6

Assumption 1 (No carryover assumption).
∀z ∈ S(Z), ∀d ∈ S(D), Yi,0 (d, z) = Yi,0 (d0 , z), Yi,1 (d, z) = Yi,1 (d1 , z),where d = (d0 , d1 ) is the generic element of the treatment path Di .
Assumption 1 states that potential outcomes Yi,t (d, z) depend only on the current treatment
status dt and the instrument path z. In the DID literature, several recent papers impose
this assumption with settings of a non-staggered treatment; see, e.g., de Chaisemartin and
D’Haultfœuille (2020) and Imai and Kim (2021).1
Next, we introduce the group variable GZi ≡ (Di,1 ((0, 0)), Di,1 ((0, 1))), which describes thetype of unit i according to the response of Di,1 on the instrument path z. Specifically, thefirst element Di,1 ((0, 0)) represents the potential treatment choice in period t = 1 if unit ibelongs to an unexposed group, and the second element Di,1 ((0, 1)) represents the potential
treatment choice in period t = 1 if unit i belongs to an exposed group. Following to theterminology in Imbens and Angrist (1994), we define GZi = (0, 0) ≡ N T Z to be the nevertakers, GZi = (1, 1) ≡ AT Z to be the always-takers, GZi = (0, 1) ≡ CM Z to be the compliers,
and GZi = (1, 0) ≡ DF Z to be the defiers.
Henceforth, we keep Assumption 1. In the next section, we use the notations developed so
far to define our target parameter in 2 × 2 DID-IV designs.
2.2

Target parameter in two time periods

In 2 × 2 DID-IV designs, our target parameter is the local average treatment effect on thetreated (LATET) in period t = 1 defined below.
Definition. The local average treatment effect on the treated (LATET) in period t = 1 is
LAT ET ≡ E[Yi,1 (1) − Yi,1 (0)|Ei = 1, Di,1 ((0, 1)) > Di,1 ((0, 0))]= E[Yi,1 (1) − Yi,1 (0)|Ei = 1, CM Z ].
This parameter measures the treatment effects in period 1, for those who belong to an
exposed group (Ei = 1), and are induced to treatment by instrument in period 1. In the
DID-IV literature, de Chaisemartin (2010) consider the same target parameter, and Hudson
et al. (2017) define the local treatment effect (LATE) in period t = 1 as their target parameter,
which is unconditional on Ei . The LATET has been also proposed in heterogeneous effects IV
models with binary instrument; see, e.g., Sloczyński et al. (2022) and Sloczyński (2020).
We define the LATET as our target parameter for two reasons. First, this parameter would
be particularly of interest if the instrument reflects a policy change of interest (Heckman and
Vytlacil (2001), Heckman and Vytlacil (2005)). Duflo (2001), for instance, are interested in”whether investments in infrastructure can cause an increase in education attainment, andwhether an increase in education attainment causes an increase in earnings”. To answer thisquestion, the author exploits a new school construction program across regions as an instrument
for education attainment. In this context, the LATET would be a policy-relevant parameterin the presence of heterogeneous treatment effects. Second, the LATET is a natural extension
1

When treatment is binary and there exist only two periods, one can explicitly introduce the treatment
path in potential outcomes because it takes only four values. We therefore consider this case in Appendix B
as an extension. One can also weaken Assumption 1 in other cases such as non-binary, ordered treatments or
multiple time periods, but this would requires the cumbersome notation and complicates the definition of ourtarget parameter, thus is beyond scope of this paper.

7

of the target parameter in DID designs, the so-called average treatment effects on the treated(ATT). In section 2.5, we show that both causal parameters measure the treatment effects
among the units who are affected by instrument (policy shock) and belong to an exposed group(Ei = 1).
Remark 1. de Chaisemartin and D’Haultfœuille (2018) define the switcher local average treatment effect on the treated (SLATET) as their target parameter in the same setting we areconsidering here2 .
Definition. The switcher local average treatment effect on the treated (SLATET) is
SLAT ET ≡ E[Yi,1 (1) − Yi,1 (0)|Ei = 1, Di,1 ((0, 1)) > Di,0 ((0, 1))]= E[Yi,1 (1) − Yi,1 (0)|Ei = 1, SW ],where the switcher (SW) is the units who become treated in period 1.
This parameter measures the treatment effects among the units who belong to an exposedgroup (Ei = 1) and switch to receive the treatment in period 1 (SW). As we will show in Appendix E, it turns out that this parameter is different from the LATET and can be decomposed
into a weighted average of two different causal parameters. In section 2.6, we provide a detailed
discussion of the connections between this article and de Chaisemartin and D’Haultfœuille(2018).
2.3

Identification assumptions in two time periods

This section establishes DID-IV designs in a simple setting with two groups and two periods.
In this setting, a popular estimand is the ratio between the DID estimand of the outcome andthe DID estimand of the treatment (Duflo (2001), Field (2007)):
wDID =

E[Yi,1 − Yi,0 |Ei = 1] − E[Yi,1 − Yi,0 |Ei = 0].
E[Di,1 − Di,0 |Ei = 1] − E[Di,1 − Di,0 |Ei = 0]

Following to the terminology in de Chaisemartin and D’Haultfœuille (2018), we call this the
Wald-DID estimand. This estimand is obtained from the IV regression of the outcome on thetreatment where the group and post-time dummies are included instruments and the interactionof the two is excluded instrument.
In practice, the Wald-DID estimand wDID is commonly interpreted as measuring the local
average treatment effect (LATE) in the presence of heterogeneous treatment effects, but theunderlying identifying assumptions are not stated formally. Duflo (2001), for instance, notesthat ”if returns to education are not constant, the 2SLS estimates are a weighted average ofthe returns to education for people who are affected by the instruments (Angrist and Imbens(1995))”.
We consider the following identifying assumptions for the Wald-DID estimand to capture the
LATET. Henceforth, we assume that the denominator of the Wald-DID estimand is different
from zero without loss of generality.
Assumption 2 (Exclusion restriction for potential outcomes).
∀z ∈ S(Z), ∀d ∈ S(D), ∀t ∈ {0, 1}, Yi,t (d, z) = Yi,t (d).
2de Chaisemartin and D’Haultfœuille (2018) consider the same situation in repeated cross section settings.
We therefore rewrite their target parameter by the notation we use in this article.

8This assumption requires that the instrument path does not directly affect potential outcomes other than through treatment. This assumption is common in the IV literature; seee.g., Imbens and Angrist (1994) and Abadie (2003). In the DID-IV literature, de Chaisemartin(2010) and Hudson et al. (2017) impose a similar assumption without introducing the instrument path.
Given Assumption 1 and Assumption 2, we can write the observed outcomes Yi,t as
Yi,t = Di,t Yi,t (1) + (1 − Di,t )Yi,t (0).
Assumption 1 and Assumption 2 also allow us to introduce the notion of exposed andunexposed outcomes. For any z ∈ S(Z), let Yi,t (Di,t (z)) denote the potential outcome if the
instrument path were z:
Yi,t (Di,t (z)) ≡ Di,t (z)Yi,t (1) + (1 − Di,t (z))Yi,t (0).
Hereafter, we refer to Yi,t (Di,t ((0, 0))) as unexposed outcomes and Yi,t (Di,t ((0, 1))) as exposed
outcomes. Note that we can not observe different potential outcomes for the same unit at thesame time. For instance, when unit i is assigned to z = (0, 0), that is, unit i is not exposedto the instrument during the two periods, we can observe only Yi,t (Di,t ((0, 0))), and can notobserve Yi,t (Di,t ((0, 1))) for that unit.
Next, we make the following monotonicity assumption as in Imbens and Angrist (1994).
Assumption 3 (Monotonicity Assumption in period t = 1).
P r(Di,1 ((0, 1)) ≥ Di,1 ((0, 0))) = 1 or P r(Di,1 ((0, 1)) ≤ Di,1 ((0, 0))) = 1.
This assumption requires that the instrument path affects the treatment choice at period t = 1 in a monotone (uniform) way. This assumption implies that the group variable
GZi = (Di,1 ((0, 0)), Di,1 ((0, 1))) can take three values with non-zero probability. In the DID-IV
literature, de Chaisemartin (2010) and Hudson et al. (2017) make the same assumption. Hereafter, we consider the type of monotonicity assumption which rules out the existence of thedefiers DF Z .
Assumption 4 (No anticipation in the first stage).
Di,0 ((0, 1)) = Di,0 ((0, 0)) a.s. for all units i with Ei = 1.
Assumption 4 requires that the potential treatment choice before the exposure to instrument
is equal to the baseline treatment choice Di,0 ((0, 0)) in an exposed group. This assumption
restricts the anticipatory behavior and would be plausible if the instrument path is ex-ante notknown for all the units in an exposed group. This assumption is ”hidden assumption” in theprevious DID-IV literature: de Chaisemartin (2010) and Hudson et al. (2017) implicitly impose
this assumption by writing observed treatment choice in period t = 0 as Di,0 (0).
In the DID literature, recent studies impose the no anticipation assumption on untreatedpotential outcomes in several ways. Callaway and Sant’Anna (2021) and Sun and Abraham(2021) assume the average version of the no anticipation assumption, whereas Athey and Imbens(2022) assume the no anticipation for all units i. Roth et al. (2023) take the intermediate approach: they assume the no anticipation for the treated units. Our no anticipation assumption
on potential treatment choices is in line with that of Roth et al. (2023).
Next, we impose the parallel trends assumptions in the treatment and the outcome. In
the DID-IV literature, de Chaisemartin (2010) and Hudson et al. (2017) assume the similarassumptions.
9Assumption 5 (Parallel Trends Assumption in the treatment).
E[Di,1 ((0, 0)) − Di,0 ((0, 0))|Ei = 0] = E[Di,1 ((0, 0)) − Di,0 ((0, 0))|Ei = 1].
Assumption 5 is a parallel trends assumption in the treatment. This assumption requiresthat the expectation of the treatment between exposed and unexposed groups would havefollowed the same path if the assignment of the instrument had not occurred. For instance, in
Duflo (2001), this assumption requires that the evolution of mean education attainment would
have been the same between exposed and unexposed groups if the policy shock had not occurred
during two periods.
Assumption 6 (Parallel Trends Assumption in the outcome).
E[Yi,1 (Di,1 ((0, 0))) − Yi,0 (Di,0 ((0, 0)))|Ei = 0] = E[Yi,1 (Di,1 ((0, 0))) − Yi,0 (Di,0 ((0, 0)))|Ei = 1].
Assumption 6 is a parallel trends assumption in the outcome. This assumption requiresthat the evolution of the unexposed outcome is the same on average between exposed andunexposed groups. For instance, in Duflo (2001), this assumption requires that the expectationof log annual earnings would have followed the same path from period 0 to period 1 between
exposed and unexposed groups in the absence of the policy shock.
When empirical researchers exploit variation arising from policy shock as an instrument for
the treatment and use the Wald-DID estimand, they often refer to Assumption 5 and 6. For
instance, Duflo (2001) estimates returns to schooling in Indonesia, relying on ”the identification
assumption that the evolution of wages and education across cohorts would not have variedsystematically from one region to another in the absence of the program”.
The theorem below shows that if Assumptions 1 - 6 hold, the Wald-DID estimand captures
the local average treatment effects on the treated (LATET) in period 1.
Theorem 1. If Assumptions 1-6 hold, the Wald-DID estimand wDID is equal to the LATET
in period t = 1, that is,
wDID = E[Yi,1 (1) − Yi,1 (0)|Ei = 1, CM Z ].
holds.
Proof. See Appendix A.
We now provide the intuition behind 2 × 2 DID-IV designs. As we already noted, the WaldDID estimand scales the DID estimand of the outcome by the DID estimand of the treatment.
Motivated by this observation, under 2 × 2 DID-IV designs, we rely on the common DID identification strategy both in the numerator and the denominator of the Wald-DID estimand (seeFigure 1). First, in the denominator of the Wald-DID estimand, we use the DID identification
strategy to identify the direct effect of the instrument on the treatment: we recover the expectation of the unexposed treatment in period t = 1 in an exposed group (z = (0, 1)), using
Assumption 4 (no anticipation in the first stage) and Assumption 5 (parallel trends assumption in the treatment). Next, in the numerator of the Wald-DID estimand, we use the DID
identification strategy in order to identify the indirect effect of the instrument on the outcome
through treatment: we recover the expectation of the unexposed outcome in period t = 1 in an
exposed group (z = (0, 1)), using Assumption 6 (parallel trends assumption in the outcome).
Finally, by scaling the indirect effect obtained from the numerator by the direct effect obtained
from the denominator, we can capture the LATET in period t = 1.
10

Fig. 1. DID-IV identification strategy in two periods and two groups. Notes: This figure plots the evolutionof the expectation of the treatment (First stage DID) and the outcome (Reduced form DID) for exposed andunexposed groups respectively. The dotted line represents the counterfactual trends of the expectation of thetreatment and the outcome in an exposed group. The effects of the instrument on the treatment and theoutcome are 0.2 and 2 respectively, and the local average treatment effect on the treated is 10.

2.4Interpreting the parallel trends assumption in the outcome

So far, we have formalized the target parameter and identifying assumptions in 2 × 2 DID-IV
designs. Overall, in this design, we rely on the common DID identification strategy in both
the denominator and the numerator of the Wald-DID estimand in order to identify the effectsof the instrument on the treatment and the outcome. The interpretation of the parallel trends
assumption in the outcome, however, is less clear than that of the parallel trends assumption in
the canonical DID designs because it does not depend on the untreated outcome, but depends
on the unexposed outcome.
In this section, we clarify the interpretation of the parallel trends assumption in the outcome
in 2×2 DID-IV designs. To do so, we first uncover the selection mechanism behind the canonical
DID-IV designs. Specifically, we show that in 2 × 2 DID-IV designs, time also plays the role of
instrument, and investigate how the identifying assumptions in 2 × 2 DID-IV designs restrict
the treatment adoption behavior across units in exposed and unexposed groups, respectively.
We then show that the average time trend in the outcome is equal to a weighted average ofthe indirect effect of time on the outcome through treatment. We call this an expected time
gain and show that the parallel trends assumption in the outcome requires the homogeneous
expected time gain between exposed and unexposed groups.
First, we introduce the additional notation. Let GTi = (Di,0 ((0, 0)), Di,1 ((0, 0))) denote thegroup variable for unit i, which represents the treatment adoption process from period 0 toperiod 1 if the instrument path were z = (0, 0): the first element Di,0 ((0, 0)) represents thepotential treatment choice without instrument in period 0 and the second element Di,1 ((0, 0))represents the potential treatment choice without instrument in period 1.
11

Table 1. Exposed group (assigned to z = (0, 1))

observed(D0 ((0, 0)), D1 ((0, 1)))D0 ((0, 0)) = 1, D1 ((0, 1)) = 1
D0 ((0, 0)) = 1, D1 ((0, 1)) = 0
D0 ((0, 0)) = 0, D1 ((0, 1)) = 1
D0 ((0, 0)) = 0, D1 ((0, 1)) = 0

counterfactual
D1 ((0, 0)) = 1
D1 ((0, 0)) = 0
ZTAT ∧ ATCM Z ∧ DF T
DF Z ∧ AT T
N T Z ∧ DF T
AT Z ∧ CM T
CM Z ∧ N T T
DF Z ∧ CM T
NT Z ∧ NT T

Table 2. Unexposed group (assigned to z = (0, 0))observed(D0 ((0, 0)), D1 ((0, 0)))D0 ((0, 0)) = 1, D1 ((0, 0)) = 1
D0 ((0, 0)) = 1, D1 ((0, 0)) = 0
D0 ((0, 0)) = 0, D1 ((0, 0)) = 1
D0 ((0, 0)) = 0, D1 ((0, 0)) = 0

counterfactual
D1 ((0, 1)) = 1
D1 ((0, 1)) = 0
ZTAT ∧ ATDF Z ∧ AT T
CM Z ∧ DF T
N T Z ∧ DF T
DF Z ∧ CM T
AT Z ∧ CM T
CM Z ∧ N T T
NT Z ∧ NT T

We recall that in 2 × 2 DID-IV designs, the units are allowed to take the treatment without
instrument during the two periods. In this setting, one can see that time also plays the role of
instrument, that is, time also affects one’s treatment choices during the two periods.
Similar to the group variable GZi introduced in section 2.1, we define GTi = (0, 0) ≡ N T T to
be the time never-takers, GTi = (1, 1) ≡ AT T to be the time always-takers, GTi = (0, 1) ≡ CM T
to be the time compliers, and GTi = (1, 0) ≡ DF T to be the time defiers. The time nevertakers N T T and the time always-takers AT T do not change their treatment status without
instrument during the two periods. In other words, their treatment choices are time-invariant
in the absence of the policy shock (instrument). On the other hand, the time compliers CM T
are induced to treatment in period 1 without instrument, and the time defiers DF T leave thetreatment in period 1 without instrument, that is, their treatment choices are affected by timein the absence of the policy shock.
By exploiting the group variables GZi and GTi , we can describe how the identifying assumptions in 2 × 2 DID-IV designs restrict the treatment adoption behavior across units in exposed
and unexposed groups, respectively. Table 1 and Table 2 show that we can partition units in
exposed and unexposed groups into six mutually exclusive and exhaustive types under 2 × 2
DID-IV designs. Here, Assumption 3 (monotonicity assumption) excludes the defiers DF Z in
exposed and unexposed groups respectively, the types painted in gray color in both tables.
In an exposed group, we can observe (D0 ((0, 0)), D1 ((0, 1))), but can not observe D1 ((0, 0))for each unit (see Table 1). Here, we use Assumption 4 (no anticipation assumption in thefirst stage), replacing D0 ((0, 1)) with D0 ((0, 0)). In an unexposed group, we can observe(D0 ((0, 0)), D1 ((0, 0))), but can not observe D1 ((0, 1)) for each unit (see Table 2). If, forinstance, the observed treatment choices of unit i in an exposed group are Di,0 ((0, 0)) = 0 and
Di,1 ((0, 1)) = 1, and the counterfactual treatment choice is Di,1 ((0, 0)) = 0, that unit belongs
to the type CM Z ∧ N T T : unit i is induced to the treatment by instrument but not by time.
If the observed treatment choices of unit i in an unexposed group are Di,0 ((0, 0)) = 0 and
Di,1 ((0, 0)) = 1, and the counterfactual treatment choice is Di,1 ((0, 1)) = 1, that unit belongs
to the type AT Z ∧ CM T : unit i is induced to the treatment by time but not by instrument.
12Given these tables, we now consider the interpretation of the parallel trends assumption
in the outcome. Let ∆0 and ∆1 denote the average time trends of the unexposed outcome in
exposed and unexposed groups, respectively:∆0 ≡ E[Yi,1 (Di,1 ((0, 0))) − Yi,0 (Di,0 ((0, 0)))|Ei = 0],∆1 ≡ E[Yi,1 (Di,1 ((0, 0))) − Yi,0 (Di,0 ((0, 0)))|Ei = 1].
We note that the parallel trends assumption in the outcome requires ∆0 = ∆1 . At the sametime, we also note that ∆0 is estimable by the observed change in outcomes in an unexposedgroup during the two periods, whereas ∆1 is fundamentally unobservable because exposed groupis assigned to the instrument path z = (0, 1).
To make the interpretations of ∆0 and ∆1 clear, we introduce the additional notation. For
each time group g t ∈ {AT T , N T T , CM T , DF T }, let wgt ,e ≡ P r[GTi = g t |Ei = e] denote thepopulation share in group Ei = e ∈ {0, 1}. Let ∆gt ,e denote the expectation of the potential
outcome path in the absence of the policy shock for time group g t in group Ei = e:
∆AT T ,e ≡ E[Yi,1 (1) − Yi,0 (1)|AT T , Ei = e],∆N T T ,e ≡ E[Yi,1 (0) − Yi,0 (0)|N T T , Ei = e],∆CM T ,e ≡ E[Yi,1 (1) − Yi,0 (0)|CM T , Ei = e],∆DF T ,e ≡ E[Yi,1 (0) − Yi,0 (1)|DF T , Ei = e].
For instance, wCM T ,0 = P r[CM T |Ei = 0] and ∆CM T ,0 = E[Yi,1 (1) − Yi,0 (0)|CM T , Ei = 0]
represent the population share and the expectation of the outcome path without instrument
for the time compliers in an unexposed group, respectively.
Each wgt ,e and ∆gt ,e are estimable in an unexposed group (e = 0): we can identify thetime group of unit i in an unexposed group and can observe the evolution of the outcome
without instrument. For instance, when the observed treatment choices are Di,0 ((0, 0)) = 0
and Di,1 ((0, 0)) = 1 for unit i in an unexposed group, we can figure out that unit i is thetime compliers CM T , and can observe the potential outcome path (Yi,0 (0), Yi,1 (1)) without
instrument for that unit. On the other hand, each wgt ,e and ∆gt ,e are unobservables in an
exposed group (e = 1) because we can not specify the time group of unit i in that group. For
instance, when the observed treatment choices are Di,0 ((0, 0)) = 0 and Di,1 ((0, 1)) = 1 for unit
i in an exposed group, we can not distinguish whether unit i belongs to the time compliers
CM T or the time never takers N T T (see Table 1).
We can interpret each ∆gt ,e as the indirect effect of time on the outcome through treatment
for time group g t in group Ei = e. First, ∆AT T ,e and ∆N T T ,e only reflect the expectation of thetime effect for treated and untreated potential outcomes respectively:∆AT T ,e = E[Yi,1 (1) − Yi,0 (1)|AT T , Ei = e],{z}|Time effect among AT T

