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The Annals of Applied Statistics

2013, Vol. 7, No. 3, 1386–1420

DOI: 10.1214/13-AOAS630

©Institute of Mathematical Statistics, 2013

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL

INFERENCE USING BAYESIAN NONPARAMETRICS:

IMPLICATIONS FOR EVALUATING THE EFFECT OF

BREASTFEEDING ON CHILDREN’S

COGNITIVE OUTCOMES1

BYJENNIFER HILL AND YU-SUNG SU

New York University and Tsinghua University

Causal inference in observational studies typically requires making com-

parisons between groups that are dissimilar. For instance, researchers inves-

tigating the role of a prolonged duration of breastfeeding on child outcomes

may be forced to make comparisons between women with substantially dif-

ferent characteristics on average. In the extreme there may exist neighbor-

hoods of the covariate space where there are not sufﬁcient numbers of both

groups of women (those who breastfed for prolonged periods and those who

did not) to make inferences about those women. This is referred to as lack of

common support. Problems can arise when we try to estimate causal effects

for units that lack common support, thus we may want to avoid inference for

such units. If ignorability is satisﬁed with respect to a set of potential con-

founders, then identifying whether, or for which units, the common support

assumption holds is an empirical question. However, in the high-dimensional

covariate space often required to satisfy ignorability such identiﬁcation may

not be trivial. Existing methods used to address this problem often require

reliance on parametric assumptions and most, if not all, ignore the informa-

tion embedded in the response variable. We distinguish between the concepts

of “common support” and “common causal support.” We propose a new ap-

proach for identifying common causal support that addresses some of the

shortcomings of existing methods. We motivate and illustrate the approach

using data from the National Longitudinal Survey of Youth to estimate the

effect of breastfeeding at least nine months on reading and math achievement

scores at age ﬁve or six. We also evaluate the comparative performance of

this method in hypothetical examples and simulations where the true treat-

ment effect is known.

1. Introduction. Causal inference strategies in observational studies that as-

sume ignorability of the treatment assignment also typically require an assumption

of common support; that is, for binary treatment assignment, Z, and a vector of

confounding covariates, X, it is commonly assumed that 0 <Pr(Z =1|X)<1.

Failure to satisfy this assumption can lead to unresolvable imbalance for matching

Received August 2011; revised January 2013.

1Supported in part by the Institute of Education Sciences Grant R305D110037 and by the Wang

Xuelian Foundation.

Key words and phrases. Common support, overlap, BART, propensity scores, breastfeeding.

1386

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1387

methods, unstable weights in inverse-probability-of-treatment weighting (IPTW)

estimators, and undue reliance on model speciﬁcation in methods that model the

response surface.

To satisfy the common support assumption in practice, researchers have used

various strategies to identify (and excise) observations in neighborhoods of the co-

variate space where there exist only treatment units (no controls) or only control

units (no treated) [see, e.g., Heckman, Ichimura and Todd (1997)]. Unfortunately

many of these methods rely on correct speciﬁcation of a model for the treatment

assignment. Moreover, all such strategies (that we have identiﬁed) fail to take ad-

vantage of the outcome variable, Y, which can provide critical information about

the relative importance of each potential confounder. In the extreme this informa-

tion could help us discriminate between situations where overlap is lacking for a

variable that is a true confounder versus situations when it is lacking for a variable

that is not predictive of the outcome (and thus not a true confounder). Moreover,

there is currently a lack of guidance regarding how the researcher can or should

characterize how the inferential sample has changed after units have been dis-

carded.

In this paper we propose a strategy to address the problem of identifying units

that lack common support, even in fairly high-dimensional space. We start by

deﬁning the causal inference setting and estimands of interest ignoring the com-

mon support issue. We then review a causal inference strategy [discussed previ-

ously in Hill (2011)] that exploits an algorithm called Bayesian Additive Regres-

sion Trees [BART; Chipman, George and McCulloch (2007, 2010)]. We discuss

the issue of common support and then introduce the concept of “common causal

support.”

Our method for addressing common support problems exploits a key feature of

the BART approach to causal inference. When BART is used to estimate causal

effects one of the “byproducts” is that it yields individual-speciﬁc posterior distri-

butions for each potential outcome; these act as proxies for the amount of infor-

mation we have about these outcomes. Comparisons of posterior distributions of

counterfactual outcomes versus factual (observed) outcomes can be used to create

red ﬂags when the amount of information about the counterfactual outcome for

a given observation is not sufﬁcient to warrant making inferences about that ob-

servation. We illustrate this method in several simple hypothetical examples and

examine the performance of our strategy relative to propensity-based methods in

simulations. Finally, we demonstrate the practical differences in our breastfeeding

example.

2. Causal inference and BART. This section describes notation, estimands,

and assumptions followed by a discussion of how BART can be used to estimate

causal effects.2

2Green and Kern (2012) discuss extensions to this BART strategy for causal inference to more

thoroughly explore heterogeneous treatment effects.

