# Transporting treatment effects from difference-in-differences studies

Audrey Renson1, Ellicott C. Matthay1, and Kara E. Rudolph2
1Department of Population Health, New York University Grossman School of
Medicine, New York, United States
2Department of Epidemiology, Mailman School of Public Health, Columbia
University, New York, United States

###### Abstract

Difference-in-differences (DID) is a popular approach to identify the causal
effects of treatments and policies in the presence of unmeasured confounding.
DID identifies the sample average treatment effect in the treated (SATT).
However, a goal of such research is often to inform decision-making in target
populations outside the treated sample. Transportability methods have been
developed to extend inferences from study samples to external target
populations; these methods have primarily been developed and applied in
settings where identification is based on conditional independence between the
treatment and potential outcomes, such as in a randomized trial. This paper
develops identification and estimators for effects in a target population,
based on DID conducted in a study sample that differs from the target
population. We present a range of assumptions under which one may identify
causal effects in the target population and employ causal diagrams to
illustrate these assumptions. In most realistic settings, results depend
critically on the assumption that any unmeasured confounders are not effect
measure modifiers on the scale of the effect of interest. We develop several
estimators of transported effects, including a doubly robust estimator based
on the efficient influence function. Simulation results support theoretical
properties of the proposed estimators. We discuss the potential application of
our approach to a study of the effects of a US federal smoke-free housing
policy, where the original study was conducted in New York City alone and the
goal is extend inferences to other US cities.

Keywords:  difference-in-differences, transportability, efficiency, causal
inference

##  1 Introduction

Difference-in-differences (DID) is a popular identification strategy when
studying the causal effects of large-scale social and economic policies [1,
2]. DID is appealing when: (i) randomization is not feasible, (ii) there is
variation across jurisdictions and over time in terms of whether a policy was
adopted, and (iii) not all variables that are confounders of the policy-
outcome relationship are measured, leading to concerns about confounding bias
[3]. By comparing pre- and post-policy outcomes in both the jurisdiction
implementing the policy and a comparable jurisdiction without the policy, and
making a so-called parallel trends assumption (i.e., that changes in average
potential outcomes over time are independent of policy adoption) [1, 4], DID
can identify the causal effect of the policy on the outcome, even in settings
where unmeasured variables would confound either (i) a pre-post analysis or
(ii) a post-policy comparison between the treated and untreated jurisdictions.

An important (often under-recognized) aspect of DID is that it identifies the
average treatment effect among the treated (ATT) in the post-policy period,
and not the average treatment effect (ATE) or other common parameters of
interest [1]. For example, the ATT in a study of a policy raising the minimum
wage is the effect of the policy on outcomes for the population living in the
jurisdiction(s) that actually raised the minimum wage, and not the population
living in all the jurisdictions in the study—those with and without the
policy. ATT estimates resulting from a DID analysis can be informative as to
whether to maintain or discontinue policies in those locations. However, a
major goal of DID research is often to inform policy decisions by governments
that have not yet adopted the policy of interest; in the minimum wage example,
it may be of interest to inform decisions by the federal government or states
with less generous minimum wage laws. Naïvely considering the estimated policy
effects to apply to untreated jurisdictions requires the additional, strong
assumption that there are no effect measure modifiers (measured or unmeasured)
whose distribution varies between the treated jurisdiction(s) under study and
the untreated jurisdiction(s) to which one wishes to make inferences [5, 6].
For example, such an extrapolation would be biased if effects of the minimum
wage differ by age, and age distributions differed across states.

Generalizability and transportability methods have been developed with the
goal of formally extending inferences made in one population to another
population in the presence of effect heterogeneity [7, 8, 9]. These methods
have mainly been applied in contexts where internal validity is established
based on an unconfoundedness assumption, typically achieved through a
randomized controlled trial (RCT). It is well-known that real-world RCTs can
deliver high internal validity, but that inferences from such studies apply
only to the people participating in the RCT, which may differ from the true
target population in terms of effects experienced. We define “target
population” to be the population to whom inference is desired, as dictated by
substantive concerns. For example, in RCTs of medical treatments, the target
population may be the population that should receive treatments in practice,
which may differ in important aspects from the individuals included in the
trial [10, 11]. Methods exist to quantitatively extend (i.e., transport or
generalize) effects estimated in RCTs to target populations other than the
included study sample, possibly alleviating the well-known tradeoff between
internal and external validity in such studies [12].

It is plausible that transportablity methods could be used to quantitatively
extend causal effects estimated from DID studies to target populations other
than the treated sample, possibly alleviating the well-known tradeoff between
internal and external validity in such DID studies as well. However, to our
knowledge, neither identification assumptions nor estimators for transporting
DID estimates have been addressed in the literature. DID presents special
challenges for transportability because of the presumed existence of
unmeasured confounders. Standard approaches to transportability assume that a
conditional average treatment effect is constant between the sample and target
population after conditioning on a measured set of covariates; if any
unmeasured confounders in a DID application are also effect measure modifiers
of the treatment-outcome relationship, then the existence of these unmeasured
confounders creates complexities in evaluating this condition which have not,
to our knowledge, been explored. Causal diagrams [13] may facilitate such an
exploration, as they have been essential in understanding assumptions for
identification of transported effects [14, 6, 9], but have seen limited use in
DID settings [4, 15]. This disconnect may be because causal diagrams generally
only capture nonparametric independence assumptions [13], whereas parallel
trends is a semiparametric assumption partially restricting the functional
form of the outcome distribution [16].

This paper develops a formal approach to identification and estimation of
effects in a target population, based on DID conducted in a study sample that
differs from the target population. This paper is framed as transportability
in the sense that we assume the study sample is not a subset of the target
population [17, 8], though our results can easily be extended to the case
where the study sample is nested within the target population. We employ
causal diagrams to understand the sampling mechanism (i.e, the model that
distinguishes the study sample from the target population), and show that our
results rely crucially on the assumption that unmeasured confounders are
either independent of the sampling process or are not effect modifiers on the
scale of the effect being estimated (in this paper, we focus on additive
effects such as the ATT and ATE, but our results can be generalized to non-
additive measures, such as risk ratios). Section 2 describes the observed data
and preliminary assumptions, Section 3 presents key identification results
linking the observed data in the sample to causal quantities in the target
population, and Section 4 presents estimators (including a doubly robust
estimator based on the efficient influence function) for these quantities,
which are illustrated using simulation in Section 5. Section 6 concludes.