∆N T T ,e = E[Yi,1 (0) − Yi,1 (0)|N T T , Ei = e] .
|{z}Time effect among N T T

This is because the time always-takers AT T and the time never-takers N T T do not change theirtreatment status during the two periods. If the exclusion restriction of time on the outcome
holds, that is, Yi,1 (1) = Yi,0 (1) and Yi,1 (0) = Yi,0 (0) hold for all units i (in other words, thestationary conditions hold), these quantities are equal to zero. Next, ∆CM T ,e and ∆DF T ,e can13be decomposed into two terms:∆CM T ,e = E[Yi,1 (0) − Yi,0 (0)|CM T , Ei = e] + E[Yi,1 (1) − Yi,1 (0)|CM T , Ei = e],|{z}
Selection gain among CM T

∆DF T ,e = E[Yi,1 (1) − Yi,0 (1)|DF T , Ei = e] + E[Yi,1 (0) − Yi,1 (1)|DF T , Ei = e] .
|{z}
Selection gain among DF T

The first terms in ∆CM T ,0 and ∆DF T ,0 represent the expectation of the time effect for untreated
and treated potential outcomes in each time group in group Ei = e, respectively. The second
term represents the selection gain in each time group in group Ei = e, respectively. The latterterms arise because the time compliers CM T and the time defiers DF T are affected by timeand change their treatment status from period 0 to period 1.
The following theorem establishes the relationship between ∆e and ∆gt ,e .
Theorem 2. Suppose Assumptions 1-4 hold, thenX∆e =wgt ,e ∆gt ,e ,gt

where the weight wgt ,e is non-negative and sum to one, that is,P

g t wg t ,e = 1 holds.

Proof. See Appendix A.
Theorem 2 shows that the average time trend of the unexposed outcome in group e is equal
to a weighted average of the indirect effect of time on the outcome through treatment for eachtime group g t in group e. The weight assigned to each ∆gt ,e is natural in that it reflects the
population share in each time group g t in group e. In this paper, we call ∆e an expected time
gain in group e hereafter.
In light of the view discussed so far, we can conclude that the parallel trends assumption
in the outcome (Assumption 6), i.e., ∆0 = ∆1 requires the same expected time gain between
exposed and unexposed groups, that is, the whole indirect effects of time on the outcome
through treatment are the same on average between the two groups.
Assumption 6 is required for DID-IV identification strategy because in the numerator of
the Wald-DID estimand, we should isolate the indirect effect of the instrument on the outcome
through treatment from that of time in an exposed group. The underlying idea to capture
the former effect is parallel to that in DID designs: we purge the latter effect by exploiting
the observed time trend of the outcome in the group that did not receive the policy shock(instrument) in the second period. In practice, if there exist pre-exposed period data, we canindirectly check the validity of Assumption 6 as well as Assumption 5, comparing the evolutionof the outcome between exposed and unexposed groups. The formal discussion for the pretrend
test is provided in section 5.3.
2.5

Relationship between DID and DID-IV

In this section, we describe the relationship between DID and DID-IV designs, and provide theview that DID-IV is DID with the noncompliance of the assigned treatment.
According to section 2.1, we first introduce the notation in DID designs. Let Zi = (Zi,0 , Zi,1 )denote the path of a program, which distributes the treatment Di,t , and let Di = (Di,0 , Di,1 )denote the path of the treatment for unit i. In the canonical DID set up, Zi = (Zi,0 , Zi,1 )takes only two values: Zi = (0, 1) if unit i is assigned to the program in period 1 (treatment
14

Table 3. Exposed group (assigned to z = (0, 1))

observed(D0 ((0, 0)), D1 ((0, 1)))D0 ((0, 0)) = 0, D1 ((0, 1)) = 1

counterfactual
D1 ((0, 0)) = 0
CM Z ∧ N T T

Table 4. Treatment group (assigned to z = (0, 0))observed(D0 ((0, 0)), D1 ((0, 0)))D0 ((0, 0)) = 0, D1 ((0, 0)) = 0

counterfactual
D1 ((0, 1)) = 1
CM Z ∧ N T T

group) and Zi = (0, 0) if unit i is not assigned to the program in period 1 (control group). Let
Ei ∈ {0, 1} denote the group variable: Ei = 1 if unit i belongs to the treatment group andEi = 0 if unit i belongs to the control group. Hereafter, in this section, we refer to treatment
and control groups as exposed and unexposed groups, respectively.
Note that in the common DID set up, the treatment status Di,t is equal to the exposure to
the program Zi,t because we ex ante impose two restrictions on the treatment adoption behavior
across units. First, we assume that all the units are not allowed to receive the treatment inperiod 0:
Di,0 ((0, 1)) = Di,0 ((0, 0)) = 0 for all i.

(1)Second, we assume that unit i should receive the treatment in period 1 if that unit belongs toan exposed group, and should not receive the treatment in period 1 if that unit belongs to an
unexposed group:
1 = Di,1 ((0, 1)) > Di,1 ((0, 0)) = 0 for all i.

(2)

These restrictions imply that we have Tables 3-4 under DID designs: there exists only the type
CM Z ∧ N T T in exposed and unexposed groups, respectively.
Then, under these restrictions, we can show that DID-IV designs nest DID designs asa special case along with three dimensions. First, Assumptions 3-5 in DID-IV designs areautomatically satisfied in DID designs. Assumption 3 follows from (2) and Assumption 4follows from (1). Assumption 6 follows from combining (1) with (2).
Second, the ATT, the target parameter in DID designs, is equal to the LATET in the
canonical DID set up. This follows from Tables 3 - 4:
AT T = E[Yi,1 (1) − Yi,1 (0)|Ei = 1]
= E[Yi,1 (1) − Yi,1 (0)|Ei = 1, CM Z ]= LAT ET.
We note that both ATT and LATET measure the treatment effects, for those who are in an
exposed group (assigned to z = (0, 1)) and are induced to treatment by instrument (CM Z ).
We therefore define the LATET as our target parameter in DID-IV designs in section 2.2.
Finally, a well-known parallel trends assumption in DID designs can also be interpreted as
requiring the same expected time gain between exposed and unexposed groups. From Tables153- 4, we can rewrite the parallel trends assumption in the untreated outcome as follows:
E[Yi,1 (0) − Yi,0 (0)|Ei = 0] = E[Yi,1 (0) − Yi,0 (0)|Ei = 1]⇐⇒ E[Yi,1 (0) − Yi,0 (0)|Ei = 0, N T T ] = E[Yi,1 (0) − Yi,0 (0)|Ei = 1, N T T ]⇐⇒ ∆N T T ,0 = ∆N T T ,1⇐⇒ ∆0 = ∆1 ,where the last equivalence holds because we have only the time never takers N T T in exposed
and unexposed groups respectively under DID designs:
wN T T ,0 = P r(N T T |Ei = e) = 1, for all e = 0, 1.
Overall, this section clarifies that DID-IV is a natural generalization of DID, and the differences between the two designs arise because DID-IV allows the noncompliance of the assigned
treatment: Di,t ̸= Zi,t . In the next section, we compare DID-IV and Fuzzy DID considered inde Chaisemartin and D’Haultfœuille (2018).
2.6

Comparing DID-IV to Fuzzy DID

de Chaisemartin and D’Haultfœuille (2018) (Henceforth, ”dCDH” in this section) also investigate the identification assumptions for the Wald-DID estimand to capture some causal effects
under the same setting in this article. However, they formalize 2 × 2 DID-IV designs differently,
calling them Fuzzy DID designs. In this section, we compare DID-IV to Fuzzy DID and pointout the issues embedded in Fuzzy DID. The detailed discussion is given in Appendix E, andthis section provides the overview of that discussion.
The main difference between dCDH and this article is in the definition of target parameter:
we focus on the LATET, whereas dCDH focus on the SLATET (see section 2.2 in this article).
Accordingly, the identifying assumptions in Fuzzy DID designs are different from those in
2 × 2 DID-IV designs. Furthermore, dCDH argue that the Wald-DID estimand identifies the
SLATET only if the treatment effect is stable over time, and propose the alternative estimands
that do not require the strong restriction on treatment effect heterogeneity.
In Appendix E, we first show that the identifying assumptions in Fuzzy DID designs exante impose the strong restrictions on the treatment adoption behavior across units and theserestrictions are asymmetric between exposed and unexposed groups.
Specifically, we examine how dCDH’s identifying assumptions exclude the types in the twogroups and construct Tables 5-63 , which are in line with Tables 1-2 in this article. From thesetables, one can see that dCDH exclude the defiers DF Z and the type N T Z ∧DF T in an exposedgroup, and the defiers DF Z , the time defiers CM T and the time compliers DF T in an unexposedgroup. Note that in our DID-IV design, we exclude only the defiers DF Z in exposed andunexposed groups by a monotonicity assumption. The difference between dCDH’s restrictions
and ours is critical for empirical application; in contrast to the monotonicity assumption, which
excludes the defiers in both groups, dCDH’s additional restrictions can be difficult to defend
from the institutional knowledge of the problem in a given application. This is because theserestrictions ex-ante exclude the units who change the treatment adoption in the absence of thepolicy shock (instrument).
Next, under Tables 5-6, we show that dCDH’s target parameter, the SLATET, can be
decomposed into a weighted average of two different causal parameters. The one parameter3

Because dCDH consider repeated cross section settings, we can observe either D0 (0) or D1 (1) for each unit
in Tables 5-6.

16

Table 5. Exposed group (z = 1)

observed
D0 (0) or D1 (1)D0 (0) = 1, D1 (1) = 1
D0 (0) = 1, D1 (1) = 0
D0 (0) = 0, D1 (1) = 1
D0 (0) = 0, D1 (1) = 0

counterfactual
D1 (0) = 1
AT Z ∧ AT T
DF Z ∧ AT T
AT Z ∧ CM T
DF Z ∧ CM T

D1 (0) = 0
CM Z ∧ DF T
N T Z ∧ DF T
CM Z ∧ N T T
NT Z ∧ NT T

Table 6. Unexposed group (z = 0)

observed
D0 (0) or D1 (0)D0 (0) = 1, D1 (0) = 1
D0 (0) = 1, D1 (0) = 0
D0 (0) = 0, D1 (0) = 1
D0 (0) = 0, D1 (0) = 0

counterfactual
D1 (1) = 1
AT Z ∧ AT T
CM Z ∧ DF T
AT Z ∧ CM T
CM Z ∧ N T T

D1 (1) = 0
DF Z ∧ AT T
N T Z ∧ DF T
DF Z ∧ CM T
NT Z ∧ NT T

measures the treatment effects among the type CM Z ∧ AT T , who are the sub-population of thecompliers. The other causal parameter measures the treatment effects among the time compliers
CM T . The time compliers are the units who switch from non-treatment to treatment in period
1 in the absence of the policy shock (instrument), that is, they are affected by time but notaffected by the instrument. This decomposition result for the SLATET has two concerning
implications. First, the interpretation of the SLATET is less clear than that of the LATET.
Second, the SLATET may not be policy-relevant even when the instrument is based on thepolicy change of interest to the researcher because this parameter is always contaminated by
the treatment effects among the time compliers.
Finally, we revisit the ”issue” raised by dCDH regarding the use of the Wald-DID estimand,and show that while their argument is correct, it is misguided. During this discussion, we also
clarify why dCDH ex-ante exclude so many types in exposed and unexposed groups for the
Wald-DID estimand to identify the SLATET.
First, we show that dCDH’s argument regarding the use of the Wald-DID estimand is basedon their reliance on the parallel trends assumption in DID designs. Recall that in our DID-IV
design, we do not assume the parallel trends assumption in the untreated outcome, but assume
the parallel trends assumption in the unexposed outcome. Because some units are allowed toadopt the treatment without instrument in DID-IV settings, the former type of parallel trends
assumption is generally not sufficient to capture the average time trend of the outcome in an
unexposed group. We show that this fact leads dCDH to impose the stable treatment effectassumption for the Wald-DID estimand to identify the SLATET. In the proof of our argument,
we also demonstrate that imposing the parallel trends assumption in DID designs yields thestrong restrictions on the treatment adoption behavior across units under Fuzzy DID designs.
Next, after confirming that dCDH’s argument is based on the parallel trends assumption in
DID designs, we argue that this assumption is unsuitable for DID-IV settings for three reasons.
First, as already noted, this assumption is not sufficient to identify the average time trends ofthe outcome even in an unexposed group. Second, in most applications of the DID-IV method,
we can not impute the untreated potential outcomes in general (e.g., Duflo (2001), Black et al.
17(2005)). For instance, in Black et al. (2005), this assumption requires the data to contain theparents with zero education attainment, which is unrealistic in practice. Finally, in most of the
DID-IV settings, we can not test this assumption using pre-exposed period data, as some units
can potentially adopt the treatment before period 0. Indeed, we show that dCDH’s placebo
test is incomplete for assessing the validity of this assumption. Surprisingly, we also show that
their placebo test coincides with our pretrends test with only a slight modification, which wewill introduce in section 5.3 for assessing the plausibility of Assumption 5 and Assumption 6.

3

DID-IV in multiple time periods

We now extend the 2×2 DID-IV design to multiple periods settings with the staggered adoptionof the instrument across units. In reality, many studies exploit variation in the timing of policy
adoption across units as an instrument for treatment in more than two periods (e.g. Blacket al. (2005), Bhuller et al. (2013), Lundborg et al. (2014), and Meghir et al. (2018)). We referto the underlying identification strategy as a staggered DID-IV design, and establish the target
parameter and identifying assumptions.
3.1

Set up

We introduce the notation we use throughout section 3 to section 5. We consider a panel
data setting with T periods and N units. For each i ∈ {1, . . . N } and t ∈ {1, . . . , T }, let Yi,tdenote the outcome and Di,t ∈ {0, 1} denote the treatment status, and Zi,t ∈ {0, 1} denote theinstrument status. Let Di = (Di,1 , . . . , Di,T ) and Zi = (Zi,1 , . . . , Zi,T ) denote the path of thetreatment and the instrument for unit i. Throughout section 3 to section 5, we assume that
{Yi,t , Di,t , Zi,t }Tt=1 are independent and identically distributed (i.i.d).
We make the following assumption about the assignment process of the instrument.
Assumption 7 (Staggered adoption for Zi,t ). For s < t, Zi,s ≤ Zi,t where s, t ∈ {1, . . . T }.
Assumption 7 requires that once units start exposed to the instrument, units remain exposedto that instrument afterward. In the DID literature, several papers make the similar assumption
for the adoption process of the treatment and call it the ”staggered treatment adoption”; see,e.g., Athey and Imbens (2022), Callaway and Sant’Anna (2021) and Sun and Abraham (2021).
Given Assumption 7, we can uniquely characterize one’s instrument path by the initial
exposure date of the instrument, which we denote Ei = min{t : Zi,t = 1}. If unit i is not
exposed to the instrument for all time periods, we define Ei = ∞. Based on the initial exposure
period Ei , we can uniquely partition units into mutually exclusive and exhaustive cohorts e fore ∈ {1, 2, . . . , T, ∞}: all the units in cohort e start exposed to the instrument in period Ei = e.
Similar to the two periods setting in section 2.1, we allow the general adoption process forthe treatment: the treatment can potentially turn on/off repeatedly over time. de Chaisemartin
and D’Haultfœuille (2020) and Imai and Kim (2021) consider the same setting in the recent
DID literature.
Next, we introduce the potential outcomes framework in multiple time periods. Let Yi,t (d, z)
denote the potential outcome in period t when unit i receives the treatment path d ∈ S(D)and the instrument path z ∈ S(Z). Similarly, let Di,t (z) denote the potential treatment status
in period t when unit i receives the instrument path z ∈ S(Z).
eAssumption 7 allows us to rewrite Di,t (z) by the initial exposure date Ei = e. Let Di,tdenote the potential treatment status in period t if unit i is first exposed to the instrument in∞period e. Let Di,tdenote the potential treatment status in period t if unit i is never exposed18

∞the ”never exposed treatment”. Since the adoption
to the instrument. Hereafter, we call Di,tdate of the instrument uniquely pins down one’s instrument path, we can write the observed
treatment status Di,t for unit i in period t as
X∞e∞Di,t = Di,t+(Di,t− Di,t) · 1{Ei = e}.
1≤e≤T∞
to be the effect of an instrument on treatment for unit i in period
We define Di,t − Di,tt, which is the difference between the observed treatment status Di,t to the never exposed∞∞
treatment status Di,t
. Hereafter, we refer to Di,t − Di,t
as the individual exposed effect in
the first stage. In the DID literature, Callaway and Sant’Anna (2021) and Sun and Abraham(2021) define the effect of a treatment on an outcome in the same fashion.
Next, we introduce the group variable which describes the type of unit i in period t, basedon the reaction of potential treatment choices in period t to the instrument path z. Lete∞) (t ≥ e) be the group variable in period t for unit i and the initial exposure, Di,tGi,e,t ≡ (Di,t∞date e. Specifically, the first element Di,trepresents the treatment status in period t if unite
i is never exposed to the instrument Ei = ∞ and the second element Di,trepresents thetreatment status in period t if unit i is first exposed to the instrument at Ei = e. Following
to the terminology in section 2.1, we define Gi,e,t = (0, 0) ≡ N Te,t to be the never-takers,
Gi,e,t = (1, 1) ≡ ATe,t to be the always-takers, Gi,e,t = (0, 1) ≡ CMe,t to be the compliers andGi,e,t = (1, 0) ≡ DFe,t to be the defiers in period t and the initial exposure date e.
Finally, we make a no carryover assumption on potential outcomes Yi,t (d, z).