1388 J. HILL AND Y.-S. SU

2.1. Notation,estimands and assumptions. We discuss a situation where we

attempt to identify a causal effect using a sample of independent observations of

size n.Datafortheith observation consists of an outcome variable, Yi, a vec-

tor of covariates, Xi, and a binary treatment assignment variable, Zi,where

Zi=1 denotes that the treatment was received. We deﬁne potential outcomes

for this observation, Yi(Zi=0)=Yi(0)and Yi(Z =1)=Yi(1), as the out-

comes that would manifest under each of the treatment assignments. It follows

that Yi=Yi(0)(1−Zi)+Yi(1)Zi. Given that observational samples are rarely

random samples from the population and we will be limiting our samples in

further nonrandom ways in order to address lack of overlap, it makes sense

to focus on sample estimands such as the conditional average treatment effect

(CATE), n

i=1E[Yi(1)−Yi(0)|Xi], and the conditional average treatment ef-

fect for the treated (CATT), i:Zi=1E[Yi(1)−Yi(0)|Xi]. Other common sam-

ple estimands we may consider are the sample average treatment effect (SATE),

n

i=1E[Yi(1)−Yi(0)], and the sample average effect of the treatment on the

treated (SATT), i:Zi=1E[Yi(1)−Yi(0)].

If ignorability holds for our sample, that is, Yi(0), Yi(1)⊥Zi|Xi=x,then

E[Yi(0)|Xi=x]=E[Yi|Zi=0,Xi=x]and E[Yi(1)|Xi=x]=E[Yi|Zi=1,

Xi=x]. The basic idea behind the BART approach to causal inference is to assume

E[Yi(0)|X=x]=f(0,x)and E[Yi(1)|Xi=x]=f(1,x)and then ﬁt a very

ﬂexible model for f.

In principle, any method that ﬂexibly estimates fcould be used to model these

conditional expectations. Chipman, George and McCulloch (2007, 2010) describe

BARTs advantages as a predictive algorithm compared to similar alternatives in

the data mining literature. Hill (2011) describes the advantages of using BART for

causal inference estimation over several alternatives common in the causal infer-

ence literature.

The BART algorithm consists of two pieces: a sum-of-trees model and a regu-

larization prior. Dropping the isubscript for notational convenience, we describe

the sum-of-trees model by Y=f(z,x)+ε,whereε∼N(0,σ2)and

f(z,x)=g(z,x;T1,M

1)+g(z,x;T2,M

2)+···+g(z,x;Tm,M

m).

Here each (Tj,M

j)denotes a single subtree model. The number of trees is typi-

cally allowed to be large [Chipman, George and McCulloch (2007, 2010) suggest

200, though, in practice, this number should not exceed the number of observa-

tions in the sample]. As is the case with related sum-of-trees strategies (such as

boosting), the algorithm requires a strategy to avoid overﬁtting. With BART this is

achieved through a regularization prior that allows each (Tj,M

j)tree to contribute

only a small part to the overall ﬁt.

BART ﬁts the sum-of-trees model using a MCMC algorithm that cycles be-

tween draws of (Tj,M

j)conditional on σand draws of σconditional on all of the

(Tj,M

j). Converence can be monitored by plotting the residual standard deviation

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1389

parameter σover time. More details regarding BART can be found in Chipman,

George and McCulloch (2007, 2010).

It is straightforward to use BART to estimate average causal effects such as

E[Y(1)|X=x]−E[Y(0)|X=x]=f(1,x)−f(0,x). Each iteration of the

BART Markov Chain generates a new draw of ffrom the posterior distribution.

Let frdenote the rth draw of f. To perform causal inference, we then compute

dr

i=fr(1,xi)−fr(0,xi),fori=1,...,n.Ifweaveragethedr

ivalues over i

with rﬁxed, the resulting values will be our Monte Carlo approximation to the

posterior distribution of the average treatment effect for the associated population.

For example, we average over the entire sample if we want to estimate the average

treatment effect. We average over i:zi=1 if we want to estimate the effect of the

treatment on the treated.

2.2. Past evidence regarding BART performance. Hill (2011) provides evi-

dence of superior performance of BART relative to popular causal inference strate-

gies in the context of nonlinear response surfaces. The focus in those comparisons

is on methods that are reasonably simple to understand and implement: standard

linear regression, propensity score matching (with regression adjustment), and in-

verse probability of treatment weighted linear regression [IPTW; Imbens (2004),

Kurth et al. (2006)].

One vulnerability of BART identiﬁed in Hill (2011) is that there is nothing to

prevent it from extrapolating over areas of the covariate space where common

support does not exist. This problem is not unique to BART; it is shared by all

causal modeling strategies that do not ﬁrst discard (or severely downweight) units

in these areas. Such extrapolations can lead to biased inferences because of the

lack of information available to identify either E[Y(0)|X]or E[Y(1)|X]in these

regions. This paper proposes strategies to address this issue.

2.3. Illustrative example with one predictor. We illustrate use of BART for

causal inference with an example [similar to one used in Hill (2011)]. This exam-

ple also demonstrates both the problems that can occur when common support is

compromised and a potential solution.