##  2 Preliminaries

Suppose we observe data on the variables $W_{i},A_{i},Y_{i0}$, and $Y_{i1}$ in
a study sample containing $n$ individuals or units ($i=1,...,n$), where
$W_{i}$ are (possibly multivariate) baseline covariates measured just before
exposure, $A_{i}$ is a binary exposure, and $Y_{it}$ $(t=0,1)$ are outcomes
measured before ($t=0$) and after ($t=1$) exposure occurs. Hereafter, we drop
the $i$ subscript unless needed to resolve ambiguity. Suppose that the study
sample is not representative of the true target population of interest, and
that the latter contains $N$ individuals ($i=1,...,N$). We let $S=1$ denote
membership in the study sample and $S=0$ denote membership in the target
population. We assume that outcomes are only measured in the study sample, but
that treatment and covariates are measured in both the study sample and the
target population. Thus, the observed data take the form
$O=\\{S,A,W,Y_{0}S,Y_{1}S\\}.$ Throughout, we use $f(x|\cdot)$ to denote a
conditional density if $x$ is continuous and a conditional probability mass
function if $x$ is discrete. Caligraphic uppercase letters denote the support
of a random variable.

We use $Y_{t}(a)$ to denote a potential outcome, or the outcome that would
have occurred if exposure $A$ had been set by intervention to the value $a$.
We assume the following throughout:

######  Assumption 1.

(No interference) $Y_{it}(a_{i},a_{i^{\prime}})=Y_{it}(a_{i})$ for $i\neq
i^{\prime}$, with $i,i^{\prime}$ such that
$\\{S_{i},S_{i^{\prime}}\\}\in\\{0,1\\}^{2}$

######  Assumption 2.

(Treatment version irrelevance) If $A_{i}=a$, then $Y_{it}=Y_{it}(a)$ with
$i,i^{\prime}$ such that $\\{S_{i},S_{i^{\prime}}\\}\in\\{0,1\\}^{2}$

Assumptions 1 and 2 are standard in the causal inference and transportability
literature and are not specific to the DID setting. Assumption 1 requires that
one unit’s treatment does not impact another unit’s potential outcome in
either the sample or the target. Assumption 2 requires that treatments are
sufficiently well-defined that observed outcomes can stand in for potential
outcomes under treatment with the observed exposures, and that versions of the
treatment do not differ between the sample and target. Assumptions 1 and 2 are
often referred to together as the stable unit treatment value assumption
(SUTVA).

###  2.1 Difference-in-differences in the study sample

Here, we give a brief review of causal identification based on DID, which we
will assume is the basis of identification in the study sample. Specifically,
we invoke the following assumptions, standard in the DID literature [18, 19,
1]:

######  Assumption 3.

(No anticipation): $Y_{0}(a)=Y_{0}$ for $a=0,1$

######  Assumption 4.

(Positivity of treatment assignment) If $f(w|S=1)>0$ then $f(A=0|W=w,S=1)>0$
with probability 1 for all $w\in\mathcal{W}$

######  Assumption 5.

(Parallel Trends): For $w\in\mathcal{W}$:

$\mathbb{E}\\{Y_{t}(0)-Y_{t-1}(0)|A=1,S=1,W=w\\}=\mathbb{E}\\{Y_{t}(0)-Y_{t-1}(0)|A=0,S=1,W=w\\}$

Assumption 3 states that future treatment does not impact the prior outcomes
(this assumption can also be relaxed to allow anticipation up to a known time
period [20]). It is well known that under Assumptions 1-5, it is possible to
identify the $W$-conditional SATT, defined as
$\eta(w)\equiv\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W=w,A=1,S=1].$ Specifically, under
Assumptions 1-5 we have:

$\displaystyle\eta(w)$
$\displaystyle=\mathbb{E}[Y_{1}-Y_{0}|W=w,A=1,S=1]-\mathbb{E}[Y_{1}-Y_{0}|W=w,A=0,S=1]$
(1) $\displaystyle\equiv m_{1}(w)-m_{0}(w),$

where we define $m_{a}(w)=\mathbb{E}[Y_{1}-Y_{0}|W=w,A=a,S=1]$. By extension,
the unconditional sample ATT (abbreviated SATT, usually the focal parameter in
DID) is identified as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|A=1,S=1]=\mathbb{E}[m_{1}(W)-m_{0}(W)|A=1,S=1].$
However, and importantly for our discussion, Assumptions 1-5 are not
sufficient to identify parameters unconditional on $A=1$, such as the sample
average treatment effect (SATE), defined as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|S=1].$ This is because parallel trends provides
information about potential outcomes only among the treated group; without
further assumptions there is no basis for identification of potential outcomes
for the group $A=0$. Moreover, and as is the focus of this paper, additional
assumptions would be required to identify effects outside the study sample,
since parallel trends and positivity of treatment assignment are conditional
on $S=1$.

##  3 Identification of transported treatment effects

In this section we consider the task of equating a causal estimand (i.e., one
specified in terms of potential outcomes) in the target population to a
function of the distribution of the observed data, $O$. Specifically, we focus
on the population average treatment effect in the treated (PATT), defined as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|A=1,S=0]$, and the population average treatment
effect (PATE) defined as $\mathbb{E}[Y_{1}(1)-Y_{1}(0)|S=0]$. We begin by
introducing a motivating example, after which we introduce and discuss a set
of sufficient identifying assumptions, and present identifying formulas which
equal each causal estimand if the assumptions are true.

###  3.1 Motivating example

As of July 30, 2018, a US Department of Housing and Urban Development (HUD)
rule required all public housing authorities to implement smoke-free housing
(SFH) policies banning smoking in residences. As a motivating example,
consider the question, what effect did the federal SFH policy have on air
quality in US public housing developments? To answer this question, we
consider transporting the results from a study conducted in public housing
buildings in New York City (NYC) only. Specifically, a team of investigators
conducted air quality monitoring in living rooms and common areas of NYC
public housing buildings, both before the federal policy went into effect
(from April to July 2018), and again approximately every six months for 3
years post-policy. A DID analysis was conducted to estimate the effect of the
policy on indoor air nicotine (among other measures), using as a comparison
group a sample of households receiving housing assistance through a program
known as Section 8, a public subsidy to supplement rental costs in private
sector buildings [21]. Air quality was sampled in stairwells, hallways, and
living rooms; for simplicity here we focus on stairwells. Because of concerns
about systematic variation in outdoor air quality between building types, the
investigators adjusted for outdoor ambient PM2.5 in their DID estimates. (We
note that in the original study, building inclusion criteria were high-rise
[$>$15 floors], large resident population [$>$150 units], at least 80% Black
or Hispanic residents, and at least 20% younger than 18 years; for simplicity
we ignore these criteria here.)

In this example, $Y_{t}$ is a continuous variable representing log-transformed
air nicotine in stairwells (where we let $t=0$ denote April-July 2018 and
$t=1$ denote April-September 2021), $A=1$ denotes residence in a public
housing building, $A=0$ denotes residence in a Section 8 household, $S=1$
denotes residence in NYC, $S=0$ denotes residence outside of NYC, and $W$ is a
continuous variable capturing outdoor ambient PM2.5. Thus, if Assumptions 1-5
hold (along with correct model specification and no measurement error), the
DID results in this study may be interpreted as estimates of the effect of the
SFH policy on indoor air quality for NYC public housing residents only. Though
the study is informative as to the effect of the policy in NYC, it is also of
interest to federal policymakers to estimate the PATT, which here represents
the effect of the HUD rule on air nicotine in April-September 2021 in public
housing in the US outside of NYC ($S=0$). Moreover, it may also be of interest
to assess the PATE, which here represents the effect of a hypothetical policy
covering both public housing and Section 8 housing. Importantly, the estimates
in this study cannot be interpreted as estimates of the PATT or PATE without
additional assumptions.