Assumption 8 (No carryover assumption).
∀z ∈ S(Z), ∀d ∈ S(D), ∀t ∈ {1, . . . , T }, Yi,t (d, z) = Yi,t (dt , z).
Henceforth, we keep Assumption 7 and 8. In the next section, we define the target parameterin staggered DID-IV designs.
3.2

Target parameter in staggered DID-IV designs

In staggered DID-IV designs, our target parameter is the cohort specific local average treatment
effect on the treated (CLATT) defined below.
Definition. The cohort specific local average treatment effect on the treated (CLATT) at agiven relative period l from the initial adoption of the instrument ise∞]
CLAT Te,e+l = E[Yi,e+l (1) − Yi,e+l (0)|Ei = e, Di,e+l> Di,e+l= E[Yi,e+l (1) − Yi,e+l (0)|Ei = e, CMe,e+l ].
Each CLATT is a natural generalization of the LATET in section 2.2 and suitable for thesetting of the staggered instrument adoption. This parameter measures the treatment effects at
a given relative period l from the initial exposure date Ei = e, for those who belong to cohort e,and are the compliers CMe,e+l , that is, who are induced to treatment by instrument in period
e + l. Each CLATT can potentially vary across cohorts and over time because it depends oncohort e, relative period l and the compliers CMe,e+l . We note that the composition of thecompliers can overlap over the post-exposure periods in cohort e. For instance, some units incohort e may belong to CMe,e+l for all the relative periods (l ≥ e): they are affected by the
instrument for all post-exposure periods.
19This parameter would be policy-relevant if researchers leverage the policy change of theirinterest as an instrument for the treatment. Suppose for instance that the treatment represents participation in a job training program, the outcome represents real earnings, and the
instrument represents a policy shock that encourages people to receive the treatment. In thisexample, if the instrument is an important policy lever for the researchers (e.g., nudge), each
CLATT is of particular interest because the compliers in each relative period after a policychange represents the dynamic effect of that policy on the take up rates of the program, andthis parameter can be interpreted as estimating the effect of participation in job training onreal earnings among those affected by the policy shock in each relative period.
3.3

Identification assumptions in staggered DID-IV designs

In this section, we establish the identification assumptions in staggered DID-IV designs. Theseassumptions are the natural generalization of Assumptions 1-6 in 2 × 2 DID-IV designs.
Assumption 9 (Exclusion Restriction in multiple time periods).
∀z ∈ S(Z), ∀d ∈ S(D), ∀t ∈ {1, . . . , T }, Yi,t (d, z) = Yi,t (d) a.s.
Assumption 9 extends the exclusion restriction in two time periods (Assumption 2) tomultiple period settings. This assumption requires that the instrument path does not directly
affect the potential outcome for all time periods and its effects are only through treatment.
Given Assumption 8 and Assumption 9, we can write the potential outcome Yi,t (d, z) as
Yi,t (dt ) = Di,t Yi,t (1) + (1 − Di,t )Yi,t (0). Following to section 2.3, we introduce the potential
outcomes in period t if unit i is assigned to the instrument path z ∈ S(Z):Yi,t (Di,t (z)) ≡ Di,t (z)Yi,t (1) + (1 − Di,t (z))Yi,t (0).
Since the initial exposure date Ei completely characterizes the instrument path, we can writee∞the potential outcomes for cohort e and cohort ∞ as Yi,t (Di,t) and Yi,t (Di,t) respectively. Theepotential outcome Yi,t (Di,t ) represents the outcome status in period t if unit i is first exposed to∞the instrument in period e and the potential outcome Yi,t (Di,t) represents the outcome status∞) as thein period t if unit i is never exposed to the instrument. Hereafter, we refer to Yi,t (Di,t”never exposed outcome”.
Assumption 10 (Monotonicity Assumption in multiple time periods).
∞e∞e
P r(Di,e+l≥ Di,e+l) = 1 or P r(Di,e+l≤ Di,e+l) = 1 for all e ∈ S(Ei ) and for all l ≥ 0.

This assumption requires that the instrument path affects the treatment adoption behavior
in a monotone way for all relative periods after the initial exposure date Ei = e. We recall∞
that we define Di,t − Di,t
to be the effect of an instrument on treatment for unit i in periodt. Assumption 10 requires that the individual exposed effect in the first stage should be nonnegative (or non-positive) during the periods after the initial exposure to the instrument for all∞ei. This assumption implies that the group variable Gi,e,t ≡ (Di,t, Di,t) can take three values with
non-zero probability for all e and all t ≥ e. Hereafter, we consider the type of the monotonicity
assumption that rules out the existence of the defiers DFe,t for all t ≥ e in any cohort e.
Assumption 11 (No anticipation in the first stage).
e∞Di,e+l= Di,e+la.s. for all i, for all e ∈ S(Ei ) and for all l < 0.

20

Assumption 11 requires that potential treatment choices in any l period before the initial
exposure to the instrument is equal to the never exposed treatment. This assumption is anatural generalization of Assumption 4 to multiple period settings and restricts the anticipatory
behavior before the initial exposure to the instrument.
Assumption 12 (Parallel Trends Assumption in the treatment in multiple time periods).
∞∞
For all s < t, E[Di,t− Di,s|Ei = e] is same for all e ∈ S(Ei ).

Assumption 12 is a parallel trends assumption in the treatment in multiple periods andmultiple cohorts. This assumption requires that the trends of the treatment across cohorts
would have followed the same path, on average, if there is no exposure to the instrument.
Assumption 12 is analogous to that of Callaway and Sant’Anna (2021) and Sun and Abraham(2021) in DID designs: these studies impose the same type of parallel trends assumption on
untreated outcomes with settings of multiple periods and multiple cohorts.
Assumption 13 (Parallel Trends Assumption in the outcome in multiple time periods).
∞∞
For all s < t, E[Yi,t (Di,t) − Yi,s (Di,s)|Ei = e] is same for all e ∈ S(Ei ).

Assumption 13 is a parallel trends assumption in the outcome with settings of multiple
periods and multiple cohorts. This assumption requires that the expectation of the never
exposed outcome across cohorts would have followed the same evolution if the assignment of
the instrument had not occurred. From the discussion in section 2.4, we can interpret that thisassumption requires the same expected time gain across cohorts and over time: the effects oftime on the outcome through treatment are the same on average across cohorts and over time.

4

Extensions

This section contains extensions to non-binary, ordered treatments, triple DID-IV designs, andrepeated cross sections. It also includes the case when we introduce the treatment path inpotential outcomes in 2 × 2 DID-IV designs. For more details and the proofs in this section,
see Appendix B.
Non-binary, ordered treatment
Up to now, we have considered only the case of a binary treatment. However the same idea
can be applied when treatment takes a finite number of ordered values, that is, we have Di,t ∈{0, 1, . . . , J}. When we have only two periods and treatment is non-binary, our target parameteris the average causal response on the treated (ACRT) defined below.
Definition. The average causal response on the treated (ACRT) is
ACRT ≡

JX

wj · E[Y1 (j) − Y1 (j − 1)|Di,1 ((0, 1)) ≥ j > Di,1 ((0, 0)), Ei = 1].

j=1where the weight wj is:
P r(D1 ((0, 1)) ≥ j > D1 ((0, 0))|Ei = 1).
wj = PJ
j=1 P r(D1 ((0, 1)) ≥ j > D1 ((0, 0))|Ei = 1)
21

The average causal response on the treated (ACRT) is a weighted average of the effects of aunit increase in the treatment on the outcome, for those who belong to an exposed group andare induced to increase the treatment in period t = 1 by instrument. The ACRT is similar to theaverage causal response (ACR) considered in Angrist and Imbens (1995), but the difference hereis that each weight wj and the associated causal parameter in this parameter are conditional
on Ei = 1.
Theorem 3 below shows that if we have a non-binary, ordered treatment, the Wald-DID
estimand is equal to the average causal response on the treated (ACRT) under the same assumptions in Theorem 1.
Theorem 3. If Assumptions 1-6 hold, the Wald-DID estimand WDID is equal to the ACRT.
WDID =

JX

wj · E[Y1 (j) − Y1 (j − 1)|Di,1 ((0, 1)) ≥ j > Di,1 ((0, 0)), Ei = 1]

j=1

= ACRT.
Proof. See Appendix B.1.
If we have a non-binary, ordered treatment in staggered DID-IV designs, our target parameter is the cohort specific average causal response on the treated (CACRT), which is the naturalgeneralization of the ACRT. The identifying assumptions are the same in section 3.3.
Definition. The cohort specific average causal response on the treated (CACRT) at a given
relative period l from the initial adoption of the instrument is
CACRTe,e+l ≡

J
X

e
e
∞
we+l,j· E[Yi,e+l (j) − Yi,e+l (j − 1)|Ei = e, Di,e+l≥ j > Di,e+l]

j=1ewhere the weight we+l,jis:e∞
P r(Di,e+l≥ j > Di,e+l|Ei = e)e.
we+l,j
= PJ
e
∞
P
r(D
≥
j
>
D
|E
=
e)
i
i,e+l
i,e+l
j=1

Triple DID-IV designs
As we have seen in section 2 and 3, our DID-IV designs mainly rely on the parallel trends
assumption in the treatment and the outcome. In practice, if the data contain three different
dimensions (e.g., cohort e, time t, and demographic group g), one can instead use the triple
DID identification strategy to estimate the effects of the instrument on the treatment and theoutcome, which we call a triple DID-IV design. In this design, one can replace Assumption 5 and
6 (Assumption 12 and 13 in multiple time periods) with common acceleration assumptions in
the treatment and the outcome (Olden and Møen (2022), Fröhlich et al. (2019), and Wooldridge(2020)).4
Repeated cross sections
In some applications, researchers have no access to panel data and use repeated cross section
data5 . In Appendix B.2, we consider repeated cross section data settings and present the4

As an empirical example, Deschênes et al. (2017) implicitly use triple DID-IV designs to estimate the effects
of NOx (Nitrogen Oxides) emissions on medication purchases and mortality rates, exploiting the NOx Budget
Trading program as an instrument for NOx emissions.
5
It also includes the case that researchers use the cross section data, and exploit a policy shock acrosscohorts as an instrument for the treatment as in Duflo (2001).

22

identification assumptions in DID-IV designs.
Introducing the treatment path in 2 × 2 DID-IV designs
In section 2.1, we impose Assumption 1 (No carryover assumption) on potential outcomes
Yi,t (d, z) as we consider the non-staggered adoption of the treatment. We can extend our
results to the case where we introduce the treatment path in potential outcomes with binary
treatment. In this case, our target parameter slightly changes with the cumbersome notation,formally defined below.
Definition. The local average treatment effect on the treated with the treatment path (LATET’)is
LAT ET ′ ≡ w0 · ∆0 + w1 · ∆1
where ∆0 and ∆1 are:∆0 ≡ E[Y1 ((1, 1)) − Y1 ((1, 0))|Ei = 1, (CM Z ∧ DF T )],∆1 ≡ E[Y1 ((0, 1)) − Y1 ((0, 0))|Ei = 1, (CM Z ∧ N T T )].
The weights w0 and w1 are:w0 =P r((CM Z ∧ DF T )|Ei = 1)
, w1 = 1 − w0 .
P r((CM Z ∧ DF T )|Ei = 1) + P r((CM Z ∧ N T T )|Ei = 1)

In Appendix B.3, we show that the similar assumptions as in Assumptions 1-6 in section
2.3 are sufficient for the Wald-DID to capture the LATET’.

5

Estimation and Inference

When researchers leverage variation in the timing of policy adoption across units as an instrument for treatment and implicitly rely on a staggered DID-IV design, they usually implement
this design via TWFEIV regressions (e.g., Johnson and Jackson (2019), Lundborg et al. (2014),
Black et al. (2005), Akerman et al. (2015), and Bhuller et al. (2013)).
In companion paper (Miyaji (2024)), however, we show that in more than two periods,
the TWFEIV estimand potentially fails to summarize the treatment effects under staggered
DID-IV designs in the presence of heterogeneous treatment effects. Specifically, Miyaji (2024)shows that under staggered DID-IV designs, the TWFEIV estimand is a weighted average ofall possible CLATTs, but some weights can be negative if the effect of the instrument on thetreatment or the outcome is not stable over time.6
In this section, we propose an alternative estimation method in staggered DID-IV designs
that is robust to treatment effect heterogeneity. First, we propose a simple regression-based
method for estimating each CLATT. Following to Callaway and Sant’Anna (2021), we thenpropose a weighting scheme to construct the summary causal parameters from each CLATT.
At the end of this section, we also discuss the pretrends tests for checking the plausibility ofparallel trends assumption in the treatment and the outcome in DID-IV designs.

6

See also the discussions in de Chaisemartin and D’Haultfœuille (2020), who decompose the numerator anddenominator in the TWFEIV estimand separately, and point out the issue of interpreting this estimand causally.

23

5.1

Stacked two stage least squares regression

In this section, we propose a regression-based method to consistently estimate our target parameter in staggered DID-IV designs. Recall that if we have a binary treatment, our target
parameter is the CLAT Te,e+l for each cohort e and a relative period l ≥ 0:
CLAT Te,e+l = E[Yi,e+l (1) − Yi,e+l (0)|Ei = e, CMe,e+l ].
Our estimation method consists of two steps.
Step 1.
We create the data sets for each CLAT Te,e+l . Each data set includes the units of timet = e − 1 and t = e + l, who are either in cohort e ∈ {2, . . . , T } or in the set of some unexposedcohorts, U (e ∈/ U ).
Researchers should carefully specify the choice set U in practice. If there exists a never
exposed cohort Ei = ∞, we can set U = {∞} and estimate CLAT Te,e+l for all cohorts (e ∈{2, . . . , T }) and all relative time periods (l ≥ 0). If there exists no never exposed cohort, we
can set U = max{Ei }, i.e., the last exposed cohort. In this case, we can estimate CLAT Te,e+l
for cohort e ∈ {2, . . . , max{Ei } − 1} and relative time period l ∈ {0, . . . , max{Ei } − 1 − e}because every unit will be exposed to the instrument after time t = max{Ei }. We note that theunits in an already exposed cohort e = 1 are not included in any data sets because we should
include the pre-exposed period e − 1 for estimating each CLAT Te,e+l .
Step 2.
e,lIn each data set, we run the following IV regression and obtain the IV estimator β̂IV
:
e,l
e,l
e,l
Yi,t = β0e,l + βi,.
1{Ei = e} + β,.t1{Ti = e + l} + βIVDi,t + ϵe,li,t .

The first stage regression is:
e,l
e,l
e,l
Di,t = π0e,l + πi,.
1{Ei = e} + π,.t1{Ti = e + l} + π e,l (1{Ei = e} · 1{Ti = e + l}) + ηi,t,

where the group indicator 1{Ei = e} and the post-period indicator 1{Ti = e + l} are theincluded instruments and the interaction of the two is the excluded instrument.
e,l\T e,e+l ≡ β̂IV
Formally, our proposed estimator CLAT
takes the following form:
e,l

α̂
e,l
\T e,e+l ≡ β̂IV= e,l ,
CLATπ̂where α̂e,l and π̂ e,l are:EN [(Yi,e+l − Yi,e−1 ) · 1{Ei = e}] EN [(Yi,e+l − Yi,e−1 ) · 1{Ei ∈ U }]−EN [1{Ei = e}]
EN [1{Ei ∈ U }]21
≡ α̂e,l − α̂e,l .
EN [(Di,e+l − Di,e−1 ) · 1{Ei = e}] EN [(Di,e+l − Di,e−1 ) · 1{Ei ∈ U }]π̂ e,l =−EN [1{Ei = e}]
EN [1{Ei ∈ U }]12
≡ π̂e,l − π̂e,l .

α̂e,l =

Here, EN [·] is the sample analog of the conditional expectation. We note that the IV estimator\T e,e+l is the Wald-DID estimator for each CLAT Te,e+l , where the choice set U is an
CLAT24

unexposed group and time t = e − 1 is a pre-exposed period. From the estimation procedure
above, we call this a stacked two-stage least squares (STS) estimator.
Our STS estimator is related to the DID estimators in staggered DID designs recently
proposed by Callaway and Sant’Anna (2021) and Sun and Abraham (2021). Specifically, theDID estimator of the treatment and the outcome in our STS estimator corresponds to thatof Sun and Abraham (2021), and coincides with that of Callaway and Sant’Anna (2021) forthe case when we have no covariates and use never treated units as a control group. Their
proposed methods avoid the issue of two-way fixed effects estimators in staggered DID designs,
and our STS estimator avoids the issue of two-way fixed effects instrumental variable estimators
in staggered DID-IV designs.
Theorem 4 below guarantees the validity of our STS estimator.
\T e,e+l is conTheorem 4. Suppose Assumptions 7-13 hold. Then, the STS estimator CLAT
sistent and asymptotically normal:√d\T e,e+l − CLAT Te,e+l ) →n(CLAT− N (0, V (ψi,e,l )).

\T e,e+l and defined in Equation (25) in Appendix C.
where ψi,e,l is influence function for CLAT
Proof. See Appendix C.
From Theorem 4, we can also construct the standard error of the STS estimator, using thesample analogue of the asymptotic variance V (ψi,e,l ).
Remark 2. Our estimation procedure is identical if we have a non-binary, ordered treatment
or use repeated cross section data. In Appendix C, we present the influence function of our
SLS estimator in repeated cross section settings.
In triple DID-IV designs, one can replace the IV regression in step 2 with the following one(gi = A, B):
Yi,t = β0e,l + β1e,l 1Ei =e + β2e,l 1Ti =e+l + β3e,l 1gi =A + β4e,l 1Ei =e,Ti =e+l + β5e,l 1Ei =e,gi =A + β6e,l 1Ti =e+l,gi =A
e,l
+ βIV
Di,t + ϵe,li,t .