Figure 1displays simulated data from each of two treatment groups from a hy-

pothetical educational intervention. The 120 observations were generated indepen-

dently as follows. We generate the treatment variable as Z∼Bernoulli(0.5).We

generate a pretest measure as X|Z=1∼N(40,102)and X|Z=0∼N(20,102).

Our post-test potential outcomes are drawn as Y(0)|X∼N(72 +3√X, 1)and

Y(1)|X∼N(90 +exp(0.06X), 1). Since we conceptualize both our confounder

and our outcome as test scores, a ceiling is imposed on each (60 and 120, resp.).

Even with this constraint this is an extreme example of heterogeneous treatment

effects, designed, along with the lack of overlap, to make it extremely difﬁcult for

any method to successfully estimate the true treatment effect.

1390 J. HILL AND Y.-S. SU

FIG.1. Left panel:simulated data (points)and true response surfaces.The black upper curve and

points that follow it correspond to the treatment condition;the grey lower curve and points that follow

it correspond to the control condition.BART inference for each treated observation is displayed as

a95% posterior interval for f(1,x

i)and f(0,x

i).Discarded units (described in Section 4)are

circled.Right panel:solid curve represents the treatment effect as it varies with our pretest,X.

BART inference is displayed as 95% posterior intervals for the treatment effect for each treated unit.

Intervals for discarded units (described in Section 4)are displayed as dotted lines.In this sample the

conditional average treatment effect for the treated (CATT)is 12.2, and the sample average treatment

effect for the treated (SATT)is 11.8.

In the left panel, the upper solid black curve represents E[Y(1)|X]and the

lower grey one E[Y(0)|X]. The black circles close to the upper curve are the

treated and the grey squares close to the lower curve are the untreated (ignore

the circled points for now). Since there is only one confounding covariate, X,

the difference between the two response surfaces at any level of Xrepresents the

treatment effect for observations with that value of the pretest X. In this sample the

conditional average treatment effect for the treated (CATT) is 12.2, and the sample

average treatment effect for the treated (SATT) is 11.8.

A linear regression ﬁt to the data yields a substantial underestimate, 7.1 (s.e.

0.62), of both estimands. Propensity score matching (not restricted to common

support) with subsequent regression adjustment yields a much better estimate,

10.4 (s.e. 0.52), while the IPTW regression estimate is 9.6 (s.e. 0.45). For both

of these methods the propensity scores were estimated using logistic regression.

The left panel of Figure 1also displays the BART ﬁt to the response sur-

face (with number of trees equal to 100 since there are only 120 observations).

Each vertical line segment corresponds to individual level inference about either

E[Yi(0)|Xi]or E[Yi(1)|Xi]for each treated observation. Note that the ﬁt is quite

good until we try to predict E[Yi(0)|Xi]beyond the support of the data. The right

panel displays the true treatment effect as it varies with X,E[Y(1)−Y(0)|X],as

a solid curve. The BART inference (95% posterior interval) for the treatment effect

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1391

for each treated unit is superimposed as a vertical segment (ignore the solid versus

dashed distinction for now). These individual-level inferences can be averaged to

obtain inference for the effect of the treatment on the treated which is 9.5 with

95% posterior interval (7.7, 11.8); this interval best corresponds to inference with

respect to the conditional average treatment effect on the treated [Hill (2011)].

None of these methods yields a 95% interval that captures CATT. BART is

the only method to capture SATT, though at the expense of a wider uncertainty

interval. All the approaches are hampered by the fairly severe lack of common

support. Notice, however, the way that the BART-generated uncertainty bounds

grow much wider in the range where there is no overlap across treatment groups

(X>40). The marginal intervals nicely cover the true conditional treatment effects

until we start to leave this neighborhood. However, inference in this region is based

on extrapolation. Our goal is to devise a rule to determine how much “excess”

uncertainty should warrant removing a unit from the analysis. We will return to

this example in Section 4.

3. Identifying areas of common support. It is typical in causal inference to

assume common support. In particular, many researchers assume “strong ignora-

bility” [Rosenbaum and Rubin (1983)] which combines the standard ignorability

assumption discussed above with an assumption of common support often formal-

ized as 0 <Pr(Z |X)<1. It is somewhat less common for researchers to check

whether common support appears to be empirically satisﬁed for their particular

data set.

Moreover, the deﬁnition of common support is itself left vague in practice. Typ-

ically, Xcomprises the set of covariates the researcher has chosen to justify the

ignorabilty assumption. As such, conservative researchers will understandably in-

clude a large number of pretreatment variables in X. However, this will likely mean

that Xincludes any number of variables that are not required to satisfy ignorability

once we condition on some other subset of the vector of covariates. Importantly,

the requirement of common support need not hold for the variables not in this sub-

set, thus, trying to force common support on these extraneous variables can lead to

unnecessarily discarding observations.