###  3.2 Naïve approach

We begin with an approach to transportability that does not take into account
the causal structure of DID (in particular, does not take into account
unmeasured confounding), after which we will use causal diagrams to illustrate
why this approach will usually fail. Since all identified potential outcomes
in equation (1) are conditional on $A=1$, an obvious starting point in
attempting to transport effects identified through DID is to identify the
PATT. Inspecting equation (1), a natural approach may be to assume that the
$W$-conditional SATTs (conditional on each value of $w$) are equal between the
sample and the target. If this were the case, one could identify the PATT
using the following expression:

$\displaystyle\mathbb{E}[Y_{1}^{1}-Y_{1}^{0}|A=1,S=0]$
$\displaystyle=\mathbb{E}[\mathbb{E}(Y_{1}^{1}-Y_{1}^{0}|W,A=1,S=1)|A=1,S=0]$
$\displaystyle=\mathbb{E}[m_{1}(W)-m_{0}(W)|A=1,S=0]$ (2)

Specifically, in order for equation (2) to hold, the following assumptions
would be sufficient:

######  Assumption 6.

(Exchangeability of selection) $Y_{t}(a)\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}S|W,A=1$

######  Assumption 7.

(Positivity of selection) If $f(w|A=1,S=0)>0$ then $f(S=1|W=w,A=1)>0$ with
probability 1 for all $w\in\mathcal{W}$

Assumption 6 states that, among the treated group, the distributions of
potential outcomes in the sample and target are equal after conditioning on
$W$. Assumption 7 states that any covariate values that may occur in the
target treated group must also be possible in the sample treated group.
Assumptions 6 and 7 together imply that the $W$-conditional ATT is constant
across settings, and hence that the PATT is identified by equation (2).

Though Assumption 6 is similar to the exchangeability of selection assumption
usually invoked for transportability of the average treatment effect (ATE), it
differs importantly in that it must hold conditional on $A=1.$ This is so
because DID was the basis for identification in the sample, so any effects
identified in the sample (whether SATT or $W$-conditional SATT) are
conditional on $A=1$, and the basis for transportability is therefore the
constancy of the $W$-conditional SATTs (not SATEs) across settings. This
constancy is dependent on replacing potential outcomes in the treated target
with those in the treated sample, and for this replacement to be licensed,
Assumption 6 must condition on $A=1$.

Unfortunately, conditioning on $A=1$ means Assumption 6 is unlikely to hold in
most DID applications. To illustrate this point, Figure 1(a) displays a single
world intervention graph (SWIG) depicting a common DID setting. SWIGs are
similar to causal directed acyclic graphs (DAGs) in that nodes represent
random variables, directed arrows represent direct effects, and conditional
independencies are given by d-separation rules [22]. SWIGs extend DAGs by
depicting interventions on variables as split nodes ($A|a$ in Figure 1(a)
indicates intervening to set $A=a$), and any variables affected by the
intervention variable become potential outcomes under that intervention.
Figure 1(a) represents a standard DID scenario in the sense that $U$
represents unmeasured common causes of $A$ and $Y_{1}$ that would confound a
cross-sectional comparison, and whose existence motivates the use of DID. In
Figure 1(b), we add $S$ with arrows into $A$ and $W$, depicting the assumption
that distributions of these variables differ across settings. Following the
convention of selection diagrams, arrows emanating from $S$ represent
“exogenous conditions that determine the values of the variables to which they
point” [14]. Assumption 6 would not be expected to hold in Figure 1(b) due to
the existence of the path $S\rightarrow A\leftarrow U\rightarrow Y_{1}(a)$, on
which $A$ is a collider. Thus, this path is opened by conditioning on $A$ (and
not closed by conditioning on $W$), rendering $S$ potentially associated with
$Y_{1}(a)$ conditional on $\\{W,A=1\\}$. For the same reason, $S$ would also
be associated with $Y_{0}$ conditional on $\\{W,A=1\\}$ in at least one data
distribution consistent with the SWIG. Importantly, such paths will be present
whenever (i) there is unmeasured confounding, and (ii) the target and sample
differ in the distribution of treatment (conditional on $W$). We expect (i) to
always be the case (otherwise DID would be unnecessary). We also expect (ii)
to be the case except in rare circumstances such as when $A$ is experimentally
assigned in both the target and the sample. Importantly, this failure of
Assumption 6 occurs regardless of whether the unmeasured confounders $U$
differ marginally in distribution between the target and sample (i.e., whether
or not there is an arrow from $S$ into $U$ in Figure 1(b)).

$U$$A$$|a$W$Y_{0}$$Y_{1}(a)$ (a)

$U$$A$$|a$W$Y_{0}$$Y_{1}(a)$$S$ (b)

Figure 1: Single world intervention graphs (SWIGs) illustrating common
scenarios relevant for (a) DID in a sample and (b) transportability of DID
results to a target population. Double-headed arrows indicate unmeasured
common causes between two nodes.

###  3.3 Identification via restrictions on effect heterogeneity

The analysis in the previous subsection illustrated that identification of
transported effects based on exchangeability according to measured covariates
(as in Assumption 6) is unlikely to be tenable in DID studies, since
conditioning on $A=1$ will typically cause unmeasured covariates $U$ to be
associated with the sampling mechanism $S$ regardless of whether this
association exists marginally. Thus, Assumption 6 would likely only be
plausible if $U$ were included in the conditioning event, but this would not
aid identification since $U$ is unmeasured. Fortunately, it is possible to
identify transported effects when variables needed for exchangeability are
unmeasured, so long as those variables are not also effect measure modifiers
on the scale on which the causal effects are being measured, which we
illustrate here.