The first stage regression is:
Di,t = π0e,l + π1e,l 1Ei =e + π2e,l 1Ti =e+l + π3e,l 1gi =A + π4e,l 1Ei =e,Ti =e+l + π5e,l 1Ei =e,gi =A + π6e,l 1Ti =e+l,gi =Ae,l+ π7e,l 1Ei =e,Ti =e+l,gi =A + ηi,t,

where 1A is the indicator function and takes one if A is true. In Appendix C, we also present
e,lthe influence function of our triple DID-IV estimator βIV.
5.2

Weighting scheme

The previous section provides the method to estimate each CLAT Te,e+l in staggered DIDIV designs. In some applications, each CLAT Te,e+l is of intrinsic interest if researchers areinterested in the treatment effect heterogeneity across cohort e and relative period l. However, inmany cases, researchers may also want to estimate summary causal parameters, which capture
the overall effect of a treatment on an outcome. Actually, in staggered DID-IV designs, each
CLAT Te,e+l depends not only on cohort e, relative period l, but also on the compliers CMe,e+l .
In this case, each CLAT Te,e+l may be difficult to interpret when the number of cohorts and the25relative period are fairly large, and when the members of compliers CMe,e+l in cohort e varyand overlap over time.
In this section, we explain how one can construct the summary causal parameters from each
CLATT in staggered DID-IV designs, based on the weighting scheme proposed by Callaway
and Sant’Anna (2021).
Specifically, we consider the following weighting scheme as in Callaway and Sant’Anna(2021):
θ

IV

=

T
XX
e

w(e, t) · CLAT Te,t ,t=1

where w(e, t) are some reasonable weighting functions assigned to each CLAT Te,t .
To propose the weighting functions for a variety of summary causal parameters in staggered
DID-IV designs, we first define the average effect of the instrument on the treatment at a given
relative period l from the initial exposure to the instrument in cohort e. We call this the cohort
1
specific average exposed effect on the treated in the first stage (CAETe,e+l), formally defined
below.
1
Definition. The cohort specific average exposed effect on the treated in the first stage (CAETe,e+l)
at a given relative period l from the initial adoption of the instrument is
1∞
CAETe,e+l= E[Di,e+l − Di,e+l|Ei = e].
1
If treatment is binary, each CET Te,lis equal to the share of the compliers in cohort e inperiod e + l:
1e∞
CAETe,e+l= E[Di,e+l− Di,e+l|Ei = e]= P r(CMe,e+l |Ei = e).
In staggered DID designs, Callaway and Sant’Anna (2021) propose various aggregated measures along with different dimensions of treatment effect heterogeneity. We can employ theirframework straightforwardly, but in staggered DID-IV designs, we should more carefully specify
the weighting functions assigned to each summary measure.
For instance, to aggregate dynamic treatment effects in cohort e over time in staggered DID
designs, Callaway and Sant’Anna (2021) consider the following summary measure:
T
X
1
CAT T (ẽ, t),θsel (ẽ) =T − ẽ + 1 t=ẽ

where the CAT T (ẽ, t) is the cohort specific average treatment effect on the treated at time t incohort ẽ (see, e.g., Callaway and Sant’Anna (2021), Sun and Abraham (2021)). Callaway andSant’Anna (2021) construct the summary measure θsel (ẽ) by equally weighting each CAT T (ẽ, t)across all post-treatment periods because all the units in cohort e adopt the treatment after
they start exposed to that treatment.
In staggered DID-IV designs, we propose the following summary measure θsel (ẽ)IV that
corresponds with θsel (ẽ):θsel (ẽ)IV =TX

1CAETẽ,t

PT
t=ẽ

1
t=ẽ CAETẽ,t26

CLAT Tẽ,t ,Table 7. Weights for a variety of summary causal parameters
Target ParameterIVθes(l)
bal,IVθes(l,l′)IVθsel(ẽ)IV
θc(t̃)
cumm,IV
θc(
t̃)
o,IV
θW

w(e, t)1
CAETe,e+l1e∈S(E) CAETe,e+l
1
CAETe,e+l1{e + l′ ≤ T }1{t = e + l}P (E = e|E + l′ ≤ T ) P
1e∈S(E) CAETe,e+l
1
CAETẽ,t1{t ≥ e}1{e = ẽ} PT1t=ẽ CAETẽ,t1
CAETe,t1{t ≥ e}1{t = t̃}P (E = e|E ≤ t) P
1e∈S(E) CAETe,t
1
CAETe,t1{t ≥ e}1{t ≤ t̃}P (E = e|E ≤ t) P
1e∈S(E) CAETe,tP
PT
1{t ≥ e}P (E = e|E ≤ T )/ e∈S(E) t=1 1{t ≥ e}P (E = e|E ≤ T )1{e + l ≤ T }1{t = e + l}P (E = e|E + l ≤ T ) P

1
CAETe,t1{t ≥ e}P (E = e|E ≤ T ) PT
1
t=e CAETe,tNotes: This table represents the specific expressions for the weights on each CLAT T (e, t)or each CACRT (e, t) in a variety of summary causal parameters. Each target parametercorresponds with that of Callaway and Sant’Anna (2021). We superscript IV to associateeach parameter with staggered DID-IV designs.
o,IV
θsel

where the weights are non-negative and sum to one by construction. This parameter summarizes
each CLAT Tẽ,t in cohort ẽ across all post-exposed periods and the weight assigned to each
CLAT Tẽ,t reflects the relative share of the compliers CMẽ,t in period t during the periods after
the initial exposure to the instrument in cohort ẽ. This weighting scheme would be reasonable
in that it is designed to be larger at the period when the proportion of the compliers is relatively
higher in cohort ẽ.
By similar arguments, we can specify the weighting functions for various summary measuresin staggered DID-IV designs, which correspond with those in Callaway and Sant’Anna (2021).
In Table 7, we summarize the specific expressions for the weights assigned to each CLAT Tẽ,tin each summary causal parameter. Here, we define each causal parameter by the notation
analogous to that of Callaway and Sant’Anna (2021) and superscript IV to associate eachparameter with staggered DID-IV designs. Note that our proposed weighting functions are
the same under non-binary, ordered treatment settings, in which our target parameter is the
CACRTẽ,t .
Estimation and Inference
We can construct the consistent estimator for the summary causal parameter θIV as follows:
θ̂

IV

=

T
XX
e

\T e,t ,ŵ(e, t) · CLAT

t=1

\T e,t is the consistent estimator
where ŵ(e, t) is the sample analog of each w(e, t) and CLAT
for each CLAT Te,t , obtained from the stacked IV regression in section 5.1. Each ŵ(e, t) is theregular asymptotically linear estimator:
n

1 X w
√
ζ + op (1),n i=1 i,e,t
27

w ⊤
w
w
w
ζi,e,t] < ∞.
] = 0 and E[ζi,e,t
represents the influence function, and satisfies E[ζi,e,t
where ζi,e,tCorollary 1 below represents the asymptotic distribution of the plug-in estimator θ̂IV andensures its validity.

Corollary 1. If the assumptions of Theorem 4 hold,√dn(θ̂IV − θIV ) →− N (0, V (liθIV )),where the influence function liθIV takes the following form:liθIV =

T
XX
e

5.3


w
w(e, t) · ψi,e,t + ζi,e,t· CLAT T e,t .

t=1

Pretrend test

In this section, we describe how one can conduct pretrend tests to check the validity of theparallel trends assumption in the outcome and the treatment.
Suppose that data are available for period t = −1. Then, one can assess the plausibility ofAssumption 5 between period t = −1 and t = 0 by testing the following null hypothesis
E[Di,0 − Di,−1 |Ei = 0] = E[Di,0 − Di,−1 |Ei = 1]⇐⇒ E[Di,0 ((0, 0)) − Di,−1 ((0, 0))|Ei = 0] = E[Di,0 ((0, 0)) − Di,−1 ((0, 0))|Ei = 1].

(3)

Similarly, one can assess the plausibility of Assumption 6 between period t = −1 and t = 0 by
testing the following null hypothesis
E[Yi,0 − Yi,−1 |Ei = 0] = E[Yi,0 − Yi,−1 |Ei = 1]⇐⇒ E[Yi,0 (Di,0 ((0, 0))) − Yi,−1 (Di,−1 ((0, 0)))|Ei = 0] = E[Yi,0 (Di,0 ((0, 0))) − Yi,−1 (Di,−1 ((0, 0)))|Ei = 1].
(4)
We can generalize these tests to multiple pre-exposed periods settings by using the pretrends
tests recently developed in the context of DID designs (Callaway and Sant’Anna (2021), Sun
and Abraham (2021), Borusyak et al. (2021)); we can apply these tools to the first stage andthe reduced form respectively to confirm the plausibility of Assumption 12 and 13.
Remark 3. When researchers implement the staggered DID-IV design via TWFEIV regressions, they often use the dynamic specifications in the first stage and the reduced form:
X
Yi,t = µi. + δt. +αl 1{t − Ei = l} + ϵi,t ,(5)l

Di,t = γi. + ζt. +X

βl 1{t − Ei = l} + ηi,t ,(6)lwhere Ei represents the initial exposure date. They plot the coefficients αl in equation (5) andβl in equation (6) in each relative period l, and test whether the coefficients before the initial
exposure to the instrument are significantly different from zero or not (e.g., Akerman et al.
(2015) and Bhuller et al. (2013)).
However, such tests are problematic if the effects of the instrument on the treatment andoutcome are heterogeneous. Sun and Abraham (2021) shows that in staggered DID designs,
the coefficient for pre-treatment periods on event study regressions can be different from zero28

even when the no anticipation assumption and the parallel trends assumption in the untreatedoutcome are plausible. Because we can view that Yi,t and Di,t are the outcomes and Zi,t isthe binary absorbing treatment in equations (5)-(6), it is inappropriate to check whether thecoefficients of pre-exposed periods are statistically different from zero or not as a way of testing
Assumption 12 and Assumption 13.

6

Application

Oreopoulos (2006) estimates returns to schooling using a major education reform in the United
Kingdom that increased the years of compulsory schooling from 14 to 15. Specifically, Oreopoulos (2006) exploit variation resulting from the different timing of implementation of school
reforms between Britain (England, Scotland, and Wales) and Northern Ireland as an instrument
for education attainment: the school-leaving age increased in Britain in 1947, while the reform
was not implemented until 1957 in Northern Ireland. The data are a sample of individuals in
Britain and Northern Ireland, who were aged 14 between 1936 and 1965, constructed from combining the series of U.K. General Household Surveys between 1984 and 2006; see Oreopoulos(2006), Oreopoulos (2008) for details.
In the first part of their analysis, Oreopoulos (2006) adopts regression discontinuity designs(RDD) and analyzes the data sets in Britain and Northern Ireland separately. Due to the imprecision of their standard errors7 , Oreopoulos (2006) then moves to ”a difference-in-differences
and instrumental-variables analysis by combining the two sets of U.K. data”.
Specifically, Oreopoulos (2006) (more precisely, Oreopoulos (2008)) runs the following twoway fixed effects instrumental variable regression with the education reform as an excluded
instrument for education attainment:
Yi,t = µn. + δ.t + βIV Di,t + ϵi,t ,Di,t = γn. + ζ.t + πZi,t + ηi,t .

(7)
(8)

Here, a cohort (a year when aged 14) plays a role of time as it determines the exposure to thepolicy change. The dependent variables Yi,t and Di,t are log annual earnings and education
attainment for unit i and cohort t, respectively. Both the first stage and the reduced form
regressions include a birth cohort fixed effect and a North Ireland fixed effect. The binary
instrument Zi,t ∈ {0, 1} takes one if unit i in cohort t is exposed to the policy change.
The staggered introduction of the school reform can be viewed as a natural experiment,
but is not randomized across regions in reality; Oreopoulos (2006) notes that the reform was
implemented with political support, taking into account the cost and benefit. This indicatesthat Oreopoulos (2006) implicitly relies on a staggered DID-IV identification strategy insteadof the IV design. Indeed, Oreopoulos (2006) presents the corresponding plots of British andNorthern Irish average education attainment and average log earnings by cohort to illustrate
the evolution of these variables before and after the policy shock.
In the author’s setting, however, the effect of the school reform on education attainment andlog annual earnings can differ between Britain and North Ireland, and potentially vary acrosscohorts. The author is also clearly conscious of the heterogeneous treatment effects: the titleof this paper is ”Estimating Average and Local Average Treatment Effects of Education when
Compulsory Schooling Laws Really Matter”. The TWFEIV estimator, therefore, can potentially fail to aggregate the treatment effects, yielding a misleading conclusion under staggered
DID-IV designs.
7

Kolesár and Rothe (2018) consider inference in regression discontinuity designs with a discrete runningvariable and apply their theory to Oreopoulos (2006).

29

In this section, we first assess the identifying assumptions in staggered DID-IV designs
implicitly imposed by Oreopoulos (2006). We then estimate the TWFEIV regression in theauthor’s setting. Finally, we estimate the target parameter and its summary measure by employing our proposed method and weighting scheme.
6.1

Assessing the identifying assumptions in staggered DID-IV designs

We first discuss the validity of the staggered DID-IV identification strategy in Oreopoulos(2006). In the author’s setting, our target parameter is the cohort specific average causal
response on the treated (CACRT), as education attainment is a non-binary, ordered treatment.
We can identify each CACRT and its summary measure if the underlying DID-IV identifying
assumptions seem plausible.
Exclusion restriction. It would be plausible, given that the policy reform did not affectlog annual earnings other than by increasing education attainment. This assumption may beviolated for instance if the reform affected both the quality and quantity of education.
Monotonicity assumption. It would be automatically satisfied in the author’s setting:the policy change (instrument) increased the minimum schooling-leaving age from 14 to 15,
which ensures that there are no defiers during the periods after the policy shock.
No anticipation in the first stage. It would be plausible that there is no anticipation, if the treatment adoption behavior is the same as the one in the absence of the policychange before its implementation in England. This assumption may be violated if units haveprivate knowledge about the probability of extended education and manipulate their education
attainment before the policy shock.
Next, we assess the validity of the parallel trends assumptions in the treatment and theoutcome. To do so, we use the interacted two-way fixed effects regressions proposed by Sun
and Abraham (2021) in the first stage and the reduced form, respectively. The results areshown in Figure 2.
Parallel trends assumption in the treatment. It requires that the expectation of
education attainment would have followed the same path between England and North Irelandacross cohorts in the absence of the school reform. Panel (a) in Figure 2 plots the results of
the interacted two-way fixed effects regression in the first stage along with a 95% pointwise
confidence interval. The pre-exposed estimates are not significantly different from zero andindicate the validity of Assumption 12.
Parallel trends assumption in the outcome. It requires that the expectation of log
annual earnings would have followed the same evolution between England and North Irelandacross cohorts in the absence of the school reform. Panel (b) in Figure 2 plots the results of
the interacted two-way fixed effects regression in the reduced form along with a 95% pointwise
confidence interval. The pre-exposed estimates seems consistent with Assumption 13: though
there exists an upward pretrends, all the estimates before the initial exposure to the policychange are not significantly different from zero.

30

Fig. 2. The effect of the instrument in the first stage and reduced form in the setting of Oreopoulos (2006).
Notes: The results for the effect of the school reform on education attainment (Panel (a)) and on log annual
earnings (Panel (b)) under the staggered DID-IV identification strategy. The unexposed group U is a lastexposed cohort, North Ireland and the reference period is t = 1946. The blue lines represent the estimates withpointwise 95% confidence intervals for pre-exposed periods in both panels. These should be equal to zero under
the null hypothesis that the parallel trends assumptions in the treatment and the outcome hold. The red lines
represent the estimates with pointwise 95% confidence intervals for post-exposed periods in both panels.

Figure 2 also sheds light on the dynamic effects of the policy reform on education attainment
and log annual earnings in post-exposed periods. In Panel (a), the estimated increase in yearsof schooling after the reform ranges from 0.56 to 0.87, and all the estimates are statisticallysignificant. In Panel (b), the estimated increase in log annual earnings after the reform varies
from 8% to 25%, and 5 out of 10 estimates are statistically significant.
Note that the post-exposed estimates in Panel (b) do not capture each CACRT in postexposed periods: each estimate in the reduced form is not scaled by the corresponding estimate
in the first stage. In the next section, we estimate each CACRT in post-exposed periods by
employing our proposed estimation method.
6.2

Illustrating our estimation method

We start by estimating two-way fixed effects instrumental variable regression in the author’s
setting. To clearly illustrate the pitfalls of TWFEIV regression, in our estimation, we slightly
modify the author’s specification. Specifically, Oreopoulos (2006) (more precisely Oreopoulos(2008)) includes some covariates (survey year, sex, and a quartic in age) and runs the weighted
regression in the main specification (see Oreopoulos (2006), Oreopoulos (2008) for details),
whereas we exclude such covariates and do not apply their weights to our regression.
The result is shown in Table 8. The TWFEIV estimate is −0.009 and it is not significantly
different from 0, which indicates that on the whole, the returns to schooling in the U.K. is nearlyzero. However, this may be a misleading conclusion: we cannot interpret that the TWFEIV
estimand captures the properly weighted average of each CACRT if the effect of the school
reform on education attainment or log annual earnings is not stable across cohorts (Miyaji(2024)).
31

Fig. 3. The cohort specific average causal response on the treated in each relative period in the setting ofOreopoulos (2006). Notes: The results for returns to schooling under the staggered DID-IV identification
strategy. The unexposed group U is North Ireland and the reference period is period t = 1946. The red lines
represent the stacked two stage least squares estimates with pointwise 95% confidence intervals for post-exposed
periods.
Table 8. Returns to schooling in Oreopoulos (2006)
Estimate
TSLS with fixed effects-0.009
IV
θsel
(e)
0.240
Notes: Sample size 82790 observations.

Standard Error
0.039
0.098

95% CI[-0.085, 0.068][0.047, 0.433]

The TWFEIV regression performs the ”bad comparisons” (c.f. Goodman-Bacon (2021)) in
the author’s setting: when we run the TWFEIV regression, we treat the set of already exposed
units in North Ireland as controls between 1957 and 1965, as both regions are already exposedto the policy shock during these periods. In Appendix D, we quantify the bias terms of theTWFEIV estimand by using Lemma 7 in Miyaji (2024), and show that the TWFEIV estimandis negatively biased in Oreopoulos (2006). Specifically, we show that all the bias terms are
positive, whereas all the assigned weights are negative, which yields the downward bias for the
TWFEIV estimand.
We now employ our proposed method to estimate each CACRT. We first create data sets bycohort t (t = 1947, . . . , 1956). Each data set only contains units of cohort t and cohort t = 1946
in England and North Ireland. We define North Ireland as an unexposed group U and discard
the units who were aged at 14 between 1957 and 1965 in order to avoid the bad comparisons.
We then run TSLS regression in each data set. The standard error is calculated by using theinfluence function shown in equation (26) in Appendix C.
Figure 3 plots the point estimates and the corresponding 95% confidence intervals in eachrelative period after the school reform. The estimates for each CACRTe,t range from 14% to
38% with wide confidence intervals, and 4 out of 10 estimates are statistically significant.
Finally, we estimate the summary causal measure by aggregating each CACRTe,t . Specifically, we estimate the weighted average of each CACRTe,t during post-exposed periods in
32

England (e = 1947):
IV
(e) =
θsel

1956
X

1
CAETe,t
CACRTe,t .
P1956
1
CAET
e,t
t=1947t=1947Here, each weight assigned to the CACRTe,t represents the relative amount of the effect of thepolicy reform on education attainment during post-exposed periods in England.
The result is shown in Table 8. The estimate is 0.24 and it is significantly different fromzero. The estimated returns to schooling are substantial; it is likely because each CACRTe,tcaptures the returns to schooling among the compliers: such units may belong to relatively
low-skilled labor or low-income family, and have potentially much gain from the school reform.
The estimates obtained from our proposed method and weighting scheme are significantly
different from the TWFEIV estimate: our STS estimates and its summary measure are all
positive, whereas the TWFEIV estimate is strictly negative. Overall, our results indicate thatthe economic returns of education are substantial in the U.K. and the estimation method
matters in staggered DID-IV designs in practice.