The goal instead should be to ensure common causal support which can be de-

ﬁned as 0 <Pr(Z |W)<1, where Wrepresents any subset of Xthat will satisfy

Y(0), Y (1)⊥Z|W. Because BART takes advantage of the information in the out-

come variable, it should be better able to target common causal support as will be

demonstrated in the examples below. Propensity score methods, on the other hand,

ignore this information, rendering them incapable of making these distinctions.

If the common causal support assumption does not hold for the units in our

inferential sample (the units in our sample about whom we’d like to make causal

inference), we do not have direct empirical evidence about the counterfactual state

for them. Therefore, if we retain these units in our sample, we run the risk of

obtaining biased treatment effect estimates.

1392 J. HILL AND Y.-S. SU

One approach to this problem is to weight observations by the strength of sup-

port [for an example of this strategy in a propensity score setting, see Crump et al.

(2009)]. This strategy may yield efﬁciency gains over simply discarding prob-

lematic units. However, this approach has two key disadvantages. First, if there

are a large number of covariates, the weights may become unstable. Second, it

changes the interpretation of the estimand to something that may have little policy

or practical relevance. For instance, suppose the units that have the most support

are those currently receiving the program, however, the policy-relevant question

is what would happen to those currently not receiving the program. In this case

the estimand would give most weight to those participants of least interest from a

policy perspective.

Another option is to identify and remove observations in neighborhoods of the

covariate space that lack sufﬁcient common causal support. Simply discarding ob-

servations deemed problematic is unlikely to lead to an optimal solution. However,

this approach has the advantage of greater simplicity and transparency. More work

will need to be done, however, to provide strategies for adequately proﬁling the

discarded observations as well as those that we retain for inference; this paper will

provide a simple starting point in this effort. The primary goal of this paper is

simply to describe a strategy to identify these problematic observations.

3.1. Identifying areas of common causal support with BART. The simple idea

is to capitalize on the fact that the posterior standard deviations of the individual-

level conditional expectations estimated using BART increase markedly in areas

that lack common causal support, as illustrated in Figure 1. The challenge is to

determine how extreme these standard deviations should be before we need be

concerned. We present several possible rules for discarding units. In all strategies

when implementing BART we recommend setting the “number of trees” parameter

to 100 to allow BART to better determine the relative importance of the variables.

Recall that the individual-level causal effect for each unit can be expressed as

di=f(1,xi)−f(0,xi). For each unit, i, we have explicit information about

f(Z

i,xi). Our concern is whether we have enough information about f(1−

Zi,xi). The amount of information is reﬂected in the posterior standard deviations.

Therefore, we can create a metric for assessing our uncertainty regarding the sufﬁ-

ciency of the common support for any given unit by comparing σf0

i=sd(f (0,xi))

and σf1

i=sd(f (1,xi)),wheresd(·)denotes the posterior standard deviation.

In practice, of course we use Monte Carlo approximations to these quantities,

sf0

iand sf1

i, respectively, obtained by calculating the standard deviation of the

draws of f(0,xi)and f(0,xi)for the ith observation.

BART discarding rules. Our goal is to use the information that BART pro-

vides to create a rule for determining which units lack sufﬁcient counterfactual

evidence (i.e., residing in a neighborhood without common support). For exam-

ple, when estimating the effect of the treatment on units, i,forwhichZi=a, one

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1393

might consider discarding any unit, i, with Zi=a,forwhichsf1−a

i>m

a,where

ma=maxj{sfa

j},∀j:Zj=a. So, for instance, when estimating the effect of the

treatment on the treated we would discard treated units whose counterfactual stan-

dard deviation sf0

iexceeded the maximum standard deviation under the observed

treatment condition sf1

iacross all the treated units.

This cutoff is likely too sharp, however, as even chance disturbances might put

some units beyond this threshold. Therefore, a more useful rule might use a cutoff

that includes a “buffer” such that we would only discard for unit iin the inferential

group deﬁned as those with Zi=a,if

sf1−a

i>m

a+sdsfa

j(1sdrule),

where sd(sfa

j)represents the estimated standard deviation of the empirical distri-

bution of sfa

jover all units with Zj=a. For this rule to be most useful, we need

Var(Y |X,Z =0)=Va r (Y |X,Z =1)to hold at least approximately.

Another option is to consider the squared ratio of posterior standard devia-

tions (or, equivalently, the ratio of posterior variances) for each observation, with

the counterfactual posterior standard deviation in the numerator. An approximate

benchmark distribution for this ratio might be a χ2distribution with 1 degree of

freedom. Thus, for an observation with Zi=awe can choose cutoffs that corre-

spond to a speciﬁed p-value of rejecting the hypothesis that the variances are the

same of 0.10,

sf1−a

i/sfa

i2>2.706 ∀i:zi=1(α=0.10 rule)

or a p-value of 0.05,

sf1−a

i/sfa

i2>3.841 ∀i:zi=1(α=0.05 rule).

These ratio rules do not require the same type of homogeneity of variance assump-

tion across units as does the 1sdrule. However, they rest instead on an implicit

assumption of homogeneity of variance within unit across treatment conditions.