We begin by expressing the concept that unmeasured confounders $U$ drive our
decision to use DID by stating the following Assumptions, which relate only to
identification in the sample:

######  Assumption 8.

(Latent exchangeability of treatment) $Y_{t}(a)\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}A|W,U,S=1$ for $t\in\\{0,1\\}$ and
$a\in\\{0,1\\}$

######  Assumption 9.

(Latent positivity of treatment) If $f(u,w|S=1)>0$ then $f(A=a|U=u,W=w,S=1)>0$
with probability 1 for $a\in\\{0,1\\}$ and
$\\{u,w\\}\in\\{\mathcal{U},\mathcal{W}\\}$

In a sense, Assumption 8 does not introduce any new restrictions because one
can define $U$ to be whatever variables (known or unknown) confound the cross-
sectional association between $A$ and $Y_{t}$ and which motivate the use of
DID in the first place. In contrast, Assumption 9 may be restrictive; the
requirement that unmeasured confounding variables $U$ (known or unknown) have
overlapping distribution between the treated and untreated may not hold in
some settings and is not necessary for identification of the SATT via DID. (As
an aside, it can be shown that parallel trends will hold if (i) Assumptions 9
and 8 hold and (ii) $U$ exerts a constant effect on $Y_{0}$ and $Y_{1}$ on the
additive scale within levels of $W$ among the treated [4]. However, in this
paper we assume parallel trends to hold and do not consider what conditions
render it plausible or not.) Next consider the follow assumptions aimed at
identification in the target:

######  Assumption 10.

(Latent exchangeability of selection) $Y_{t}(a)\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}S|W,U,A$ for $t\in\\{0,1\\}$ and
$a\in\\{0,1\\}$

######  Assumption 11.

(Latent positivity of selection) If $f(u,w|A=a,S=0)>0$ then
$f(S=1|U=u,W=w,A=a)>0$ with probability 1 for $a\in\\{0,1\\}$ and
$\\{u,w\\}\in\\{\mathcal{U},\mathcal{W}\\}$

Assumption 10 modifies Assumption 6 by allowing for $U$ in the conditioning
event, so that the potential outcomes are equal in distribution between the
sample and the target after conditioning on $W$, $U$, and $A$. Similarly,
Assumption 11 requires all possible values of both $U$ and $W$ in the target
population to also be possible in the sample. In addition to conditioning on
$U$, Assumptions 10 and 11 modify Assumption 6 and 7 by requiring their
respective conditions for both the treated and untreated, not just the
treated. We can similarly assess Assumption 10 graphically: if (as is the case
in Figure 1(a)) the variables $\\{W,U,A\\}$ d-separate $S$ from $Y_{0}$ and
$S$ from $Y_{1}(a)$, then Assumption 10 holds.

Because $U$ is unmeasured, Assumptions 10 and 11 are insufficient for
transportability; they render effects conditional on $\\{W,U,A\\}$ constant
across settings, but these effects are not themselves identifiable. However,
transportability is still possible if $U$ is not an additive effect measure
modifier, which we state as follows:

######  Assumption 12.

(U-homogeneity)
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|U,W,S,A]=\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,S,A]$

Note that Assumption 12 does not require that $U$ not be a confounder, only
that the treatment effect does not vary across levels of $U$ on the additive
scale. Note also the scale-dependence of Assumption 12; for example, it cannot
hold for both log-transformed $Y_{t}$ and $Y_{t}$ on its natural scale, unless
there is no effect of treatment or $U$ is unassociated with $Y_{t}$. The fact
that Assumption 12 refers to the additive scale follows the fact that our
focus is on additive treatment effects; if effects on an alternate scale (such
as risk ratios) were of interest, then Assumption 12 would need to be
reformulated to express treatment effect homogeneity on that scale. If effects
on the additive scale are homogeneous with respect to $U$, then additive
effects conditional on $\\{W,U,A\\}$ (which are constant across settings by
Assumptions 10 and 11) do not depend on $U$, yielding identification of the
PATT. This is stated in the following theorem:

######  Theorem 1.

(Transportability for difference-in-differences) Under Assumptions 1-5 and
10-12, the PATT is identified as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|A=1,S=0]=\mathbb{E}[m_{1}(W)-m_{0}(W)|A=1,S=0]$.
Moreover, if Assumptions 8 and 9 also hold, then the identification for the
PATE is given as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|S=0]=\mathbb{E}[m_{1}(W)-m_{0}(W)|S=0]$, and for
the population average treatment effect in the untreated (PATU) as
$\mathbb{E}[Y_{1}(1)-Y_{1}(0)|A=0,S=0]=\mathbb{E}[m_{1}(W)-m_{0}(W)|A=0,S=0]$.

The proof of Theorem 1 is provided in Appendix A.1. Importantly, Theorem 1
gives identifying formulas for the PATT as well as the PATE and PATU. Notably,
Assumptions 8-9 are only required for identification of the PATE and PATU, not
the PATT. This is an important distinction, particularly because one of the
key advantages of DID is that identification can hold without having to assume
positivity for the unmeasured confounders. As an aside, the addition of
Assumptions 8 and 12 to the standard identifying assumptions for DID (in our
exposition, Assumptions 1-5) also renders identifiable the SATE and the sample
average treatment effect in the untreated (SATU) (shown in Appendix A.2).
These results are intuitive: under latent exchangeability of selection, the
treatment effects in the population are weighted averages of the
$\\{W,U,A\\}-$conditional treatment effects in the sample; these conditional
effects do not depend on $U$ under $U$-homogeneity. Moreover, because $U$
represents all unmeasured confounders, differences between the $W$-conditional
SATT, SATE, and SATU can only be caused by effect heterogeneity according to
$U$, which has been ruled out by Assumption 12. Therefore the $W$-conditional
SATT, SATE, and SATU all equal one another.

Assumptions 8-12 are not the only set of assumptions that yield identification
of effects in the target when $U$ is related to the sampling mechanism, but
alternative assumption sets will generally also place restrictions on
unmeasured effect heterogeneity. For example, supposing that Assumptions 10-11
hold, it is possible to identify the PATT under a parallel trends assumption
for both the treated and untreated counterfactual regimes (i.e., if we added
to Assumption 5 an equivalent expression replacing $Y_{t}(0)$ and $Y_{t-1}(0)$
with $Y_{t}(1)$ and $Y_{t-1}(1)$). However, this stronger parallel trends
assumption also implies the $W$-conditional SATT, SATE, and SATU are all equal
[20], implying effect homogeneity according to $U$.

Assumption |  Meaning in application
---|---
1 (No interference) |  Nicotine levels in one building are not affected by SFH policies in other buildings
2 (Treatment version irrelevance) |  Variation in SFH implementation/enforcement do not affect air nicotine
3 (No anticipation) |  Individuals did not change their behavior in anticipation of SFH
4 (Positivity of treatment assignment) |  There are Section 8 buildings at all levels of outdoor PM2.5 seen among NYCHA buildings
5 (Parallel trends) |  In absence of the SFH policy, at a given level of outdoor PM2.5, absolute changes in log-transformed air nicotine levels over time would have been equal between NYCHA and Section 8 buildings
6 (Exchangeability of selection) |  Among public housing buildings nationally, at a given level of outdoor PM2.5, the distribution of potential nicotine levels is equal between NYC and the rest of the USA
7 (Positivity of selection) |  There are NYCHA buildings at all levels of PM2.5 seen outside public housing buildings nationally
8 (Latent exchangeability of treatment) |  In NYC only, at a given level of outdoor PM2.5 and ventilation, potential air nicotine distributions are independent of Section 8 vs. NYCHA
9 (Latent positivity of treatment) |  There are both NYCHA and Section 8 buildings at all levels of outdoor PM2.5 and ventilation seen in the study sample
10 (Latent exchangeability of selection) |  Among public housing buildings nationally, at a given level of outdoor PM2.5 and ventilation, the distribution of potential nicotine levels is equal between NYC and the rest of the USA
11 (Latent positivity of selection) |  There are NYCHA buildings at all levels of outdoor PM2.5 and ventilation seen for public housing buildings nationally
12 (U-homogeneity) |  Building ventilation is not an additive effect measure modifier after conditioning on outdoor PM2.5 and indicators of NYC vs. remaining USA and Section 8 vs. public housing.
Table 1: Interpretation of assumptions in the motivating example. Recall that
in the example, $A$ denotes residence in public housing vs. Section 8 (and
hence exposure to the smoke-free housing policy vs. not); $Y_{t}$ denotes log-
transformed air nicotine in stairwells; $W$ denotes outdoor ambient PM2.5; $S$
denotes residence in NYC vs. the remaining US; and $U$ denotes building
ventilation (and possibly other unmeasured confounders).