7

Conclusion

Instrumental variable strategies are pervasive in economics to estimate the effect of a treatment
on an outcome. In this design, however, we commonly face two challenges: the internal andexternal validity of the IV estimate. To overcome at least the external validity, many studies
have leveraged variation occurring from the different timing of policy adoption across units as
an instrument for treatment, and use instrumental variable techniques. The instrument basedon these policy changes, however, generally fails to satisfy the randomization assumption in IV
designs in practice, casting the doubt on the internal validity of the IV estimate. Rather, theunderlying identification strategy is parallel to DID designs, under which we identify the effectof the policy shock on the outcome, leveraging the variation of the exposure to that policy
shock across units and over time.
In this paper, we formalize the underlying identification strategy as an instrumented differencein-differences (DID-IV) by combining the IV techniques with DID designs. We start by considering a simple setting with two periods and two groups. In this setting, our DID-IV design
mainly consists of a monotonicity assumption, and parallel trends assumptions in the treatment
and the outcome between the two groups. We show that the Wald-DID estimand captures the
local average treatment effect on the treated (LATET) under 2 × 2 DID-IV designs. We also
clarify the interpretation of the parallel trends assumption in the outcome. Specifically, weshow that in DID-IV settings, time also plays the role of instrument, and the parallel trends assumption in the outcome requires the same expected time gain between exposed and unexposedgroups. Finally, we compare DID-IV to Fuzzy DID designs considered in de Chaisemartin and
D’Haultfœuille (2018), and point out the issues inherent in Fuzzy DID designs.
Next, we consider the DID-IV design in the case where there are more than two time periods
and units become exposed to the instrument at different times. We call this a staggered DID-IV
design, and formalize the target parameter and identifying assumptions. Specifically, our target
parameter in this design is the cohort specific local average treatment effects on the treated(CLATT). The identifying assumptions are the natural generalization of those in 2 × 2 DID-IV
designs.
We also provide the estimation method in staggered DID-IV designs, which does not require
strong restrictions on treatment effect heterogeneity. In practice, most DID-IV applications implement the staggered DID-IV design by running TWFEIV regressions. In companion paper
33

(Miyaji (2024)), however, we show that the conventional approach is inadequate for summarizing the treatment effects if the effect of the instrument on the treatment or the outcome
is not stable over time. Our estimation method carefully chooses the comparison groups anddoes not suffer from the bias arising from the time-varying exposed effects. We also propose
the weighting scheme in staggered DID-IV designs, and explain how one can conduct pretrends
test to assess the validity of the parallel trends assumption in the treatment and the outcome.
Finally, we illustrate the empirical relevance of our findings with the setting of Oreopoulos(2006) who estimate returns to schooling in the United Kingdom, exploiting the timing variationof the introduction of school reforms between British and North Ireland. First, we assessthe underlying DID-IV identification strategy in the author’s setting and check whether theidentifying assumptions are plausible. Next, we estimate a TWFEIV regression and our stacked
two stage least squares regressions in each dataset. We find that the TWFEV estimate turns
out to be strictly negative, whereas our STS estimates are all positive. Finally, we estimate thesummary causal parameter by exploiting our STS estimates. The estimate for the summary
measure is also positive and indicates that returns to schooling are substantial in the U.K.
Overall, this paper provides a new econometric framework for estimating the causal effects
when the treatment adoption is potentially endogenous over time, but researchers can use variation in the timing of policy adoption across units as an instrument for the treatment. To
avoid the issue of using the TWFEIV estimator under this design, we also provide a reliable
estimation method that is free from strong restrictions on treatment effect heterogeneity. Further developing alternative estimation methods and diagnostic tools will be a promising areafor future research, facilitating the credibility of DID-IV research design in practice.

34

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36

A

Proofs in section 2

Proof of Theorem 1.
Proof. First we consider the denominator of the Wald-DID estimand. For the denominator, wehave
E[D1 − D0 |E = 1] − E[D1 − D0 |E = 0]
=E[D1 ((0, 1)) − D0 ((0, 1))|E = 1] − E[D1 ((0, 0)) − D0 ((0, 0))|E = 0]
=E[D1 ((0, 1)) − D1 ((0, 0))|E = 1]
+ {E[D1 ((0, 0)) − D0 ((0, 1))|E = 1] − E[D1 ((0, 0)) − D0 ((0, 0))|E = 0]}=E[D1 ((0, 1)) − D1 ((0, 0))|E = 1]
+ {E[D1 ((0, 0)) − D0 ((0, 0))|E = 1] − E[D1 ((0, 0)) − D0 ((0, 0))|E = 0]}=P r(D1 ((0, 1)) > D1 ((0, 0))|E = 1)
=P r(CM Z |E = 1).

(9)

(10)

where the second equality follows from the simple manipulation. The third equality follows
from Assumption 4 (no anticipation in the first stage) and the forth equality follows from
Assumption 3 (Monotonicity assumption) and Assumption 5 (Parallel Trends Assumption in
the treatment).
Next, to show that the Wald-DID estimand equals to the LATET, it suffices to show thatE[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0] = E[Y1 (1) − Y1 (0)|E = 1, CM Z ] · P r(CM Z |E = 1)
= LAT ET · P r(CM Z |E = 1).
For the numerator, we haveE[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0]
=E[Y1 (D1 ((0, 1))) − Y0 (D0 ((0, 1)))|E = 1] − E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 0]
=E[Y1 (D1 ((0, 1))) − Y1 (D1 ((0, 0)))|E = 1]
+ {E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 1)))|E = 1] − E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 0]}=E[Y1 (D1 ((0, 1))) − Y1 (D1 ((0, 0)))|E = 1]
+ {E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 1] − E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 0]}=E[(D1 ((0, 1)) − D1 ((0, 0))) · (Y1 (1) − Y1 (0))|E = 1]
=E[Y1 (1) − Y1 (0)|E = 1, CM Z ] · P r(CM Z |E = 1).
=LAT ET · P r(CM Z |E = 1).

(11)

The first equality follows from Assumption 1 (No carryover assumption) and Assumption 2(Exclusion restriction). The second equality follows from the simple manipulation. The third
equality follows from Assumption 4. The forth equality follows from Assumption 6 (Parallel
Trends Assumption in the outcome) and the simple calculation. The fifth equality follows fromthe Law of Iterated Expectations and Assumption 3.
Combining the result (11) with (10), we obtain
E[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0]
LAT ET · P r(CM Z |E = 1)=
E[D1 − D0 |E = 1] − E[D1 − D0 |E = 1]
P r(CM Z |E = 1)
= LAT ET.
Completing the proof.
37

Proof of Theorem 2.
Recall that we define ∆e as follows:∆e ≡ E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = e].
Then, we obtain:∆e = E[Y1 (1) − Y0 (1)|AT T , E = e]P r(AT T |E = e)
+ E[Y1 (0) − Y0 (0)|N T T , E = e]P r(N T T |E = e)
+ E[Y1 (1) − Y0 (0)|CM T , E = e]P r(CM T |E = e)
+ E[Y1 (0) − Y0 (1)|DF T , E = e]P r(DF T |E = e)X=wgt ,e ∆gt ,e .
gtHere the first equality follows from the Law of Iterated Expectation and the second equality
follows from the definition of wgt ,e and ∆gt ,e . Clearly, the weight wgt ,e sum to one by construction.
Completing the proof.

B

Extensions

B.1

Non-binary, ordered treatment

Proof of Theorem 3.
Proof. Let λtZ,j = 1(Dt ((0, z)) ≥ j) be the indicator function for t ∈ {0, 1}, z ∈ {0, 1} andj ∈ {0, . . . , J + 1}. We note that λtZ,0 = 1 and λtZ,J+1 = 0 hold for all t and z by construction.
Here, we can rewrite the observed outcome Yt as follows:
Yt = Z1 · Yt (Dt ((0, 1))) + (1 − Z1 ) · Yt (Dt ((0, 0)))
)
(
) (
J
J
X
X
= Z1 ·Yt (j) · (λt1,j − λt1,j+1 ) + (1 − Z1 ) ·Yt (j) · (λt0,j − λt0,j+1 ) .
j=0

j=0

where we use Assumption 1 and 2.
For the numerator in the Wald DID estimand, we have:E[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0]
= E[Y1 (D1 ((0, 1))) − Y1 (D1 ((0, 0)))|E = 1]
+ {E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 1] − E[Y1 (D1 ((0, 0))) − Y0 (D0 ((0, 0)))|E = 0]}= E[Y1 (D1 ((0, 1))) − Y1 (D1 ((0, 0)))|E = 1].
Here the first equality follows from the simple manipulation and Assumption 4. The second
equality follows from Assumption 6.

38

In terms of the λtZ,j , we write the previous expression as:
E[Y1 (D1 ((0, 1))) − Y1 (D1 ((0, 0)))|E = 1]
" J
#
X
=E
Y1 (j) · [λ11,j − λ11,j+1 − λ10,j + λ10,j+1 ]|E = 1
j=0

" J
#
X
1
1
1
1
=E
(Y1 (j) − Y1 (j − 1)) · [λ1,j − λ0,j ] + Y1 (0) · (λ1,0 − λ0,0 )|E = 1
j=1

" J
#
X
=E
(Y1 (j) − Y1 (j − 1)) · [λ11,j − λ10,j ]|E = 1 .
j=1where the second equality follows from the fact: λ11,0 − λ10,0 = 1.
We note that λ11,j ≥ λ10,j from Assumption 3 and that λ11,j and λ10,j can take only two values,
zero or one. Therefore, we obtain:
" J
#
X
1
1
E
(Y1 (j) − Y1 (j − 1)) · [λ1,j − λ0,j ]|E = 1
j=1

=

J
X

E[(Y1 (j) − Y1 (j − 1)|λ11,j − λ10,j = 1, E = 1]P r(λ11,j − λ10,j = 1|E = 1)

j=1

=

J
X

E[(Y1 (j) − Y1 (j − 1)|D1 ((0, 1)) ≥ j > D1 ((0, 0)), E = 1]

j=1

× P r(D1 ((0, 1)) ≥ j > D1 ((0, 0))|E = 1).

(12)

For the denominator in the Wald-DID estimand, by the similar argument, we first obtain:
E[D1 − D0 |E = 1] − E[D1 − D0 |E = 0]
= E[D1 ((0, 1)) − D1 ((0, 0))|E = 1]
+ {E[D1 ((0, 0)) − D0 ((0, 0))|E = 1] − E[D1 ((0, 0)) − D0 ((0, 0))|E = 0]}= E[D1 ((0, 1)) − D1 ((0, 0))|E = 1].
Here the first equality follows from the simple algebra and Assumption 4. The second equality
follows from Assumption 5.
Then, we have:E[D1 ((0, 1)) − D1 ((0, 0))|E = 1]
#
" J
X
=E
j · [λ11,j − λ11,j+1 − λ10,j + λ10,j+1 ]|E = 1
j=0

#
" J
X
=E
[λ11,j − λ10,j ]|E = 1
j=1

=

J
X

P r(D1 ((0, 1)) ≥ j > D1 ((0, 0))|E = 1).

j=1

Combining the result (13) with (12), we obtain the desired result.
39

(13)

B.2

Repeated cross sections

In this section, we present our identification results under repeated cross section settings.
B.2.1

Two time periods

Let Yi and Di denote the outcome and the treatment for unit i. Let Zi denote the instrument
path for unit i: Zi = (0, 0) if unit i is not exposed to the instrument and Zi = (0, 0) if unit i
is exposed to the instrument. Let Ei ∈ {0, 1} denote the group indicator for unit i: Ei = 1 if
Zi = (0, 1) and Ei = 0 if Zi = (0, 0). Let Ti ∈ {0, 1} denote the binary indicator for time. For
all z ∈ S(Z), let Yi (0, z), Yi (1, z), and Di (z) denote potential outcomes and potential treatment
choices for unit i. Let Di,t (z) denote potential treatment choices under Ti = t. We assume that
{Yi , Di , Zi , Ei , Ti }ni=1 are independent and identically distributed (i.i.d).
In two periods and two groups settings, our target parameter is the local average treatment
effect in period 1:
LAT ET ≡ E[Yi (1) − Yi (0)|Ti = 1, Ei = 1, Di,1 ((0, 1)) > Di,1 ((0, 0))]= E[Yi (1) − Yi (0)|Ti = 1, Ei = 1, CM Z ].
We make the following identification assumptions for the Wald-DID estimand to capture
the LATET. These assumptions are suitable for repeated cross section settings.
Assumption 14 (Exclusion restriction).
∀z ∈ S(Z), Yi (0, z) = Yi (0), Yi (1, z) = Yi (1).
Assumption 15 (Monotonicity).
P r(Di,1 ((0, 1)) ≥ Di,1 ((0, 0))) = 1.
Assumption 16 (No anticipation in the first stage).
Di,0 ((0, 1)) = Di,0 ((0, 0)) a.s. for all units i with Ei = 1.
Assumption 17 (Parallel Trends assumption in the treatment).
E[Di ((0, 0))|Ei = 1, Ti = 1] − E[Di ((0, 0))|Ei = 1, Ti = 0]
=E[Di ((0, 0))|Ei = 0, Ti = 1] − E[Di ((0, 0))|Ei = 0, Ti = 0].
Assumption 18 (Parallel Trends assumption in the outcome).
E[Yi (Di (0, 0))|Ei = 1, Ti = 1] − E[Yi (Di (0, 0))|Ei = 1, Ti = 0]
=E[Yi (Di (0, 0))|Ei = 0, Ti = 1] − E[Yi (Di (0, 0))|Ei = 0, Ti = 0].
Theorem 5 below shows that the Wald-DID estimand is equal to the local average treatment
effect on the treated (LATET) in period 1 under Assumptions 14-18. Here, we assume thebinary treatment, but non-binary, ordered treatment case is easy to extend as in Theorem 3(thus we omit it for brevity). In the proof, we omit the index i to ease the notation.

40

Theorem 5. Suppose Assumptions 14-18 hold. If we assume a binary treatment, the WaldDID estimand corresponds to the local average treatment effect on the treated (LATET) in
period 1:
E[Y |E = 1, T = 1] − E[Y |E = 1, T = 0] − {E[Y |E = 0, T = 1] − E[Y |E = 0, T = 0]}
E[D|E = 1, T = 1] − E[D|E = 1, T = 0] − {E[D|E = 0, T = 1] − E[D|E = 0, T = 0]}= E[Y (1) − Y (0)|T = 1, E = 1, CM Z ]= LAT ET.

wDID ≡

Proof. First we consider the denominator of the Wald-DID estimand. For the denominator, we
have
E[D|E = 1, T = 1] − E[D|E = 1, T = 0] − {E[D|E = 0, T = 1] − E[D|E = 0, T = 0]}=E[D((0, 1))|E = 1, T = 1] − E[D((0, 1))|E = 1, T = 0]
− {E[D((0, 0))|E = 0, T = 1] − E[D((0, 0))|E = 0, T = 0]}=E[D((0, 1)) − D((0, 0))|E = 1, T = 1](+

E[D((0, 0))|E = 1, T = 1] − E[D((0, 1))|E = 1, T = 0])

− {E[D((0, 0))|E = 0, T = 1] − E[D((0, 0))|E = 0, T = 0]}=E[D((0, 1)) − D((0, 0))|E = 1, T = 1](+

E[D((0, 0))|E = 1, T = 1] − E[D((0, 0))|E = 1, T = 0])

− {E[D((0, 0))|E = 0, T = 1] − E[D((0, 0))|E = 0, T = 0]}=P r(D1 ((0, 1)) > D1 ((0, 0))|E = 1, T = 1)
=P r(CM Z |E = 1, T = 1).

(14)

The second equality follows from the simple manipulation. The third equality follows from
Assumption 16 and the forth equality follows from Assumption 15 and Assumption 17.

41

Next, for the numerator, we haveE[Y |E = 1, T = 1] − E[Y |E = 1, T = 0] − {E[Y |E = 0, T = 1] − E[Y |E = 0, T = 0]}=E[Y (D((0, 1)))|E = 1, T = 1] − E[Y (D((0, 1)))|E = 1, T = 0]
− {E[Y (D((0, 0)))|E = 0, T = 1] − E[Y (D((0, 0)))|E = 0, T = 0]}=E[Y (D((0, 1))) − Y (D((0, 0)))|E = 1, T = 1](+

E[Y (D((0, 0)))|E = 1, T = 1] − E[Y (D((0, 1)))|E = 1, T = 0])

− {E[Y (D((0, 0)))|E = 0, T = 1] − E[Y (D((0, 0)))|E = 0, T = 0]
=E[Y (D((0, 1))) − Y (D((0, 0)))|E = 1, T = 1](+

E[Y (D((0, 0)))|E = 1, T = 1] − E[Y (D((0, 0)))|E = 1, T = 0])

− {E[Y (D((0, 0)))|E = 0, T = 1] − E[Y (D((0, 0)))|E = 0, T = 0]
=E[Y (D((0, 1))) − Y (D((0, 0)))|E = 1, T = 1]
=E[(D((0, 1)) − D((0, 0))) · (Y (1) − Y (0))|E = 1, T = 1]
=E[Y (1) − Y (0)|T = 1, E = 1, CM Z ] · P r(CM Z |E = 1, T = 1).
=LAT ET · P r(CM Z |E = 1, T = 1).

(15)

The second equality follows from the simple manipulation. The third equality follows from
Assumption 16. The forth equality follows from Assumption 18 and the simple calculation.
The fifth equality follows from the Law of Iterated Expectations and Assumption 15.
Combining the result (14) with (15), we obtain
LAT ET · P r(CM Z |E = 1, T = 1)
P r(CM Z |E = 1, T = 1)
= LAT ET.

wDID =

Completing the proof.
B.2.2

Multiple time periods

Let Ti ∈ {1, . . . , T } denote the time period when unit i is observed and let Zi,t denote theinstrument status under Ti = t. We assume Assumption 7 in section 3, that is, we assume thestaggered assignment of the instrument across units. In addition, we assume Assumption 14(Exclusion restriction), which allows us to write Yi (Di , z) = Yi (Di ). Let Ei ∈ {1, . . . , T, ∞}denote the cohort which unit i belongs to. Let Yi (Die ) and Die denote potential outcomes andepotential treatment choices when unit i belongs to cohort e. Let Di,tdenote potential treatment
choices under Ti = t when unit i belongs to cohort e. We assume that {Yi , Di , Zi , Ei , Ti }ni=1 are
independent and identically distributed (i.i.d).
In multiple time periods and multiple cohorts settings, our target parameter is the cohort
specific local average treatment effect on the treated in period T = e + l:e∞
CLAT Te,e+l ≡ E[Yi (1) − Yi (0)|Ti = e + l, Ei = e, Di,e+l> Di,e+l]= E[Yi (1) − Yi (0)|Ti = e + l, Ei = e, CMe,e+l ].
42

When repeated cross section data are available and we have multiple time periods, our staggered
DID-IV designs consist of Assumptions 7, 10, 11 (in section 3), Assumption 14 (Exclusion
restriction), and the following parallel trends assumptions.
Assumption 19 (Parallel Trends Assumption in the treatment in multiple time periods).
For all s < t, E[Di∞ |Ei = e, Ti = t] − E[Di∞ |Ei = e, Ti = s] is same for all e ∈ S(Ei ).
Assumption 20 (Parallel Trends Assumption in the outcome in multiple time periods).
For all s < t, E[Yi (Di∞ )|Ei = e, Ti = t] − E[Yi (Di∞ )|Ei = e, Ti = s] is same for all e ∈ S(Ei ).
B.3

Introducing the treatment path in 2 × 2 DID-IV designs

In this section, we discuss the DID-IV identification strategy in two periods with a binary
treatment, introducing the treatment path in potential outcomes Yi,t (d, z). We first consider
the two types of the no anticipation assumption on potential outcomes Yi,t (d, z) instead of
imposing Assumption 1 (No carryover assumption). We then define the expected time gain andformalize the parallel trends assumption in the outcome as in Assumption 6 in this setting.
Finally, we show that a Wald-DID estimand identifies the LATET’ (see section 4) under thesuitable assumptions similar to the ones in section 2.3. Henceforth, we consider the same setting
as in section 2.1 except that we do not adopt Assumption 1.
First, we make the following no anticipation assumptions on the outcome.
Assumption 21 (No anticipation on the outcome among the CM Z ∧ N T T in an exposedgroup).
∀z ∈ S(Z), Yi,0 ((0, 1), z) = Yi,0 ((0, 0), z) for all the units with Ei = 1 and (CM Z ∧ N T T ).
This assumption requires that the potential outcome at period 0 is same as the baseline
outcome Yi,0 ((0, 0), z) given the instrument path z, for those who are assigned to the instrumentz = (0, 1) and belongs to the type CM Z ∧ N T T . We note that this assumption corresponds
to the no anticipation assumption usually made in the common DID set up as in Roth et al.
(2023) (see Table 3 and Table 4 in section 2.5)8 .
Assumption 22 (No anticipation on the outcome among the CM Z ∧ DF T in an exposedgroup).
∀z ∈ S(Z), Yi,0 ((1, 1), z) = Yi,0 ((1, 0), z) for all the units with Ei = 1 and (CM Z ∧ DF T ).
This assumption requires that the potential outcome at period 0 is same as the baseline
outcome Yi,0 ((1, 0), z) given the instrument path z, for those who are assigned to the instrumentz = (0, 1) and belongs to the type CM Z ∧ DF T . Assumption 22 is inherent to the DID-IV
identification strategy when we introduce the treatment path.
We can rationalize Assumption 21 and 22 by noting that both the two Assumptions andthe no anticipation assumption proposed by the recent DID literature restrict the anticipatory
behavior of the units who belong to the exposed group and the compliers CM Z .