Additionally, they may be less stable and will be prone to rejection for units that

have particularly large amounts of information for the observed state. For instance,

an observation in a neighborhood of the covariate space that has control units may

still reject (i.e., be ﬂagged as a discard) if there are, relatively speaking, many more

treated units in this neighborhood as well.

Exploratory analyses using measures of common causal support uncertainty.

Another way to make use of the information in the posterior standard deviations

is more exploratory. The idea here is to use a classiﬁcation strategy such as a re-

gression tree to identify neighborhoods of the covariate space with relatively high

levels of common support uncertainty. For instance, when the goal is estimation of

the effect of the treatment on the treated we may want to determine neighborhoods

1394 J. HILL AND Y.-S. SU

that have clusters of units with relatively high levels of sf1−Zi

ior sf1−Zi

i/sfZi

i.Then

these “ﬂags” combined with researcher knowledge of the substantive context of the

research problem can be combined to identify observations or neighborhoods to be

excised from the analysis if it is deemed necessary. This approach may have the ad-

vantage of being more closely tied to the science of the question being addressed.

We illustrate possibilities for exploring and characterizing these neighborhoods in

Sections 4.3 and 6.

Reliance on this type of exploratory strategy will likely be eschewed by re-

searchers who favor strict analysis protocols as a means of promoting honesty in

research. In fact, the original BART causal analysis strategy was conceived with

this predilection in mind, which is why (absent the need or desire to address com-

mon support issues) the advice given is to run it only once and at the default set-

tings; this minimizes the amount of researcher “interference” [Hill (2011)]. These

preferences may still be satisﬁed, however, by specifying one of the discarding

rules above as part of the analysis protocol. For further discussion of this issue see

Section 3.3.

3.2. Competing strategies for identifying common support. The primary com-

petitors to our strategy for identiﬁcation of units that lack sufﬁcient common causal

support rely on propensity scores. While there is little advice directly given to the

topic of how to use the propensity score to identify observations that lack com-

mon support for the included predictors [for a notable exception see Crump et al.

(2009)], in practice, most researchers using propensity score strategies ﬁrst esti-

mate the propensity score and then discard any inferential units that extend be-

yond the range of the propensity score [Dehejia and Wahba (1999), Heckman,

Ichimura and Todd (1997), Morgan and Harding (2006)]. This type of exclusion

is performed automatically in at least two popular propensity score matching soft-

ware packages, MatchIt in R [Ho et al. (2013)] and psmatch2 in Stata [Leuven

and Sianesi (2011)] when the “common support” option is chosen. For instance,

if the focus is on the effect of the treatment on the treated, one would typically

discard the treated units with propensity scores greater than the maximum control

propensity score, unless there happened to be some treated with propensity scores

less than the minimum control propensity score (in which case these treated units

would be discarded as well).

More complicated caliper matching methods might further discard inferential

units that lie within the range of propensity scores of their comparison group if

such units are more than a set distance (in propensity score units) away from

their closest match [see, e.g., Frolich (2004)]. Given the number of different ra-

dius/caliper matching methods and the lack of clarity about the optimal caliper

width, it was beyond the scope of this paper to examine those strategies as well.

Weighting methods are typically not coupled with discarding rules since one of

the advantages touted by weighting advocates is that IPTW allows the researcher

to include their full sample of inferential and comparison units. However, in some

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1395

situations failure to discard inferential units that are quite different from the bulk

of the comparison units can lead to more unstable weight estimates.

We have two primary concerns about use of propensity scores to identify units

that fail to satisfy common causal support. First, they require a correct speciﬁ-

cation of the propensity score model. Offsetting this concern is the fact that our

BART strategy requires a reasonably good ﬁt to the response surface. As demon-

strated in Hill (2011), however, BART appears to be ﬂexible enough to perform

well in this respect even with highly nonlinear and nonparallel response surfaces.

A further caveat to this concern is the fact that several ﬂexible estimation strate-

gies have recently been proposed for estimating the propensity score. In particular,

Generalized Boosted Models (GBM) and Generalized Additive Models (GAM)

have both been advocated in this capacity with mostly positive results [McCaffrey,

Ridgeway and Morral (2004), Woo, Reiter and Karr (2008)], although some more

mixed ﬁndings exist for GBM in particular settings [Hill, Weiss and Zhai (2013)].

In Section 5we explore the relative performance of these approaches against our

BART approach.

Our second concern is that the propensity score strategies ignore the information

about common support embedded in the response variable. This can be important

because the researcher typically never knows which of the covariates in her data

set are actually confounders; if a covariate is not associated with both the treatment

assignment and the outcome, we need not worry about forcing overlap with regard

to it. Using propensity scores to determine common support gives greatest weight

to those variables that are most predictive of the treatment variable. However, these

variables may not be most important for predicting the outcome. In fact, there is

no guarantee that they are predictive of the outcome variable at all. Conversely,

the propensity score may give insufﬁcient weight to variables that are highly pre-

dictive of the outcome and thus may underestimate the risk of retaining units with

questionable support with regard to such a variable.