###  3.4 Application

Table 1 provides interpretations of each of the 12 Assumptions presented in
terms of the applied question. In particular, $U$ represents unmeasured
differences between public housing and Section 8 that impact levels of air
nicotine independently of the treatment, leading investigators to pursue a DID
design. For example, $U$ may represent ventilation (with $U=1$ denoting high
and $U=0$ denoting low ventilation); we expect public housing building to more
often have low ventilation and that ventilation impacts air nicotine, but
ventilation was not measured in the study. In Figure 1(b), arrows from $S$
into $W$ and $A$ depict measured environmental and societal conditions that
lead to differing air quality and differing distributions of public housing
vs. Section 8 residence across regions in the US. Since $Y_{t}$ was log-
transformed, Assumption 12 requires that for buildings with the same levels of
outdoor PM2.5 and separately for public housing and Section 8, the additive
effect of a smoke-free housing policy on log-transformed air nicotine (and
hence a type of mulitplicative effect) is constant for buildings with high and
low ventilation. Thus, Assumption 12 would be violated if high- and low-
ventilation buildings had differing baseline levels of air nicotine and the
effect of a smoke-free housing policy was to decrease air nicotine by a
constant absolute amount (e.g., a constant reduction in parts per million).

##  4 Estimators

In the section, we presume identification holds according to one of the sets
of assumptions presented Theorem 1, and consider the problem of estimating the
statistical parameter

$\psi(a^{*})=\mathbb{E}[\eta(W)|A=a^{*},S=0],a^{*}=0,1.$

(See equation (1) for the definition of $\eta(\cdot)$.) From Theorem 1, we
have that under Assumptions 1-5 and 10-12, $\psi(1)$ equals the PATT; with the
addition of Assumptions 8-9, $\psi(0)$ equals the PATU and $E[\psi(A)|S=0]$
equals the PATE. To simplify notation in this section, let $\Delta
Y=Y_{1}-Y_{0}$ denote differenced outcomes, $m_{a}(W)=\mathbb{E}[\Delta
Y|W,S=1,A=a]$ denote the true outcome-difference model, and
$g_{a,s}(W)=f(A=a,S=s|W)$, denote the true propensity scores for treatment
assignment and selection. We use $\widehat{m}_{a}$ and $\widehat{g}_{a,s}$ to
denote estimators of those quantities, which may or may not be correctly
specified. A correctly specified model is one that converges in probability to
the true population moments. We also use
$P_{n}\\{h(O)\\}=n^{-1}\sum_{i=1}^{n}h(O_{i})$ to denote the sample average of
a function $h(\cdot)$ of the observed data.

###  4.1 G-computation estimator

A g-computation estimator (also called a substitution estimator or plug-in
estimator) is constructed by plugging in estimators of the empirical
counterparts of the population quantities into the identifying formula in
Theorem 1:

$\displaystyle\widehat{\psi}_{gcomp}(a^{*})$
$\displaystyle=P_{n}\bigg{\\{}\frac{I(A=a^{*},S=0)}{P_{n}\\{I(A=a^{*},S=0)\\}}\\{\widehat{m}_{1}(W)-\widehat{m}_{0}(W)\\}\bigg{\\}}$

The estimator $\widehat{\psi}_{gcomp}$ will be consistent and asymptotically
normal if $\widehat{m}_{a}$ is correctly parametrically specified, but not
necessarily otherwise.

###  4.2 Inverse-odds weighted estimator

Instead, one may have more information about the functional form of the
propensity scores. The following inverse-odds weighted estimator will be
consistent and asymptotically normal if $\widehat{g}_{a,s}$ are correctly
parametrically specified, but not necessarily otherwise:

$\displaystyle\widehat{\psi}_{iow}(a^{*})$
$\displaystyle=P_{n}\bigg{\\{}\bigg{[}\frac{I(A=a^{*},S=1)\widehat{g}_{a^{*},0}(W)}{P_{n}\\{I(A=a^{*},S=0)\\}\widehat{g}_{1,1}(W)}-\frac{I(A=0,S=1)\widehat{g}_{a^{*},0}(W)}{P_{n}\\{I(A=a^{*},S=0)\\}\widehat{g}_{0,1}(W)}\bigg{]}\Delta
Y\bigg{\\}}$

###  4.3 Doubly robust estimator

Lastly, we provide a doubly robust estimator, meaning in this case that the
estimator is consistent and asymptotically normal if either
$\widehat{g}_{a,s}$ or $\widehat{m}_{a}$ consistent of correctly-specified
parametric models; it need not be the case that both are correct. A doubly
robust estimator for $\psi$ is given by:

$\displaystyle\widehat{\psi}_{dr}(a^{*})$
$\displaystyle=P_{n}\bigg{\\{}\frac{I(A=a^{*},S=1)\widehat{g}_{a^{*},0}(W)}{P_{n}I(A=a^{*},S=0)\widehat{g}_{1,1}(W)}\\{\Delta
Y-\widehat{m}_{1}(W)\\}-\frac{I(A=0,S=1)\widehat{g}_{1,0}(W)}{P_{n}I(A=a^{*},S=0)\widehat{g}_{0,1}(W_{i})}\\{\Delta
Y-\widehat{m}_{0}(W)\\}$
$\displaystyle\quad\quad+\frac{I(A=a^{*},S=0)}{P_{n}I(A=a^{*},S=0)}\\{\widehat{m}_{1}(W)-\widehat{m}_{0}(W)\\}\bigg{\\}}$

In Appendix B, we show the derivation of $\widehat{\psi}_{dr}(a^{*})$ as a
“one-step” estimator based on the efficient influence function for
$\psi(a^{*})$, which implies that $\widehat{\psi}_{dr}(a^{*})$ is
asymptotically efficient. The fact that $\widehat{\psi}_{dr}(a^{*})$
corresponds to the efficient influence function also leads to an estimator of
the asymptotic variance under the assumption that $\widehat{g}_{a,s}$ and
$\widehat{m}_{a}$ are both correctly specified, which we also provide in
Appendix B. In Appendix C, the double robust property of
$\widehat{\psi}_{dr}(a^{*})$ is demonstrated, and proof of the consistency of
the g-computation and IOW estimators are provided as a bi-product of the
double robust property. Code to implement the proposed estimators is available
at `https://github.com/audreyrenson/did_generalizability`.