8Here, it is inconsequential whether the instrument path z is included or not in potential outcomes because
we have d = z in the common DID set up.

43We now make the parallel trends assumption in the outcome that is suitable for the set up¯ gt ,e denote
we are considering here. We first define the similar notation as in section 2.4. Let ∆the expectation of the time trends in each groups in group Ei = e:¯ AT T ,e ≡ E[Yi,1 ((1, 1)) − Yi,0 ((1, 1))|AT T , Ei = e],∆¯ N T T ,e ≡ E[Yi,1 ((0, 0)) − Yi,0 ((0, 0))|N T T , Ei = e],∆¯ CM T ,e ≡ E[Yi,1 ((0, 1)) − Yi,0 ((0, 1))|CM T , Ei = e],∆¯ DF T ,e ≡ E[Yi,1 ((1, 0)) − Yi,0 ((1, 0))|DF T , Ei = e].
∆¯ 0 and ∆¯ 1 denote the expected time gain in unexposed and exposed groups respectively:
Let ∆
X
¯0 ≡
¯ gt ,0 ,∆wgt ,0 ∆
gt

¯1 ≡
∆

X

¯ gt ,1 ,wgt ,1 ∆gt

where the definition of the weight wgt ,e is same as in section 2.4.
As we previously noted in section 2.4, the parallel trends assumption in the outcome can beinterpreted as requiring the homogeneous expected time gain between exposed and unexposedgroups. The following assumption indeed make a such restriction in the current set up.
Assumption 23 (Parallel trend assumption in the outcome). The expected time gain between¯0 = ∆¯ 1.
exposed and unexposed groups is same, that is, we have ∆The theorem below shows that a Wald-DID estimand is equal to the target parameter
LAT ET ′ under Assumption 2-5 and Assumption 21-23.
Theorem 6. Suppose Assumption 2-5 and Assumption 21-23 holds. Then, a Wald-DID estimand corresponds to LAT ET ′ , that is, we haveE[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0]
= LAT ET ′ .
E[D1 − D0 |E = 1] − E[D1 − D0 |E = 0]
Proof. First, we consider the denominator of the Wald-DID estimand. From the similar argument in the proof of Theorem 1, one can show the following result:E[D1 − D0 |E = 1] − E[D1 − D0 |E = 0] = P r(CM Z |E = 1)
= P r(CM Z ∧ DF T |E = 1) + P r(CM Z ∧ N T T |E = 1).
(16)
Here the second equality holds from the fact that we can partition the compliers CM Z in an
exposed group into (CM Z ∧ DF T ) and (CM Z ∧ N T T ) (see Table 1).

44

Next, for the numerator, we first decompose E[Y1 − Y0 |E = 1] as follows.
¯ CM T ,1 wCM T ,1 + ∆¯ AT T ,1 wAT T ,1
E[Y1 − Y0 |E = 1] = ∆+ E[Y1 ((0, 1)) − Y0 ((0, 1))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((1, 1)) − Y0 ((1, 1))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1)
+ E[Y1 ((1, 0)) − Y0 ((1, 0))|E = 1, (N T Z ∧ DF T )]P r((N T Z ∧ DF T )|E = 1)
+ E[Y1 ((0, 0)) − Y0 ((0, 0))|E = 1, (N T Z ∧ N T T )]P r((N T Z ∧ N T T )|E = 1)
¯ CM T ,1 wCM T ,1 + ∆¯ AT T ,1 wAT T ,1=∆
+ E[Y1 ((0, 1)) − Y1 ((0, 0))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((0, 0)) − Y0 ((0, 0))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((1, 1)) − Y1 ((1, 0))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1)
+ E[Y1 ((1, 0)) − Y0 ((1, 0))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1)
+ E[Y1 ((1, 0)) − Y0 ((1, 0))|E = 1, (N T Z ∧ DF T )]P r((N T Z ∧ DF T )|E = 1)
+ E[Y1 ((0, 0)) − Y0 ((0, 0))|E = 1, (N T Z ∧ N T T )]P r((N T Z ∧ N T T )|E = 1)
¯ CM T ,1 wCM T ,1 + ∆¯ AT T ,1 wAT T ,1=∆
¯ N T T ,1 wN T T ,1 + ∆¯ DF T ,1 wDF T ,1+∆
+ E[Y1 ((0, 1)) − Y1 ((0, 0))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((1, 1)) − Y1 ((1, 0))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1)
¯1=∆
+ E[Y1 ((0, 1)) − Y1 ((0, 0))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((1, 1)) − Y1 ((1, 0))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1)
(17)
The first equality follows from Table 1 and Assumption 2. The second equality follows from
Assumption 21, Assumption 22 and simple manipulation. The third equality follows from Table¯ 1.
1. The final equality follows from the definition of the expected time gain ∆We next decompose E[Y1 − Y0 |E = 0] as follows.
E[Y1 − Y0 |E = 0]
= E[Y1 ((1, 1)) − Y0 ((1, 1))|E = 0, AT T ]P r(AT T |E = 0)
+ E[Y1 ((0, 1)) − Y0 ((0, 1))|E = 0, CM T ]P r(CM T |E = 0)
+ E[Y1 ((0, 0)) − Y0 ((0, 0))|E = 0, N T T ]P r(N T T |E = 0)
+ E[Y1 ((1, 0)) − Y0 ((1, 0))|E = 0, DF T ]P r(DF T |E = 0)
¯ 0.
=∆

(18)

Here the first equality follows from Table 2 and the second equality follows from the definition¯ 0.
of the expected time gain ∆From the result (18) with (17) and Assumption 23, we obtain
E[Y1 − Y0 |E = 1] − E[Y1 − Y0 |E = 0]
= E[Y1 ((0, 1)) − Y1 ((0, 0))|E = 1, (CM Z ∧ N T T )]P r((CM Z ∧ N T T )|E = 1)
+ E[Y1 ((1, 1)) − Y1 ((1, 0))|E = 1, (CM Z ∧ DF T )]P r((CM Z ∧ DF T )|E = 1).
Combining the result (19) with (16), we obtain the desired result.
45

(19)

C

Proof in section 4

C.1

Proof of Theorem 4First, we prove the consistency of our SLS estimator. Recall that α̂e,l and π̂ e,l take the followingform:
EN [(Yi,e+l − Yi,e−1 ) · 1{Ei = e}] EN [(Yi,e+l − Yi,e−1 ) · 1{Ei ∈ U }]−EN [1{Ei = e}]
EN [1{Ei ∈ U }]12
≡ α̂e,l − α̂e,l .
EN [(Di,e+l − Di,e−1 ) · 1{Ei = e}] EN [(Di,e+l − Di,e−1 ) · 1{Ei ∈ U }]−π̂ e,l =EN [1{Ei = e}]
EN [1{Ei ∈ U }]12
≡ π̂e,l − π̂e,l .

α̂e,l =

We assume that α̂e,lPand π̂ e,l are well defined. More precisely, we assume that cohort e isnon-empty, that is, ni=1 1{Ei = e} > 0 and there exist
Pn some sets of the unexposed cohortU ⊆ {u : e − 1 < u ≤ T } that are non-empty, i.e., i=1 1{Ei ∈ U } > 0. This assumption
guarantees that each Wald-DID estimatore,l\T e,e+l = α̂CLATπ̂ e,l12α̂e,l− α̂e,l.
= 12π̂e,l − π̂e,lis also well defined.
\T e,e+l . We note that by the Law of Large
First we derive the probability limit of CLAT
Numbers and Slutsky’s theorem, we have
E[(Yi,e+l − Yi,e−1 ) · 1{Ei = e}]
P r(Ei = e)
= E[Yi,e+l − Yi,e−1 |Ei = e],
p

1
α̂e,l
→
−

where the second equality follows from the Law of Iterated Expectations.
By the similar arguments, we have
p

2
α̂e,l
→
− E[Yi,e+l − Yi,e−1 |Ei ∈ U ]
p

1
π̂e,l
→
− E[Di,e+l − Di,e−1 |Ei = e]
p

2
π̂e,l
→
− E[Di,e+l − Di,e−1 |Ei ∈ U ]From the Slutsky’s theorem, we have
E[Yi,e+l − Yi,e−1 |Ei = e] − E[Yi,e+l − Yi,e−1 |Ei ∈ U ]p\T e,e+l →.
CLAT−
E[Di,e+l − Di,e−1 |Ei = e] − E[Di,e+l − Di,e−1 |Ei ∈ U ]Lastly, it remains to show that the right hand side of (20) is equal to CLAT Te,e+l .

46

(20)

For the numerator, we have
E[Yi,e+l − Yi,e−1 |Ei = e] − E[Yi,e+l − Yi,e−1 |Ei ∈ U ]X=E[Yi,e+l − Yi,e−1 |Ei = e] −E[Yi,e+l − Yi,e−1 |Ei = e]P r(Ei = e|Ei ∈ U )e∈Ue∞=E[Yi,e+l (Di,e+l) − Yi,e−1 (Di,e−1)|Ei = e] −X∞∞)|Ei ∈ U ]P r(Ei = e|Ei ∈ U )) − Yi,e−1 (Di,e−1
E[Yi,e+l (Di,e+l

e∈U
e
∞
∞
∞
)|Ei = e]) − Yi,e−1 (Di,e−1=E[Yi,e+l (Di,e+l ) − Yi,e+l (Di,e+l )|Ei = e] + E[Yi,e+l (Di,e+l

−

X

∞
∞
E[Yi,e+l (Di,e+l) − Yi,e−1 (Di,e−1)|Ei ∈ U ]P r(Ei = e|Ei ∈ U )e∈U∞e)|Ei = e]) − Yi,e+l (Di,e+l=E[Yi,e+l (Di,e+l∞∞∞∞+ E[Yi,e+l (Di,e+l) − Yi,e−1 (Di,e−1)] − E[Yi,e+l (Di,e+l) − Yi,e−1 (Di,e−1)]=E[Yi,e+l (1) − Yi,e+l (0)|Ei = e, CMe,e+l ]P r(CMe,e+l |Ei = e).

(21)

The third equality follows from Assumption 8, 9 and 11. The forth equality follows from
Assumption 13 and the fifth equality follows from Assumption 10.
For the denominator, by the similar calculations,
E[Di,e+l − Di,e−1 |Ei = e] − E[Di,e+l − Di,e−1 |Ei ∈ U ]e∞∞∞= E[Di,e+l− Di,e+l|Ei = e] + E[Di,e+l− Di,e−1|Ei = e] −X∞∞
E[Di,e+l− Di,e−1|Ei = e]P r(Ei = e|Ei ∈ U )e∈U= P r(CMe,e+l |Ei = e),(22)where the final equality follows from Assumption 10 and Assumption 12.
Combining the result (21) with (22), we obtain the desirable result:
E[Yi,e+l − Yi,e−1 |Ei = e] − E[Yi,e+l − Yi,e−1 |Ei ∈ U ]E[Di,e+l − Di,e−1 |Ei = e] − E[Di,e+l − Di,e−1 |Ei ∈ U ]E[Yi,e+l (1) − Yi,e+l (0)|Ei = e, CMe,e+l ]P r(CMe,e+l |Ei = e)=
P r(CMe,e+l |Ei = e)
= CLAT Te,e+l .
Next, we prove that our STS estimator is asymptotically normal, deriving its influencefunction.
We define θe,l to be
E[Yi,e+l − Yi,e−1 |Ei = e] − E[Yi,e+l − Yi,e−1 |Ei ∈ U ](= CLAT Te,e+l )E[Di,e+l − Di,e−1 |Ei = e] − E[Di,e+l − Di,e−1 |Ei ∈ U ]12αe,l− αe,l≡ 1.
2πe,l − πe,l

θe,l ≡We use the following fact repeatedly in the derivation. This fact is also found in de Chaisemartin
and D’Haultfœuille (2018).
Fact 1. If
√

n
n
√
1 X
1 X
n(Â − A) = √ai + op (1),n(B̂ − B) = √bi + op (1),
n i=1
n i=1

47

we have
√

n

Â

A
−
B̂ B

!

First we derive the influence function of√n

1 X ai − (A/B)bi=√+ op (1).
B
n i=1
√
1
2
1
2
n(α̂e,l+ α̂e,l− (αe,l+ αe,l)). We note thatn

1 X
(1{Ei = e} − E[1{Ei = e}]).
n(EN [1{Ei = e}] − E[1{Ei = e}]) = √
n i

and
√
n(EN [(Yi,e+l − Yi,e−1 )1{Ei = e}] − E[(Yi,e+l − Yi,e−1 )1{Ei = e}])n
1 X=√((Yi,e+l − Yi,e−1 ) · 1{Ei = e} − E[(Yi,e+l − Yi,e−1 ) · 1{Ei = e}]).
n i
From the observations and using Fact 1, we obtainn√
1 X 1{Ei = e} · [(Yi,e+l − Yi,e−1 ) − E[Yi,e+l − Yi,e−1 |Ei = e]]11+ op (1).
n(α̂e,l − αe,l ) = √E[1{Ei = e}]
n i
n

1 X
≡√
ζi,e,l + op (1).
n i
By symmetry, we also obtain the influence function of√122n(α̂e,l− αe,l
)= √

n

√
2
2
n(α̂e,l− αe,l):nX
1{Ei = U } · [(Yi,e+l − Yi,e−1 ) − E[Yi,e+l − Yi,e−1 |Ei = U ]]E[1{Ei = U }]i

+ op (1).

n1 Xϕi,e,l + op (1).
≡√n iThis implies that
n
√
1 X
1
2
1
2
√
n(α̂e,l − α̂e,l − (αe,l − αe,l )) =(ζi,e,l − ϕi,e,l ) + op (1)
n i
n

1 X
≡√
ai,e,l + op (1).
n i

(23)

√
1
2
1
2
Next we derive the influence function of n(π̂e,l+ π̂e,l− (πe,l+ πe,l)). From the symmetry,by replacing Y with D, we obtain the following:
n
√
1 X
1
2
1
2
(ηi,e,l − ξi,e,l ) + op (1)n(π̂e,l − π̂e,l − (πe,l − πe,l )) = √
n i
n

1 X
≡√
bi,e,l + op (1),
n i

48

(24)

where we define
1{Ei = e} · [(Di,e+l − Di,e−1 ) − E[Di,e+l − Di,e−1 |Ei = e]],E[1{Ei = e}]1{Ei = U } · [(Di,e+l − Di,e−1 ) − E[Di,e+l − Di,e−1 |Ei = U ]].
ξi,e,l ≡E[1{Ei = U }]ηi,e,l ≡Using (23), (24) and Fact 1, by some calculations, we obtain
√

1
2
1
2
αe,l
− αe,lα̂e,l− α̂e,l
− 1
)
n( 1
2
2
π̂e,l − π̂e,l
πe,l − πe,ln
1 X=√
ψi,e,l + op (1),n i\T e,e+l − CLAT Te,e+l ) =n(CLAT√

where the influence function ψi,e,l is:ψi,e,l1= 12πe,l − πe,l
=

1
1
2
πe,l
− πe,l!
12αe,l− αe,lζi,e,l − ϕi,e,l − 1(ηi,e,l − ξi,e,l )2πe,l − πe,l
 p

 p
!
p
p
1{Ei = U } δi,e,l− (E[δi,e,l|Ei = U ])1{Ei = e} δi,e,l− E[δi,e,l|Ei = e]−,E[1{Ei = e}]E[1{Ei = U }](25)pwhere we define δi,e,l= (Yi,e+l − Yi,e−1 ) − θe,l · (Di,e+l − Di,e−1 ).
Therefore, the asymptotic variance V (ψi,e,l ) is

V (ψi,e,l )
1
= 1
2 2
(πe,l − πe,l
)
C.2


 p

 p
2 
2  !
p
p
E 1{Ei = e} δi,e,l
E 1{Ei = U } δi,e,l− E[δi,e,l− (E[δi,e,l|Ei = e]|Ei = U ]+.
E[1{Ei = e}]2
E[1{Ei = U }]2

Repeated cross sections

We also present the influence function of our STS estimator when repeated cross section datar
are available.9 . Let θe,ldefinerθe,l≡αe,e+l − αe,e−1 − [βU,e+l − βU,e−1 ],
πe,e+l − πe,e−1 − [γU,e+l − γU,e−1 ]where
αe,t = E[Yi |Ei = e, Ti = t], βU,t = E[Yi |Ei ∈ U, Ti = t],πe,t = E[Di |Ei = e, Ti = t], γU,t = E[Di |Ei ∈ U, Ti = t] (t = e + l, e − 1).
r
In repeated cross section settings, our STS estimator is the sample analog of θe,l
, whichrr
we denote θ̂e,l . By the similar arguments in the proof of Theorem 4, one can show that θ̂e,lis
9

The derivation here is essentially the same in de Chaisemartin and D’Haultfœuille (2018), who present
the influence function of the Wald-DID estimator in repeated cross section settings with two periods and twogroups.