The BART approach, on the other hand, naturally and coherently incorporates

all of this information. For instance, if there is lack of common support with re-

spect to a variable that is not strongly predictive of the outcome, then the posterior

standard deviation for the counterfactual unit should not be systematically higher

to a large degree. However, a variable that similarly lacks common support but is

strongly predictive of the outcome should yield strong differences in the distribu-

tions of the posterior standard deviations across counterfactuals. Simply put, the

standard deviations should pick up “important” departures from complete overlap

and should largely ignore “unimportant” departures. This ability of BART to cap-

italize on information in the outcome variable allows it to more naturally target

common causal support.

3.3. Honesty. Advocates of propensity score strategies sometimes directly ad-

vocate for ignoring the information in the response variable [Rubin (2002)]. The

argument goes that such practice allows the researcher to be more honest because

a propensity score model can in theory be chosen (through balance checks) before

1396 J. HILL AND Y.-S. SU

the outcome variable is even included in the analysis. This approach can avoid the

potential problem of repeatedly tweaking a model until the treatment effect meets

one’s prior expectations. However, in reality there is nothing to stop a researcher

from estimating a treatment effect every time he ﬁts a new propensity score model

and, in practice, this surely happens. We argue that a better way to achieve this

type of honesty is to ﬁt just one model and use a prespeciﬁed discarding rule, as

can be achieved in the BART approach to causal inference.

4. Illustrative examples. We illustrate some of the key properties of our

method using several simple examples. Each example represents just one draw

from the given data generating mechanism, thus, these examples are not meant

to provide conclusive evidence regarding relative performance of the methods in

each scenario. These examples provide an opportunity to visualize some of the

basic properties of the BART strategy relative to more traditional propensity score

strategies: propensity score matching with regression adjustment and IPTW re-

gression estimates. Since we estimate average treatment effects for the treated in

all the examples, for the IPTW approach the treated units all receive weights of 1

and the control units receive weights of ˆe(x)/(1−ˆe(x)),where ˆe(x) denotes the

estimated propensity score.

4.1. Simple example with one predictor. First, we return to the simple example

from Section 2to see how our common causal support identiﬁcation strategies

work in that setting. Since there is only one predictor and it is a true confounder,

common support and common causal support are equivalent in this example and

we would not expect to see much difference between the methods.

The circled treated observations in the left-hand panel of Figure 1indicate the

29 observations that would be dropped using the standard propensity score discard

rule. Similarly, the dotted line segments in the right panel of the ﬁgure indicate

individual-speciﬁc treatment effects that would no longer be included in our aver-

age treatment effect inference. All three BART discard rules lead to the same set

of discarded observations as the propensity score strategy in this example.

SATT and CATT for the remaining units are 7.9 and 8.0, respectively. Our new

BART estimate is 8.2 with 95% posterior interval (7.7, 9.0). With this reduced

sample propensity score, matching (with subsequent regression adjustment) yields

an estimate of the treatment effect at 8.3 (s.e. 0.26) while IPTW yields an estimate

of 7.6 (s.e. 0.32).

Advantages of BART over the propensity score approach are not evident in this

simple example. They should manifest in examples where the assignment mecha-

nism is more difﬁcult to model or when there are multiple potential confounders

and not all variables that predict treatment also predict the outcome (or they do so

with different emphasis). We explore these issues next.

4.2. Illustrative examples with two predictors. We now describe two slightly

more complicated examples to illustrate the potential advantages of BART over

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1397

propensity-score-based competitors. In both examples there are two independent

covariates, each generated as N(0,1), and the goal is to estimate CATT which is

equal to 1 (in fact, the treatment effect is constant across observations in these

examples). The question in each case is whether some of the treated observations

should be dropped due to lack of empirical counterfactuals.

4.2.1. Example 2A: Two predictors,no confounders. In the ﬁrst example the

assignment mechanism is simple—after generating Zas a random ﬂip of the coin,

all controls with X1>0 are removed. The response surface is generated as E[Y|

Z,X1,X

2]=Z+X2+X2

2, thus, the true treatment effect is constant at 1. Since

there are no true confounders in this example, the requirement of common support

on both X1and X2will be overly conservative; overlap on neither is required to

satisfy common causal support. Figure 2illustrates how each strategy performs in

this scenario.

In both plots circles represent treated observations and squares represent control

observations. The left panel shows the results based on discarding units that lack

common support with respect to the propensity score. The observations discarded

by the propensity score method are displayed as solid circles. Since treatment as-

signment is driven solely by X1, there is a close mapping between X1and the

propensity score (were it not for the fact that X2was also in the estimation model

for the propensity score, the correspondence would be one-to-one). 62 of the 112

treatment observations are dropped based on lack of overlap with regard to the

propensity score.

FIG.2. Plots of simulated data with two predictors;the true treatment effect is 1. X1predicts treat-

ment assignment only and X2predicts outcome only.Control observations are displayed as squares.

Treated observations are displayed as circles.The left panel displays results based on propensity

score common support;solid circles indicate which observations were discarded.In the right panel

the size of the circle is proportional to the sf0

i.Observations discarded based on the BART 1sdrule

are displayed as solid circles.Observations discarded based on the BART α=0.10 rule are circled.