##  5 Simulation study

We generated $nsims=200$ datasets of $nobs=10,000$ each, according to the
following data generating mechanism:

$\displaystyle S$ $\displaystyle\sim Bernoulli(0.5)$ $\displaystyle U$
$\displaystyle\sim Bernoulli(logit^{-1}[-1+S])$ $\displaystyle W$
$\displaystyle\sim Bernoulli(0.5-0.25S)$ $\displaystyle A$ $\displaystyle\sim
Bernoulli(0.3+0.1S+0.1W+0.1U)$ $\displaystyle Y_{0}$ $\displaystyle\sim
N(1+W+U,0.1)$ $\displaystyle Y_{1}$ $\displaystyle\sim N(0.5W+U+A+0.5WA,0.1)$

To see that parallel trends holds in the simulation, note that for $a=0,1$:

$\displaystyle\mathbb{E}[Y_{1}(0)-Y_{0}(0)|A=a,S=1,W]$
$\displaystyle=\mathbb{E}\\{[0.5W+U+(0)+0.5W(0)]-[1+W+U]|A=a,S=1,W\\}$
$\displaystyle=\mathbb{E}\\{[0.5W-1-W]|A=a,S=1,W\\}$ $\displaystyle=-1-0.5W$

We applied each of the three proposed estimators for the PATT to each dataset
with all models correctly specified, all models incorrectly specified, only
outcomes models misspecified, and both selection and treatment models
misspecified. We treated $U$ as an unmeasured variable in all analysis. For
correctly specified models, all variables except $U$ were included with the
above functional form, in misspecified outcome models we only include main
terms for W and A, and in misspecified propensity models we dropped terms for
S. The true PATT$=1.28$ was calculated by generating potential outcomes for 1
million observations. Results shown in Figure 2 illustrate that IOW is biased
whenever the propensity score for treatment and selection is misspecified,
g-compuation is biased whenever the outcome model is misspecified, and that
the doubly robust estimator is approximately unbiased if either model is
correct. Code to implement the simulation is available at
`https://github.com/audreyrenson/did_generalizability`.

Figure 2: Results of each estimator applied to $nsims=200$ simulated datasets
of $nobs=10,000$ each. $bfal$ indicates all models misspecified, $qfal$ only
outcomes models misspecified, $gfal$ both selection and treatment models
misspecified, and $true$ all models correctly specified.

##  6 Discussion

This paper introduced an approach to estimating treatment effects in a target
population based on DID conducted in a study sample that differs from the
target population. Under certain assumptions, some of which may be understood
with the aid of causal diagrams, we can identify the PATT, PATE, and PATU. We
also propose several estimators of the aforementioned effects in the target
population that only require measurement of covariates and/or treatments in
the target population, not necessarily outcomes. This approach may be useful
when, as is the case in our motivating example involving air nicotine,
measurement of outcomes in the target population (in this case, the entire
U.S.) may not be feasible, and unobserved confounding is present (in this
case, ventilation) but those unobserved confounders do not modify the additive
treatment effect. Though our approach assumed the same set of covariates were
sufficient for internal and external validity, the methods can easily be
adapted to settings where the covariates needed for external validity are a
subset of those needed for internal validity. Though our approach has been
framed around the problem of transportability (i.e., the study sample is not a
subset of target population), our methods can easily be adapted to
generalizability problems (when the study sample is nested in the target
population). The approach may therefore also prove useful when a select group
of jurisdictions (such as states or provinces) implement a policy, but
decisions need to made a higher level of organization (such as national
governments).

It is important to note that our motivating example was greatly simplified for
illustrative purposes; a full analysis to address the motivating question
would likely be more complex. For example, one would need to carefully
consider how the exclusion criteria may impact the plausibility of
assumptions, whether other covariates would need to be measured, and whether
differences in building management between public housing in NYC and other
areas might violate treatment version irrelevance.

Causal diagrams have rarely been employed to understand identification in DID
designs, but have been essential for elucidating the way causal structure
impacts generalizability and transportability problems. By employing causal
diagrams, we highlighted that the causal structure implied by unmeasured
confounding that often motivates DID creates particular complexities for
generalizability and transportability. Specifically, we were able to identify
transported treatment effects under an assumption that the unmeasured
confounders are not additive effect measure modifiers, but not necessarily
otherwise.

The validity of an assumption that unmeasured confounders are not additive
effect measure modifiers may be difficult to assess in practice. In our
example, we possess no a priori substantive information to suggest that the
additive effect of a smoking ban on log-transformed air nicotine would be
constant according to the building’s level of ventilation (a presumed
confounder). This suggests that, when transportability is of interest in DID
studies, investigators should measure and adjust for as many potential
confounders as possible (even if not formally needed for parallel trends) in
order to reduce the number of variables for which we must make homogeneity
assumptions. Future work will seek to develop bounds under violations of
effect homogeneity along with methods to assess the sensitivity of conclusions
to this key assumption.

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##  Appendix A Proof of identification results

###  A.1 Proof of Theorem 1

First we show identification for the PATT:

$\displaystyle\mathbb{E}[Y_{1}(1)$ $\displaystyle-
Y_{1}(0)|A=1,S=0]=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=1,S=0]|A=1,S=0\\}$
(iterated expectation)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=1,S=1]|A=1,S=0\\}$
(Assumptions 1, 2, 10 & 11)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,A=1,S=1]|A=1,S=0\\}$
(Assumption 12) $\displaystyle=\mathbb{E}(m_{1}(W)-m_{0}(W)|A=1,S=0)$
(Assumptions 1-5)

Next consider identification of the PATU:

$\displaystyle\mathbb{E}[Y_{1}(1)$ $\displaystyle-
Y_{1}(0)|A=0,S=0]=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=0,S=0]|A=0,S=0\\}$
(iterated expectation)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=0,S=1]|A=0,S=0\\}$
(Assumptions 1, 2, 10 & 11)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=1,S=1]|A=0,S=0\\}$
(Assumptions 1, 2, 8 & 9)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,A=1,S=1]|A=0,S=0\\}$
(Assumption 12) $\displaystyle=\mathbb{E}(m_{1}(W)-m_{0}(W)|A=0,S=0)$
(Assumptions 1-5)

Having identified the PATU and the PATT, the PATE is trivially identified:

$\displaystyle\mathbb{E}[Y_{1}(1)-Y_{1}(0)|S=0]$
$\displaystyle=\mathbb{E}[\mathbb{E}(Y_{1}(1)-Y_{1}(0)|A,S=0)|S=0]$
$\displaystyle=\mathbb{E}[\mathbb{E}(m_{1}(W)-m_{0}(W)|A,S=0)|S=0]$
$\displaystyle=\mathbb{E}[m_{1}(W)-m_{0}(W)|S=0]$