49

consistent for CLAT Te,e+l under Assumptions 7, 10, 11, 14, 19, and 20, and have the following
influence function:rψi,e,l
=

1
2
1
2
1
]
− γe,l− [γe,l− πe,lπe,l1e,e+l · [δi,e,l − E[δi,e,l |Ei = e, Ti = e + l]] 1e,e−1 · [δi,e,l − E[δi,e,l |Ei = e, Ti = e − 1]]−E[1e,e+l ]E[1e,e−1 ]×!
1U,e+l · [δi,e,l − E[δi,e,l |Ei ∈ U, Ti = e + l]] 1U,e−1 · [δi,e,l − E[δi,e,l |Ei ∈ U, Ti = e − 1]]−+,E[1U,e+l ]E[1U,e−1 ](26)rr
where δi,e,l= Yi − θe,l
· Di .

C.3

Triple DID-IV designs

We also present the influence function of our triple DID-IV estimator when panel or repeatedprand θe,l,g
definecross section data are available. Let θe,l,g
αe,A − αe,B − [βU,A − βU,B ],πe,A − πe,B − [γU,A − γU,B ][(αe,e+l,A − αe,e−1,A ) − (αe,e+l,B − αe,e−l,B )] − [(βU,e+l,A − βU,e−1,A ) − (βU,e+l,B − βU,e−1,B )]rθe,l,g≡,[(πe,e+l,A − πe,e−1,A ) − (πe,e+l,B − πe,e−l,B )] − [(γU,e+l,A − γU,e−1,A ) − (γU,e+l,B − γU,e−1,B )]pθe,l,g≡where
αe,g′ = E[Yi,e+l − Yi,e−1 |Ei = e, gi = g ′ ], βU,g′ = E[Yi,e+l − Yi,e−1 |Ei ∈ U, gi = g ′ ],πe,g′ = E[Di,e+l − Di,e−1 |Ei = e, gi = g ′ ], γU,g′ = E[Di,e+l − Di,e−1 |Ei ∈ U, gi = g ′ ] (g ′ = A, B),andαe,t,g′ = E[Yi |Ei = e, Ti = t, gi = g ′ ], βU,t,g′ = E[Yi |Ei ∈ U, Ti = t, gi = g ′ ],πe,t,g′ = E[Di |Ei = e, Ti = t, gi = g ′ ], γU,t,g′ = E[Di |Ei ∈ U, Ti = t, gi = g ′ ] (g ′ = A, B, t = e + l, e − 1).
p
In panel data settings, our triple DID-IV estimator is the sample analog of θe,l,g
and has thefollowing influence function:pψi,e,l,g=1(ζi,e,A − ζi,e,B − ζi,U,A + ζi,U,B ),p
DIDe,l,gpppwhere DIDe,l,g= πe,A − πe,B − [γU,A − γU,B ], δi,e,l,g= (Yi,e+l − Yi,e−1 ) − θe,l,g· (Di,e+l − Di,e−1 ),
and
 p

 p

p
p
1e,g′ · δi,e,l,g− E[δi,e,l,g|Ei = e, gi = g ′ ]1U,g′ · δi,e,l,g− E[δi,e,l,g|Ei ∈ U, gi = g ′ ]ζi,e,g′ =, ζi,U,g′ =.
E[1e,g′ ]E[1U,g′ ]In repeated cross section data settings, our triple DID-IV estimator is the sample analog ofr
θe,l,gand has the following influence function:rψi,e,l,g=1([ζi,e,e+l,A − ζi,e,e−1,A − ζi,e,e+l,B + ζi,e,e−1,B ] − [ζi,U,e+l,A − ζi,U,e−1,A − ζi,U,e+l,B + ζi,U,e−1,B ]),r
DIDe,l,g50

r= [(πe,e+l,A − πe,e−1,A ) − (πe,e+l,B − πe,e−l,B )] − [(γU,e+l,A − γU,e−1,A ) − (γU,e+l,B −where DIDe,l,grr
γU,e−1,B )], δi,e,l,g = Yi − θe,l,g· Di , and rr|Ei = e, Ti = t, gi = g ′ ]− E[δi,e,l,g
1e,t,g′ · δi,e,l,g
ζi,e,t,g′ =,E[1e,t,g′ ] rr|Ei ∈ U, Ti = t, gi = g ′ ]− E[δi,e,l,g
1U,t,g′ · δi,e,l,g
ζi,U,t,g′ =.
E[1U,t,g′ ]DDecomposing the TWFEIV estimand in Oreopoulos (2006)

In this appendix we quantify the bias terms in the TWFEIV estimand, arising from the badcomparisons in Oreopoulos (2006). Hereafter, let e = 1947 and U = 1957 denote England andNorth Ireland respectively, and let Ne,t denotes the sample size for England in cohort t. Let
Re,t denote the sample mean of random variable Ri,t in region e (e = 1947, 1957) and cohort t:
Ne,t

1 X
Re(i),t .
Re,t ≡
Ne,t iFirst, we decompose the TWFEIV estimator β̂IV as follows10 :P
Ne,t Ẑe,t [Ye,t − Ye,1946 − (YU,t − YU,1946 )]β̂IV = P t
t Ne,t Ẑe,t [De,t − De,1946 − (DU,t − DU,1946 )]P
Ne,t Ẑe,t [De,t − De,1946 − (DU,t − DU,1946 )] · W\
DIDe,t= t P,
t Ne,t Ẑe,t [De,t − De,1946 − (DU,t − DU,1946 )]where we define:[Ye,t − Ye,1946 − (YU,t − YU,1946 )]W\
DIDe,t ≡,[De,t − De,1946 − (DU,t − DU,1946 )]and Ẑe,t is the residuals from regressing Zi,t on the cohort and North Ireland fixed effects11 .
By the similar arguments in the proof of Theorem 4, one can show that in staggered DID-IV
designs, we have0(t < e) CLAT T(U− 1 ≥ t ≥ e)
p
e,t
(27)
W\
DIDe,t →−1
1
CAETe,t · CLAT Te,t − CAETU,t · CLAT TU,t(t ≥ U )
1
1
CAETe,t− CAETU,t
1= E[Di − Di∞ |Ti = t, Ei = e]. Similarly, we havewhere CAETe,t(t < e) 0p1
CAETe,t(U − 1 ≥ t ≥ e)
[De,t − De,1946 − (DU,t − DU,1946 )] →−
11
CAETe,t− CAETU,t(t ≥ U )10(28)

For the detailed calculation steps, see the proof of Lemma 7 in Miyaji (2024). In our decomposition, thereference period (t = 1) in the proof is t = 1946.
11
We can write Ẑi,t = Ẑe,t because Zi,t only varies across cohorts and regions.

51

Combining the result (27) with (28) and by the Slutsky’s theorem, we obtain the following
decomposition result for the TWFEIV estimand in Oreopoulos (2006):
X
X
1
2
βIV =
we,t
· CLAT Te,t +we,t· ∆e,t ,(29)
U −1≥t≥et≥U

where ∆e,t is:
1
1
CAETe,t· CLAT Te,t − CAETU,t· CLAT TU,t,
1
1
CAETe,t − CAETU,t1
2
and the weights we,tand we,t
are:

1
=
we,t

P
U −1≥t≥e1E[Ẑi,t |Ei = e] · ne,t · CAETe,t
,
P
1
1
1
E[Ẑi,t |Ei = e] · ne,t · CAETe,t+E[Ẑi,t |Ei = e] · ne,t · (CAETe,t− CAETU,t
)
t≥U

(30)
2
we,t
=

P
U −1≥t≥e11E[Ẑi,t |Ei = e] · ne,t · (CAETe,t− CAT TU,t
)
,
P
1
1
1
E[Ẑi,t |Ei = e] · ne,t · CAETe,t+E[Ẑi,t |Ei = e] · ne,t · (CAETe,t− CAETU,t
)
t≥U

(31)
where ne,t and E[Ẑi,t |Ei = e] represent the population share and population residuals forEngland in cohort t respectively.
In Oreopoulos (2006), we can only identify CLAT Te,t between 1947 and 1956 because thepolicy change occurred in England in 1947 and in North Ireland in 1957. This implies thateach ∆e,t in equation (29) is the bias term arising from the bad comparisons between 1957 and1965 performed by the TWFEIV regression.
Figure 4 plots the weight and the corresponding estimate for each CLAT Te,t and ∆e,t (bias
12term). The consistent estimators for each we,t
, we,t, CLAT Te,t and ∆e,t are constructed fromthe sample analogue, using equations (27) - (28).
Figure 4 shows that all the CLATTs are positive and positively weighted, whereas all thebias terms are positive and negatively weighted. This indicates that the TWFEIV estimand isnegatively biased in the setting of Oreopoulos (2006).

E

Comparing DID-IV to Fuzzy DID

In this appendix we compare DID-IV and Fuzzy DID proposed by de Chaisemartin and
D’Haultfœuille (2018) (henceforth, ”dCDH”). We assume that the reader has briefly readdCDH. We first explain how dCDH’s identifying assumptions are related to ours in this article.
We then point out the issues inherent in Fuzzy DID designs. First, we show that dCDH’s assumptions ex ante impose strong and asymmetric restrictions on treatment adoption behavior
across units between exposed and unexposed groups. Next, under these restrictions, we showthat dCDH’s target parameter, the SLATET, can be decomposed into a weighted average oftwo different causal parameters. At the end of this appendix, we also revisit the ”issue” pointed
out by dCDH regarding the use of the Wald-DID estimand, and show that while their argument
is correct, it is misguided.

52

Fig. 4. Decomposition result for the TWFEIV estimand in Oreopoulos (2006). Notes: The figure plots theestimated weights and the corresponding estimates for each CLAT Te,t and ∆e,t (bias term). The closed squares
are the weights and the corresponding estimates for each CLAT Te,t . The closed triangles are the weights andthe corresponding estimates for each ∆e,t (bias term).

E.1

Comparing dCDH’s identifying assumptions to ours

In this section, we investigate the detailed connections between dCDH’s identifying assumptions
and ours. Because dCDH consider the repeated cross section settings, when we compare theidentifying assumptions between the two papers, we will refer to Assumptions 14-18 in thisarticle. For now, we ignore the difference in the definition of target parameter between dCDH
and this article.
dCDH consider the following identification assumptions for the Wald-DID estimand to capture their target parameter, the SLATET12 . We note that in dCDH, a group variable G plays
the role of instrument Z in our notation13 . In the following, we therefore replace G with Z andcall the groups Z = 1 and Z = 0 exposed and unexposed groups, respectively.14 For the detail
explanations for each assumption, see dCDH.
Assumption 24 (Fuzzy design).
E[D|Z = 1, T = 1] > E[D|Z = 1, T = 0],
E[D|Z = 1, T = 1] − E[D|Z = 1, T = 0] > E[D|Z = 0, T = 1] − E[D|Z = 0, T = 0].

(32)
(33)

Assumption 25 (Stable percentage of treated units in an unexposed group).
0 < E[D|Z = 0, T = 1] = E[D|Z = 0, T = 0] < 1.
12

In repeated cross section settings, the formal definition is provided in Assumption 29.
This follows from two observations in dCDH. First, dCDH call the groups G = 1 and G = 0 treatment andcontrol groups, respectively. Second, the group variable G is included in Assumption 26 (Treatment participation
equation).
14
Note that in Appendix B.2 in this article, we construct the group variable E from the instrument path Z
in order to uncover Assumption 16 (No anticipation in the first stage), which is the hidden assumption in theprevious literature.
13

53

Assumption 26 (Treatment participation equation).
D = 1{V ≥ vZT }, with V ⊥⊥ T |Z.
Assumption 27 (Parallel Trends assumption in the untreated outcome).
E[Y (0)|Z = 1, T = 1] − E[Y (0)|Z = 1, T = 0] = E[Y (0)|Z = 0, T = 1] − E[Y (0)|Z = 0, T = 0].
Assumption 28 (Stable treatment effect over time).
E[Y (1) − Y (0)|Z, T = 1, D0 (Z) = 1] = E[Y (1) − Y (0)|Z, T = 0, D0 (Z) = 1].
In Assumption 28, we modify the dCDH’s notation D(t) in order to ease its interpretation:
we define Dt (Z) = 1{V ≥ vZt } to be the treatment status under time T = t in group Z insteadof defining it as D(t).
We now state the relationships between dCDH’s assumptions and ours. We first explain
the similarities. First, both dCDH and this article impose the condition (33) in Assumption 24(Fuzzy design), as Assumptions 15-17 in this article imply this condition15 .
Next, the treatment participation equation in Assumption 26 corresponds to Assumption 15(Monotonicity) in this article. The equivalence between the treatment participation equationand the potential treatment choices framework with Assumption 15 (Monotonicity) follows
from the result of Vytlacil (2002). Here, we point out that dCDH implicitly assume the sharp
assignment of the instrument Z in their proofs: they assume v10 = v00 in Assumption 26,
that is, they assume that the thresholds in the treatment participation equation are the same
between exposed and unexposed groups in period 0.
Finally, dCDH implicitly impose Assumption 14 (Exclusion Restriction) and Assumption 16(No anticipation in the first stage) in this article when they formalize potential outcomes andtreatment participation equations. Specifically, dCDH do not introduce the instrument pathin their framework and define potential outcomes as Y (D), which implies Assumption 14. As
one can see in Assumption 26, dCDH assume that the treatment participation equation only
depends on the current instrument status, which implies Assumption 16 since dCDH assume
the sharp assignment of the instrument: v10 = v00 .
We next describe the differences between dCDH’s assumptions and ours. First, dCDH
assume the parallel trends assumption in the untreated outcome (Assumption 27), whereas we
assume the parallel trends assumption in the unexposed outcome. Second, dCDH assume thestable treatment rate assumption in an unexposed group (Assumption 25), whereas we assume
the parallel trends assumption in the treatment between exposed and unexposed groups. Third,dCDH impose the independence assumption between unobserved heterogeneity V and time
variable T given Z in Assumption 26, whereas we do not impose such restriction. Forth, dCDH
argue that the Wald-DID estimand requires the stable treatment effect assumption during thetwo periods (Assumption 28) to capture the SLATET, whereas we do not require such restrictionin order for this estimand to identify the LATET. Finally, dCDH assume the condition (32)in Assumption 24 (Fuzzy design), which requires that the treatment rate in an exposed groupincreases between the two periods, whereas we do not assume this condition.
15

From Assumptions 15-17, we have:
E[D|E = 1, T = 1] − [D|E = 1, T = 0] − (E[D|E = 0, T = 1] − E[D|E = 0, T = 0])=E[D1 ((0, 1)) − D1 ((0, 0))|E = 1, T = 1]
=P r(CM Z |E = 1, T = 1) > 0.

54

Remark E.1.1. When Assumption 25 is violated, dCDH consider the following assumption inorder for the Wald-DID estimand to capture the SLATET.
Assumption 29 (Homogeneous treatment effect between exposed and unexposed groups).
SLAT ET = SLAT ET ′ ,where we define16 :SLAT ET = E[Y (1) − Y (0)|Z = 1, T = 1, D1 (1) > D0 (0)],SLAT ET ′ = E[Y (1) − Y (0)|Z = 0, T = 1, D1 (0) ̸= D0 (0)].
This assumption requires that the treatment effects among the switchers should be thesame between exposed and unexposed groups, which dCDH call the ”homogeneous” treatment
effect assumption. In Appendix E.4, we present the decomposition result for the SLATET,
and show that we cannot straightforwardly interpret this assumption as requiring the ”homogeneous” treatment effect between the two groups. In the following discussion, we therefore
treat Assumptions 24-28 as dCDH’s main identifying assumptions.
E.2

Strong and asymmetric restrictions in Fuzzy DID designs

In this section, we show that dCDH’s identifying assumptions implicitly impose strong andasymmetric restrictions on treatment adoption behavior across units between exposed andunexposed groups. First, we prove some lemmas implied by dCDH’s assumptions. Based onthese lemmas, we then create the tables which present all the types in exposed and unexposedgroups under Fuzzy DID designs. These tables show that dCDH’s assumptions ex-ante exclude
many types in both groups and these restrictions are heavily assigned on an unexposed group.
At the end of this section, we provide the empirical implication of the distinction between
dCDH’s restrictions and ours in DID-IV designs.
First, we show that Assumption 26 (Treatment Participation equation) implies the following
assumption.
Assumption 30 (Monotone change in treatment in exposed and unexposed groups). For allz ∈ {0, 1},
P r(D0 (z) ≥ D1 (z)|Z = z) = 1 or P r(D0 (z) ≤ D1 (z)|Z = z) = 1
holds.
Here, recall that we define Dt (Z) = 1{V ≥ vZt } to be the treatment status under T = t ingroup Z.
Lemma 1. Assumption 26 implies Assumption 30.
Proof. Fix z ∈ {0, 1}. Then we have vz1 ≤ vz0 or vz1 ≥ vz0 .
Therefore, conditioning Z = z, we haveD1 (z) = 1{V ≥ vz1 } ≤ D0 (z) = 1{V ≥ vz0 } a.s. or D1 (z) = 1{V ≥ vz1 } ≥ D0 (z) = 1{V ≥ vz0 } a.s.
because we assume that the unobserved heterogeneity V is independent of time variable T
conditional on the instrument Z.
Completing the proof.
dCDH denote SLATET and SLATET’ as ∆ and ∆′ respectively. When we define the SLATET, we use
D0 (0) = D0 (1), which follows from the sharp assignment of the instrument: v10 = v00 .
16

55

Lemma 1 shows that in Fuzzy DID designs, the treatment status changes between period
0 and period 1 in a monotone (uniform) way in exposed and unexposed groups, respectively.
We note that the treatment participation equation itself does not imply Assumption 30: theindependence between the unobserved heterogeneity V and time variable T given Z yields thisassumption. Indeed, in this article, we do not assume this restriction.
As we have seen in section 2.4 in this article, time also plays the role of instrument in DID-IV
settings. From this observation, we can view that in an unexposed group (z = 0), Assumption
30 corresponds to a monotonicity assumption with respect to time, formally defined below.
Assumption 31 (Monotonicity Assumption w.r.t. time in an unexposed group).
P r(D0 (0) ≤ D1 (0)|Z = 0) or P r(D0 (0) ≥ D1 (0)|Z = 0).
Assumption 31 requires that time affects the treatment adoption process from period 0 toperiod 1 in a monotone (uniform) way in an unexposed group z = 0. In terms of the notation
introduced in section 2.4 in this article, this assumption implies that the group variable GT cantake three values with non-zero probability. Hereafter, we consider the type of Assumption 31
which rules out the existence of the time-defiers DF T in an unexposed group.
Next, we show that dCDH’s assumptions imply that there are no time compliers CM T andtime defiers DF T in an unexposed group (z = 0).
Lemma 2. Suppose Assumption 25, Assumption 26 and Assumption 31 hold. Then, there areno time compliers CM T and time defiers DF T in an unexposed group (z = 0).
Proof. Without loss of generality, suppose that Assumption 31 excludes the time defiers DF T
in an unexposed group (z = 0).
Then, Assumption 25 implies:
E[D|T = 1, Z = 0] = E[D|T = 0, Z = 0]⇐⇒ P r(D1 (0) > D0 (0)|Z = 0) = 0⇐⇒ P r(CM T |Z = 0) = 0(34)