No observations were discarded based on the BART α=0.05 rule ratio rule.

1398 J. HILL AND Y.-S. SU

After re-estimating the propensity score matching on the smaller sample, the

matching estimate is 1.29. Since treatment assignment is independent of the po-

tential outcomes by design, this estimate should be unbiased over repeated sam-

ples. However, it now has less than half the observations available for estima-

tion. Inverse-probability-of-treatment weighting (IPTW) yields an estimate of 1.40

(s.e. 0.42) after discarding.3

In the right plot of Figure 2the size of the circle for each treated unit is propor-

tional to the corresponding size of the posterior standard deviation of the expected

outcome under the control condition (in this case, the counterfactual condition for

the treated). The size of the square that represents each control observation is pro-

portional to the cutoff level for discarding units. Observations discarded by the

1sdrulehave been made solid. Observations discarded by the α=0.10 rule have

been circled. No observations were discarded using the α=0.05 rule.

In contrast to the propensity score discard rule, the BART 1sdrulerecognizes

that X1does not play an important role in the response surface, so it only drops

7 observations that are at the boundary of the covariate space. The corresponding

BART estimate is 1.12 with a posterior standard deviation (0.26) that is quite a bit

smaller than the standard errors of both propensity score strategies. The α=0.10

rule drops 18 observations, on the other hand, and these observations are in a

different neighborhood than those dropped by the 1sdrulesince the individual

level ratios can get large not just when sf0

iis (relatively) large but also when sf1

i

is (relatively) small. The corresponding estimate of 1.17 and associated standard

error (0.23) are quite similar to those achieved by the 1sdrule.TheBARTα=

0.05 rule yields an estimate from the full sample since it leads to no discards (1.13

with a standard error of 0.27). All of the BART strategies beneﬁt from being able

to take advantage of the information in the outcome variable.

4.2.2. Example 2B: Two predictors,changing information. In the second ex-

ample the assignment mechanism is slightly more complicated. We start by gen-

erating Zas a binomial draw with probabilities equal to the inverse logit of

X1+X2−0.5X1X2. Next all control units with X1>0and X2>0 are re-

moved. Two different response surfaces are generated, each as E[Y|Z, X1,X

2]=

Z+0.5X1+2X2+φX1X2, where one version sets φto 1 and the other sets φto 3.

Therefore, both covariates are confounders in this example and both the common

support assumption and the common causal support assumption are in question.

Once again the treatment effect is 1.

The propensity score discard strategy chooses the same observations to discard

across both response surface scenarios because it only takes into account infor-

mation in the assignment mechanism. Thus, the left panel in Figure 3presents the

3If we fail to re-estimate the propensity score after the initial discard, the matching estimate is 1.53

(s.e. 0.40) and the IPTW estimate is 1.47 (s.e. 0.44).

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1399

FIG.3. Plots of simulated data with two predictors;the true treatment effect is 1. The display is

analogous to Figure 2,although here the two left plots display propensity score results across the

two scenarios and the two right display BART results across the two scenarios.

same plot twice; the only differences are the estimates of the treatment effect which

vary with response surface. The matching estimates get worse (0.74, then 0.13) as

the response surface becomes more highly nonlinear as do the IPTW estimates

(0.75, then 0.05). The uncertainty associated with the estimates grows between the

ﬁrst and second response surface (from roughly 0.2 to roughly 0.4), yet standard

95% conﬁdence intervals do not cover the truth in the second setting.4

4If we fail to re-estimate the propensity score after discarding, the estimates are just as bad or

worse. For the ﬁrst scenario, the matching estimate would be 0.65 (s.e. 0.28) and the IPTW estimate

would be 0.75 (s.e. 0.20). For the second scenario, the matching estimate would be 0.02 (s.e. 0.44)

and the IPTW estimate would be 0.06 (s.e. 0.36).

1400 J. HILL AND Y.-S. SU

The BART discard strategies, on the other hand, respond to information in the

response surface. Since the lack of overlap occurs in an area deﬁned by the in-

tersection of X1and X2, uncertainty in the posterior counterfactual predictions

increases sharply when the coefﬁcient on the interaction moves from 1 to 3 (as

displayed in the top and bottom plots in the right panel of Figure 3, resp.) and

more observations are dropped for both the 1sdruleand α=0.10 rule. In this ex-

ample α=0.10 rule once again focuses more on observations in the quadrant with

lack of overlap with respect to the treatment condition, whereas 1sdruleidentiﬁes

observations than tend to have greater uncertainty more generally. No observations

are dropped by α=0.05 rule even when φis 3.

The BART treatment effect estimates in both the ﬁrst scenario (all about 1.1)

and the second scenario (0.83, 0.70 and 0.76) are all closer to the truth than the

propensity-score-based estimates in this example. In the ﬁrst scenario the uncer-

tainty estimates (posterior standard errors of 0.26 for each) are slightly higher than

the standard errors for the propensity score estimates; in the second scenario the

uncertainty estimates (posterior standard errors all around 0.3) are all smaller than

the standard errors for the propensity score estimates.