###  A.2 Identifying the SATE and SATU under additional assumptions

Under Assumptions 8, 9, and 12, the SATE is identified as

$\displaystyle\mathbb{E}[Y_{1}(1)$ $\displaystyle-
Y_{1}(0)|S=1]=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,S=1]|S=1\\}$
(iterated expectation)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=1,S=1]|S=1\\}$
(Assumptions 8 & 9)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,A=1,S=1]|S=1\\}$
(Assumption 12) $\displaystyle=\mathbb{E}\\{m_{1}(W)-m_{0}(W)|S=1\\}$
$\displaystyle\quad\text{(Assumptions \ref{asn:noint}-\ref{asn:pt})},$

and the SATU is identified as:

$\displaystyle\mathbb{E}[Y_{1}(1)$ $\displaystyle-
Y_{1}(0)|A=0,S=1]=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=0,S=1]|A=0,S=1\\}$
(iterated expectation)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,U,A=1,S=1]|A=0,S=1\\}$
(Assumptions 8 & 9)
$\displaystyle=\mathbb{E}\\{\mathbb{E}[Y_{1}(1)-Y_{1}(0)|W,A=1,S=1]|A=0,S=1\\}$
(Assumption 12) $\displaystyle=\mathbb{E}\\{m_{1}(W)-m_{0}(W)|A=0,S=1\\}$
(Assumptions 1-5)

##  Appendix B Efficient influence function for transported treatment effects

To ease notation, we let $\Delta Y=Y_{1}-Y_{0}.$ We let
$P_{n}\\{h(O)\\}=n^{-1}\sum_{i=1}^{n}h(O_{i})$ denote the sample mean of a
function $h(\cdot)$ of the observed data $O$, $P$ dnote the true distribution
of the observed data, and $\widehat{P}_{n}$ denote an estimator of the
observed data distribution (which may or may not be the empirical
distribution). Here we focus on the statistical estimand

$\displaystyle\psi(a^{*},P)$
$\displaystyle=\mathbb{E}[m_{1}(W)-m_{0}(W)|A=a^{*},S=0]\\}$
$\displaystyle=\int[m_{1}(z)-m_{0}(w)]f(w|A=a^{*},S=0)dw$

where we write $\psi(a^{*},P)$ as a function of $P$ to emphasize that it
depends on the true observed data distribution.

###  B.1 Proof of EIF

######  Theorem 2.

The efficient influence function for $\psi(a^{*})$ is given by

$\displaystyle D(a^{*},O_{i},P)$
$\displaystyle=\frac{I(A_{i}=1,S_{i}=1)g_{a^{*},0}(W_{i})}{f(A=a^{*},S=0)g_{1,1}(W_{i})}\\{\Delta
Y_{i}-m_{1}(W_{i})\\}-\frac{I(A_{i}=0,S_{i}=1)g_{a^{*},0}(W_{i})}{f(A=a^{*},S=0)g_{0,1}(W_{i})}\\{\Delta
Y_{i}-m_{0}(W_{i})\\}$
$\displaystyle\quad\quad+\frac{I(A_{i}=a^{*},S_{i}=0)}{f(A=a^{*},S=0)}\\{m_{1}(W_{i})-m_{0}(W_{i})\\}-\psi(a^{*})$

###### Proof.

NOTE: this proof is somewhat non-rigorous because it appears at times to rely
on $W$ being discrete and other times continuous. Plan is to re-rewrite using
the approach of Hines et al. [23].

$\displaystyle IF\\{\psi(a^{*},P)\\}$
$\displaystyle=\int\bigg{(}IF\\{m_{1}(w)\\}-IF\\{m_{0}(w)\\}\bigg{)}f(w|A=a^{*},S=0)dw+\int\\{m_{1}(W)-m_{0}(w)\\}IF\\{f(w|A=a^{*},S=0)\\}dw$
$\displaystyle=\int\frac{I(A=1,S=1,W=w)}{f(A=1,S=1,W=w)}[\Delta
Y-m_{1}(w)]f(w|A=a^{*},S=0)dw$
$\displaystyle\quad-\int\frac{I(A=0,S=1,W=w)}{f(A=0,S=1,W=w)}[\Delta
Y-m_{0}(w)]f(w|A=a^{*},S=0)dw$
$\displaystyle\quad+\int\\{m_{1}(w)-m_{0}(w)\\}\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\\{I(W=w)-f(w|A=a^{*},S=0)\\}dw$
$\displaystyle=\frac{I(A=1,S=1)g_{a^{*},0}(W)}{f(A=a^{*},S=0)g_{1,1}(W)}[\Delta
Y-m_{1}(W)]-\frac{I(A=0,S=1)g_{a^{*},0}(W)}{f(A=a^{*},S=0)g_{0,1}(W)}[\Delta
Y-m_{0}(W)]$
$\displaystyle\quad+\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}[m_{1}(W)-m_{0}(W)]-\int\\{m_{1}(w)-m_{0}(w)\\}f(w|A=a^{*},S=0)dw$

where the first equality uses the fact that the efficient influence function
is a derivative and applies the product rule for derivatives, the second
substitutes known influence functions for conditional expectations and
conditional densities/probability mass functions, and the third rearranges. ∎

###  B.2 One-step estimator

Because the efficient influence function for $\psi(a^{*})$ is given by
$D(a^{*},O_{i},P)$, a one-step estimator [23] is given by

$\displaystyle\widehat{\psi}_{dr}(a^{*})$
$\displaystyle=\psi(a^{*},\widehat{P}_{n})-P_{n}\\{D(a^{*},O_{i},\widehat{P}_{n})\\}$
$\displaystyle=P_{n}\bigg{\\{}\frac{I(A=1,S=1)\widehat{g}_{a^{*},0}(W)}{P_{n}(I[A=a^{*},S=0])\widehat{g}_{1,1}(W)}\\{\Delta
Y-\widehat{m}_{1}(W)\\}-\frac{I(A=0,S=1)\widehat{g}_{a^{*},0}(W)}{P_{n}(I[A=a^{*},S=0])\widehat{g}_{0,1}(W)}\\{\Delta
Y-\widehat{m}_{0}(W)\\}$
$\displaystyle\quad\quad+\frac{I(A=a^{*},S=0)}{P_{n}(I[A=a^{*},S=0])}\\{\widehat{m}_{1}(W)-\widehat{m}_{0}(W)\\}\bigg{\\}}$

where $\widehat{P}_{n}=\\{\widehat{g}_{a,s},\widehat{m}_{a}\\}$ with
$\\{a,s\\}\in\\{0,1\\}^{2}.$ If $\widehat{P}_{n}$ consists of correctly-
specified parametric models, it follows by the central limit theorem that