The first equivalence follows from V ⊥⊥ T |Z in Assumption 26. Equation (34) implies that thereTare no time comliers CM in an unexposed group (z = 0).
Finally, we show that the condition (32) in Assumption 24 (Fuzzy design) and Assumption
26 imply that in an exposed group (z = 1), there are no units switching from treatment to nontreatment between period 0 and period 1. In other words, in Assumption 30, we should have:
P r(D0 (1) ≤ D1 (1)|Z = 1) = 1.
Lemma 3. The condition (32) in Assumption 24 and Assumption 26 imply P r(D0 (1) ≤D1 (1)|Z = 1)=1.
Proof. From the condition (32) in Assumption 24, we have
E[D|Z = 1, T = 1] > E[D|Z = 1, T = 0]⇐⇒ E[D1 (1) − D0 (1)|Z = 1] > 0⇐⇒ P r(D1 (1) > D0 (1)|Z = 1) − P r(D0 (1) > D1 (1)|Z = 1) > 0,(35)

where the first equivalence follows from V ⊥⊥ T |Z in Assumption 26. Recall that Assumption
26 implies Assumption 30 from Lemma 1. Suppose that P r(D0 (1) ≥ D1 (1)|Z = 1) = 1 holds.
Then, we have P r(D1 (1) > D0 (1)|Z = 1) = 0. This contradicts with the condition (35).
56

Table 9. Exposed group (z = 1)

observed
D0 (0) or D1 (1)D0 (0) = 1, D1 (1) = 1
D0 (0) = 1, D1 (1) = 0
D0 (0) = 0, D1 (1) = 1
D0 (0) = 0, D1 (1) = 0

counterfactual
D1 (0) = 1
AT Z ∧ AT T
DF Z ∧ AT T
AT Z ∧ CM T
DF Z ∧ CM T

D1 (0) = 0
CM Z ∧ DF T
N T Z ∧ DF T
CM Z ∧ N T T
NT Z ∧ NT T

Table 10. Unexposed group (z = 0)

observed
D0 (0) or D1 (0)D0 (0) = 1, D1 (0) = 1
D0 (0) = 1, D1 (0) = 0
D0 (0) = 0, D1 (0) = 1
D0 (0) = 0, D1 (0) = 0

counterfactual
D1 (1) = 1
AT Z ∧ AT T
CM Z ∧ DF T
AT Z ∧ CM T
CM Z ∧ N T T

D1 (1) = 0
DF Z ∧ AT T
N T Z ∧ DF T
DF Z ∧ CM T
NT Z ∧ NT T

We now clarify how dCDH’s identifying assumptions restrict the treatment adoption behavior across units in exposed and unexposed groups, respectively. Tables 9 - 10 show that theiridentifying assumptions exclude many types in both groups and the restrictions are heavily
imposed on an unexposed group17 : there exist five and three types in exposed and unexposedgroups respectively, where the types painted in gray color are excluded in both groups.
The distinction between dCDH’s restrictions and ours is apparent when we compare Tables
9 - 10 to Table 1 - 2 in this article18 : in both groups, we only exclude the defiers DF Z by
Assumption 15 (Monotonicity), whereas dCDH additionally exclude the type N T Z ∧ DF T in
an exposed group by Lemma 3, and additionally exclude the time defiers DF T and the timecompliers CM T in an unexposed group by Lemma 2.
These differences between dCDH’s restrictions and ours seem critical in many empiricalsettings: unlike the monotonicity assumption, which eliminate the compliers CM Z in bothgroups, dCDH’s additional restrictions seem difficult to assess from the institutional knowledge
in a given application, thus the practitioners may want to avoid imposing these restrictions in
empirical work. For instance, in some cases, we may have no valid reason for excluding thespecific type N T Z ∧ DF T in an exposed group, who are not affected by instrument but affectedby time. Similarly, in other cases, we may have no justification to exclude the time defiers
DF T and the time compliers CM T in an unexposed group because of the steady growth of thetreatment rate.
Although these restrictions in dCDH seem strong, one might argue that each assumption,such as the condition (32) in Assumption 24 and Assumption 25 (Stable percentage of treatedunits in an unexposed group), can be justifiable in certain applications. However, these assumptions give rise to two additional issues. First, when we impose the condition (32) in Assumption
17

In both tables, we can only observe either D0 (z) or D1 (z) in group z as we consider repeated cross section
settings.
18
We note that Tables 1-2 in this article is constructed under panel data settings, but the types represented
in these tables remain consistent even when considering repeated cross section settings. The only modificationis that as in Tables 9-10, one can only observe either D0 (z) or D1 (z) for unit i in group z in each table.

57

24, we should test the plausibility of this condition from the data in practice because this condition excludes the case that the treatment rate in an exposed group is stable during the two
periods: E[D|Z = 1, T = 1] = E[D|Z = 1, T = 0]. Although dCDH argue that ”Assumption
1 (Assumption 24 in this article) is just a way to define the treatment and the control group(exposed and unexposed group in this article) in our fuzzy setting”, they do not explain how
we should proceed when this condition is violated in practice.
Second, when we impose Assumption 25, we should find or estimate the groups whose treatment rates are stable over time. Although dCDH propose the two-step estimation method when
we should estimate the stable treatment group from the data, its performance and feasibility
is not clear, especially when we have multiple periods and multiple groups.
E.3

Decomposing the SLATETIn the previous section, we investigate how dCDH’s identifying assumptions ex-ante restrict
the treatment adoption behavior across units between exposed and unexposed groups. In thissection, under these restrictions, we show that dCDH’s target parameter, the SLATET, can be
decomposed into a weighted average of two different causal parameters.
The following theorem presents the decomposition result for the SLATET under Fuzzy DID
designs, and clarifies the difference between dCDH’s target parameter (SLATET) and ours
(LATET).
Theorem 7. Suppose Assumptions 24 - 28 hold. Then, we can decompose the SLATET into
two different causal parameters:
SLAT ET ≡ E[Y (1) − Y (0)|Z = 1, T = 1, D1 (1) > D0 (0)]= E[Y (1) − Y (0)|Z = 1, T = 1, CM T ]P r(CM T |Z = 1, SW )+ E[Y (1) − Y (0)|Z = 1, T = 1, CM Z ∧ N T T ]P r(CM Z ∧ N T T |Z = 1, SW ), (36)where the switcher (SW) in an exposed group (Z = 1) is the units who become treated in timeT = 1.
Proof. The proof directly follows from Table 9 in an exposed group.
Theorem 7 shows that we can decompose the SLATET into a weighted average of two
different causal parameters under Fuzzy DID designs: one parameter measures the treatment
effects among the time compliers CM T in an exposed group and the other parameter measures
the treatment effects among the type (CM Z ∧ N T T ) in an exposed group.
This theorem has two concerning implications. First, the interpretation of the SLATET
is less clear than that of the LATET because it consists of two different causal parameters.
Although the SLATET indeed captures the ”local” average treatment effect, it may be difficult
to interpret economically in a given application because one of the two causal parameters
captures the treatment effects, for those who are induced to treatment by time.
Second, the SLATET may not be policy-relevant even when the researchers exploit thepolicy change of their interest as an instrument for treatment. Suppose that the instrument
represents the important policy lever for researchers, and they are intrinsically interested in
the treatment effects among the compliers CM Z in an exposed group. In this situation, ourtarget parameter, the LATET, is a policy-relevant parameter by construction. On the other
hand, the SLATET only captures the treatment effects among the type (CM Z ∧ N T T ), whichis the sub-population of the compliers CM Z , even when the proportion of the time compliers
CM T is zero within that group. As the fraction of the time compliers CM T increases in that58

Table 11. Unexposed group (z = 0)

observed
D0 (0) or D1 (0)D0 (0) = 1, D1 (0) = 1
D0 (0) = 1, D1 (0) = 0
D0 (0) = 0, D1 (0) = 1
D0 (0) = 0, D1 (0) = 0

counterfactual
D1 (1) = 1
AT Z ∧ AT T
CM Z ∧ DF T
AT Z ∧ CM T
CM Z ∧ N T T

D1 (1) = 0
DF Z ∧ AT T
N T Z ∧ DF T
DF Z ∧ CM T
NT Z ∧ NT T

group, the SLATET puts more weight on the treatment effects among the time compliers, whichcontaminates the interpretation of the magnitude of this parameter even in such policy-relevant
contexts.
Using the decomposition result for the SLATET, we finally clarify the interpretation ofAssumption 29. When Assumption 25 (Stable percentage of treated units in an unexposedgroup) is violated, dCDH additionally consider Assumption 29 in order for the Wald-DID
estimand to identify the SLATET, and call this the ”homogeneous” treatment effect assumption
between exposed and unexposed groups.
We show that this assumption can not be interpreted as requiring the ”homogeneous”
treatment effect among the same sub-population between exposed and unexposed groups. To
do so, we first note that if we do not assume Assumption 25, we have Table 11 in an unexposedgroup instead of Table 10 in Appendix E.2. Here, we assume that Assumption 26 and 31
exclude the defiers DF Z and the time defiers DF T in an unexposed group, respectively.
Then, from Table 11, we can interpret the SLATET’ (see Assumption 29) as the treatment
effects among the time compliers in an unexposed group in period 1:
SLAT ET ′ ≡ E[Y (1) − Y (0)|Z = 0, T = 1, D1 (0) ̸= D0 (0)]= E[Y (1) − Y (0)|Z = 0, T = 1, CM T ].

(37)

By combining equations (36) and (37), we can conclude that Assumption 29 (ST AT ET =SLAT ET ′ ) does not require the homogeneous treatment effects in the same sub-population
between the two groups. Rather, this assumption requires that a weighted average of thetreatment effects among the time compliers CM T and the type (CM Z ∧ N T T ) in an exposedgroup should be equal to the treatment effect among the time compliers CM T in an unexposedgroup. This interpretation implies that the requirement of the ”homogeneous” treatment effectin Assumption 29 is less clear than one might expect.
E.4

Revisiting the ”issue” regarding the use of the Wald-DID estimand

Finally, we revisit the ”issue” raised by dCDH regarding the use of the Wald-DID estimand in
Fuzzy DID designs, and show that while their argument is correct, it is misguided. During this
discussion, we also clarify why dCDH exclude so many types in exposed and unexposed groups
as we see in Appendix E.2. Hereafter, we assume Assumptions 24 - 28 in Fuzzy DID designs.
dCDH argue that the Wald-DID estimand requires Assumption 28 (stable treatment effectover time) in order to identify the SLATET, and propose alternative estimands that do not relyon this assumption. We first show that their argument stems from their reliance on the parallel
trends assumption in the untreated outcome, which is common in DID designs, instead of on
the parallel trends assumption in the unexposed outcome as in this article. We next argue thatthe former type of parallel trends assumption is unsuitable for DID-IV settings.
59

First, we clarify the interpretation of Assumption 28 by introducing the additional notation.
This assumption is actually conditional on D0 (Z) = 1 in addition to Z and T , but dCDH do
not provide the reason why this strong restriction is required only for the sub-population. For
each time group g t , let wgt ,z = P r(GT = g t |Z = z) denote the population share conditionalon group Z = z, and let wgt ,z,D0 (0)=1 = P r(GT = g t |Z = z, D0 (0) = 1) denote the population
share conditional on D0 (0) = 1 in addition to group Z = z. Additionally, let δz,t,gt = E[Y (1) −Y (0)|Z = z, T = t, GT = g t ] denote the average treatment effect conditional on group Z = z,time T = t, and time group GT = g t .
Then, from Table 9 and Table 10, we can decompose Assumption 28 in the following:
E[Y (1) − Y (0)|Z = 0, T = 1, D0 (0) = 1] = E[Y (1) − Y (0)|Z = 0, T = 0, D0 (0) = 1]⇐⇒ δ0,1,AT T = δ0,0,AT T ,(38)
E[Y (1) − Y (0)|Z = 1, T = 1, D0 (1) = 1] = E[Y (1) − Y (0)|Z = 1, T = 0, D0 (1) = 1]⇐⇒ δ1,1,AT T · wAT T ,1,D0 (0)=1 + δ1,1,DF T · wDF T ,1,D0 (0)=1=δ1,0,AT T · wAT T ,1,D0 (0)=1 + δ1,0,DF T · wDF T ,1,D0 (0)=1 ,(39)
where we use the Law of Iterated Expectation, D0 (0) = D0 (1) (implied by the sharp assignmentof the instrument), and V ⊥⊥ T |Z in Assumption 26. Equation (38) shows that in an unexposedgroup (z = 0), Assumption 28 requires the stable treatment effect in the time always-takers
AT T . Equation (39) shows that in an exposed group (z = 1), this assumption requires thata weighted average of the treatment effects among the time defiers DF T and the time always
takers AT T is stable during the two periods.
Conditions (38) and (39) are required for Fuzzy DID designs because dCDH rely on theparallel trends assumption in the untreated outcomes. In DID-IV settings, we can not observe
the average time trends of untreated potential outcomes for the time always takers AT T in an
unexposed group and the time always takers AT T and the time defiers DF T in an exposedgroup because they always adopt the treatment during the two periods (see Table 9 and Table
10). Therefore, if we assume the parallel trends assumption in the untreated outcomes, weshould recover them by using conditions (38) and (39).
To see this formally, we use our notation to briefly sketch the proof of dCDH on the WaldDID estimand identifying SLATET under fuzzy DID designs. First, consider the conditional
expectation E[Y |Z = 0, T = 1] − E[Y |Z = 0, T = 0], which appears in the numerator of the
Wald-DID estimand. We can decompose this quantity into two terms:
E[Y |Z = 0, T = 1] − E[Y |Z = 0, T = 0]=(δ0,1,AT T − δ0,0,AT T ) · wAT T ,0 + {E[Y (0)|Z = 0, T = 1] − E[Y (0)|Z = 0, T = 0]}.
The first term arises because we can not observe the average time trends of the untreatedpotential outcome for the time always-takers AT T in an unexposed group, and we should add
and subtract this quantity to construct the second term. The first term disappears if we assume
condition (38).
Similarly, one can decompose the conditional expectation E[Y |Z = 1, T = 1] − E[Y |Z =60

1, T = 0] as follows:
E[Y |Z = 1, T = 1] − E[Y |Z = 1, T = 0]n
= δ1,1,AT T · wAT T ,1,D0 (0)=1 + δ1,1,DF T · wDF T ,1,D0 (0)=1− δ1,0,AT T · wAT T ,1,D0 (0)=1 − δ1,0,DF T · wDF T ,1,D0 (0)=1o+{E[Y (0)|Z = 1, T = 1] − E[Y (0)|Z = 1, T = 0]}+E[Y (1) − Y (0)|SW, Z = 1, T = 1]P r(SW |Z = 1),
where the type SW (switcher) includes the units who switch from non treatment to treatment
during the two periods. The first term arises because we can not observe the average timetrends of the untreated potential outcome for the time always-takers AT T and the time nevertakers N T T in an exposed group, and we should add and subtract this quantity to construct
the second term. The first term disappears if we assume condition (39). Here, we note that
we do not require the stable treatment assumption for the time compliers CM T and the type
CM Z ∧ N T T in an exposed group: by adding and subtracting the expectation of the untreatedpotential outcome path for these types, we have the third term.
Then, by noticing that the denominator of the Wald-DID estimand identifies P r(SW |Z = 1)
under Assumption 25 and Assumption 26, the Wald-DID estimand captures the SLATET under
Assumption 27 (parallel trends assumption in the untreated outcome) and conditions (38) and(39). From the discussions so far, one can conclude that the parallel trends assumption in theuntreated outcome leads dCDH to impose conditions (38) and (39).
Here, we add few remarks to clarify why dCDH ex ante impose strong restrictions on
treatment adoption behavior across units in order for the Wald-DID estimand to identify the
SLATET. It turns out that this also stems from their reliance on the parallel trends assumption
in the untreated outcome.
Remark E.4.1. dCDH exclude the type N T Z ∧ DF T in an exposed group and the time defiers
DF T in an unexposed group because if we add and subtract the average time trends of theuntreated outcome for these types, we additionally identify the treatment effects among themin period 0 (not in period 1), as they adopt the treatment in period 0, but leave it in period
1 (see Tables 9-10). This identification result seems not intuitive because the identification
variation comes from the policy shock (instrument) in period 1.
Remark E.4.2. dCDH exclude the time compliers CM T in an unexposed group because if we
add and subtract the average time trends of the untreated outcome for that type, we additionallycapture the treatment effects among the time compliers CM T from the conditional expectation
E[Y |Z = 0, T = 1] − E[Y |Z = 0, T = 0], which implies that the SLATET in an exposed groupis offset by the SLATET’ in an unexposed group.
So far, we have confirmed that dCDH’s argument regarding the use of the Wald-DID estimand rests on the parallel trends assumption in the untreated outcome in DID designs. Finally,
we argue that this assumption is unsuitable for DID-IV settings for three reasons.
First, this assumption is not sufficient to capture the average time trends of the outcome
even in an unexposed group. This is because in DID-IV settings, the units are allowed to takethe treatment in the absence of the instrument, and we can not observe the untreated outcomes
for these types in an unexposed group.
Second, in most of the DID-IV applications, we can not impute the untreated potential
outcomes in general. For instance, Black et al. (2005) estimates the causal link between parents’61and children’s education attainment, exploiting variation in the timing of the implementationof the school reform across municipalities and cohorts as an instrument for parents’ education
attainment. In the author’s setting, the parallel trends assumption in the untreated outcome
requires the data to contain the parents with zero education attainment, which is unrealistic
and the authors would not have in mind in practice.
Finally, this assumption is generally not testable using the pre-exposed period data in agiven application. This seems apparent, as some units can already adopt the treatment before
period 0, and we can not compare the pretrends of the untreated outcome between exposed
and unexposed groups.
dCDH propose the placebo test in their appendix, but we show that it is incomplete forchecking the plausibility of the parallel trends assumption in the untreated outcome. dCDH’s
test consists of two steps. First, we test whether the share of treated units is zero in bothgroups from T = −1 to T = 0:
E[D|Z = 1, T = 0] − E[D|Z = 1, T = −1] = 0,
E[D|Z = 0, T = 0] − E[D|Z = 0, T = −1] = 0.

(40)
(41)

Second, we test the following null hypothesis:E[Y |Z = 1, T = 0] − E[Y |Z = 1, T = −1] = E[Y |Z = 0, T = 0] − E[Y |Z = 0, T = −1]. (42)
Although dCDH ”assume” the conditions (40) and (41), dCDH also note that when one of
the two conditions fails, the second test can ”no longer be used to test” Assumption 27. We,
therefore, describe the dCDH’s test in two steps.
dCDH’s test has some drawbacks. First, the conditions (40) and (41), which we should
check in the first step, are strong, but dCDH do not explain how we should proceed when these
conditions are violated in practice. Second, in this test, the second step does not directly test
Assumption 27 in the pre-exposed periods, as it does not compare the evolution of the mean
untreated outcome between exposed and unexposed group before period T = 0. Indeed, dCDH
describe the equality (42) as a necessary condition for Assumption 27 and Assumption 28 to besatisfied under the conditions (40) and (41). Finally, it is unclear how we should conduct thistest when we have multiple pre-exposed period data. dCDH assume ”for instance that data isavailable for the period T = −1”, but they do not indicate how we should perform this test in
multiple pre-exposed period settings.
Surprisingly, dCDH’s test corresponds to our pretrends test in section 5.3 if we replace theconditions (40)- (41) in the first step with the weaker one:
E[D|Z = 1, T = 0] − E[D|Z = 1, T = −1] = E[D|Z = 0, T = 0] − E[D|Z = 0, T = −1]. (43)
Under repeated cross section settings, one can figure out that the conditions (42) - (43) coincidewith the conditions (3) -(4) in this article.

62