$\sqrt{n}[\widehat{\psi}_{dr}(a^{*})-\psi(a^{*})]\xrightarrow{d}N(0,\mathbb{E}[D(a^{*},O,\widehat{P}_{n})^{2}])$

where $\xrightarrow{d}$ denotes convergence in distribution. Thus, an
estimator of the asymptotic variance that is consistent when $\widehat{P}_{n}$
consists of correctly-specified parametric models is given by

$\widehat{var}[\widehat{\psi}_{dr}(a^{*})]=P_{n}\\{D(a^{*},O,\widehat{P}_{n})^{2}\\}$

##  Appendix C Double robust property of $\widehat{\psi}_{dr}$

In this section, for ease of notation we let $m_{a}\equiv m_{a}(W)$ and
$g_{a,s}\equiv g_{a,s}(W)$. First, suppose
$\widehat{m}_{a}\xrightarrow{p}m_{a}^{*}$ and
$\widehat{g}_{a,s}\xrightarrow{p}g_{a,s}^{*}$, not necessarily assuming
$g_{a,s}=g_{a,s}^{*}$ or $m_{a}=m_{a}^{*}$. Using Slutzky’s theorem and
continuous mapping theorem we have

$\displaystyle\widehat{\psi}_{dr}(a^{*})$
$\displaystyle\xrightarrow{p}\psi^{*}(a^{*})\equiv\mathbb{E}\bigg{\\{}\frac{I(A=1,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{1,1}^{*}}\\{\Delta
Y-m_{1}^{*}\\}-\frac{I(A=0,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{0,1}^{*}}\\{\Delta
Y-m_{0}^{*}\\}$
$\displaystyle\quad\quad\quad+\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\\{m_{1}^{*}-m_{0}^{*}\\}\
\bigg{\\}}$

First consider the case where outcome models are correctly specified, so that
$m_{a}(w)=m_{a}^{*}(w)$ for all $w\in\mathcal{W}.$ By the linearity property
of expectations, we have

$\displaystyle\psi^{*}(a^{*})$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{I(A=1,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{1,1}^{*}}(\Delta
Y-m_{1}^{*})\bigg{\\}}$ (C.1)
$\displaystyle\quad\quad-\mathbb{E}\bigg{\\{}\frac{I(A=0,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{0,1}^{*}}(\Delta
Y-m_{0}^{*})\bigg{\\}}$ (C.2)
$\displaystyle\quad\quad+\mathbb{E}\bigg{\\{}\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}(m_{1}^{*}-m_{0}^{*})\bigg{\\}}$
(C.3)

Under $m_{a}=m_{a}^{*},$ we have

$\displaystyle(\ref{eq:dr1})$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{I(A=1,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{1,1}^{*}}(\mathbb{E}[\Delta
Y|A=1,S=1,W]-m_{1})\bigg{\\}}$ $\displaystyle=0$

Likewise, $(\ref{eq:dr2})=0.$ Therefore,
$\psi^{*}(a^{*})=\mathbb{E}\bigg{\\{}\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}(m_{1}-m_{0})\bigg{\\}}=\mathbb{E}[m_{1}-m_{0}|A=a^{*},S=0]=\psi(a^{*}).$
Moreover, because (C.3) is the probability limit of the g-computation
estimator, we have that
$\widehat{\psi}_{gcomp}(a^{*})\xrightarrow{p}\psi(a^{*})$ whenever
$\widehat{m}_{a}\xrightarrow{p}m_{a}.$

Next, consider the case where treatment and selection models are correctly
specified, so that $g_{a,s}(w)=g_{a,s}^{*}(w)$ for all $w\in\mathcal{W}$.
Rearranging we have

$\displaystyle\psi^{*}(a^{*})$
$\displaystyle=\mathbb{E}\bigg{\\{}\bigg{(}\frac{I(A=1,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{1,1}^{*}}-\frac{I(A=0,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{0,1}^{*}}\bigg{)}\Delta
Y\bigg{\\}}$ (C.4)
$\displaystyle\quad+\mathbb{E}\bigg{\\{}\bigg{(}\frac{I(A=0,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{0,1}^{*}}-\frac{I(A=1,S=0)}{f(A=a^{*},S=0)}\bigg{)}m_{0}^{*}\bigg{\\}}$
(C.5)
$\displaystyle\quad-\mathbb{E}\bigg{\\{}\bigg{(}\frac{I(A=1,S=1)g_{a^{*},0}^{*}}{f(A=a^{*},S=0)g_{1,1}^{*}}-\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\bigg{)}m_{1}^{*}\bigg{\\}}$
(C.6)

Since $g_{a,s}^{*}=g_{a,s}$, we have

$\displaystyle(\ref{eq:dr4})$
$\displaystyle=\mathbb{E}\bigg{\\{}\bigg{(}\frac{I(A=1,S=1)f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=1,S=1|W)}-\frac{I(A=0,S=1)f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=0,S=1|W)}\bigg{)}\Delta
Y\bigg{\\}}$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{I(A=1,S=1)f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=1,S=1|W)}m_{1}(W)-\frac{I(A=0,S=1)f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=0,S=1|W)}m_{0}(W)\bigg{\\}}$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{\mathbb{E}[I(A=1,S=1)|W]f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=1,S=1|W)}m_{1}(W)-\frac{E[I(A=0,S=1)|W]f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=0,S=1|W)}m_{0}(W)\bigg{\\}}$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)}[m_{1}(W)-m_{0}(W)]\bigg{\\}}$
$\displaystyle=\mathbb{E}\bigg{\\{}\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}[m_{1}(W)-m_{0}(W)]\bigg{\\}}$
$\displaystyle=\psi(a^{*})$ $\displaystyle(\ref{eq:dr5})$
$\displaystyle=\mathbb{E}\bigg{\\{}\bigg{(}\frac{\mathbb{E}[I(A=0,S=1)|W]f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)f(A=0,S=1|W)}-\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\bigg{)}m_{0}^{*}\bigg{\\}}$
$\displaystyle=\mathbb{E}\bigg{\\{}\bigg{(}\frac{f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)}-\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\bigg{)}m_{0}^{*}\bigg{\\}}$
$\displaystyle=0$

Likewise,
(C.6)=$\mathbb{E}\bigg{\\{}\bigg{(}\frac{f(A=a^{*},S=0|W)}{f(A=a^{*},S=0)}-\frac{I(A=a^{*},S=0)}{f(A=a^{*},S=0)}\bigg{)}m_{1}^{*}\bigg{\\}}=0.$
Thus if $\widehat{g}_{a,s}(w)\xrightarrow{p}g_{a,s}(w)$,
$\widehat{\psi}_{dr}(a^{*})\xrightarrow{p}\psi(a^{*}).$ Moreover, because
(C.4) is the probability limit of the IOW estimator, we have that
$\widehat{\psi}_{IOW}(a^{*})\xrightarrow{p}\psi(a^{*})$ whenever
$\widehat{g}_{a,s}\xrightarrow{p}g_{a,s}$.