4.3. Proﬁling the discarded units:Finding a needle in a haystack. When treat-

ment effects are not homogeneous, discarding observations from the inferential

group can change the target estimand. For instance, if focus is on the effect of the

treatment on the treated (e.g., CATT or SATT) and we discard treated observations,

then we can only make inferences about the treated units that remain (or the pop-

ulation they represent). It is important to have a sense of how this new estimand

differs from the original. In this section we illustrate a simple way to “proﬁle” the

units that remain in the inferential sample versus those that were discarded in an

attempt to achieve common support.

In this example there are 600 observations and 40 predictors, all generated as

N(1,1). Treatment was assigned randomly at the outset; control observations were

then eliminated from two neighborhoods in this high-dimensional covariate space.

The ﬁrst such neighborhood is deﬁned by X3>1andX4>1, the second by

X5>1andX6>1. The nonlinear nonparallel response surface is generated as

E[Y(0)|X]<−0.5X1+2X2+0.5X5+2X6+X5X6+0.5X2

5+1.5X2

6and

E[Y(1)|X]<−0.5X1+2X2+0.5X5+2X6+0.2X5X6. The treatment effect

thus varies across levels of the included covariates. Importantly, since X3and X4

do not enter into the response surface, only the second of the two neighborhoods

that lack overlap should be of concern.

The leftmost plot in Figure 4displays results from the BART and propensity

score methods both before and after discarding. The numbers at the right repre-

sent the percentage of the treated observations that were dropped for each discard

method. Solid squares represent the true estimand (SATT) for the sample corre-

sponding to that estimate (the same for all methods that do not discard but different

for those that do). Circles and line segments represent estimates and corresponding

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1401

FIG.4. Left plot displays estimands (squares)and attempted inference (circles for estimates and

bars for 95%intervals)for the BART and propensity score methods both with and without discarding.

The right plots display regression tree ﬁts using the covariates as predictors.The responses used are

the statistic from 1sdruleand then the propensity score,respectively.

95% intervals for each estimate. None of the methods that fail to discard has a 95%

interval that covers the truth for the full sample. After discarding using the BART

rules, all of the intervals cover the true treatment effect for the remaining sample.

The propensity score methods drop far fewer treated observations, leading to esti-

mands that do not change much and estimates that still do not cover the estimands

for the remaining sample.

We make use of simple regression trees [CART; Breiman (2001), Breiman et al.

(1984)] to investigate the differences between the neighborhoods perceived as

problematic for each method. Regression trees use predictors to partition the sam-

ple into subsamples that are relatively homogenous with respect to the response

variable. For our purposes, the predictors are our potential confounders and the

response is the statistic corresponding to a given discard rule.5Asimpletreeﬁt

provides a crude means of describing the neighborhoods of the covariate space

considered most problematic by each rule with respect to common support. Each

tree is restricted to a maximum depth of three for the sake of parsimony.

5Another strategy would be to use the indicator for discard as the response variable. This could

become problematic if the number of discarded observations is small and would yield no information

about the likelihood of being discarded in situations where no units exceeded the threshold.

1402 J. HILL AND Y.-S. SU

To proﬁle the units that the BART 1sdruleconsiders problematic, we use for

the response variable in the tree the corresponding statistic relative to the cutoff

rule (appropriate for estimating the effect of the treatment on the treated), sf0

i−

m1−sd(sf1

j),whereiand jindex treated units. The tree ﬁt is displayed in the top

right plot of Figure 4with the mean of the response in each terminal node given in

the corresponding oval. Note that the decision rules for the tree are based almost

exclusively on the variables X5and X6, as we would hope they would be given

how the data were generated.

The tree ﬁt using the propensity score as the response is displayed in the lower

right plot of Figure 4.X5plays a far less prominent role in this tree and X6does not

appear at all. X16,X36 ,andX40 play important roles even though these variables

are not strong predictors in the response surface; in fact, these are all independent

of both the treatment and the response.

This example illustrates two things. First, regression trees may be a useful strat-

egy for proﬁling which neighborhoods each method has identiﬁed as problematic

with regard to common support. Second, the propensity score approach may fail

to appropriately discover areas that lack overlap if the model for the assignment

mechanism and the model for the response surface are not well aligned with re-

spect to the relative importance of each variable. We explore the importance of this

type of alignment in more detail in the next section.

5. Simulation evidence. This section explores simulation evidence regarding

the performance of our proposed method for identifying lack of common support

relative to the performance of two commonly-used and several less-commonly-

used propensity-score-based alternatives. Overall we compare the performance of

12 different estimation strategies across 32 different simulated scenarios.

5.1. Simulation scenarios. These scenarios represent all combinations of ﬁve

design factors. The ﬁrst factor varies whether the logit of the conditional expec-

tation of the treatment assignment is linear or nonlinear in the covariates. The

second factor varies the relative importance of the covariates with regard to the

assignment mechanism versus the response surface. In one setting of this factor

(“aligned”) there is substantial alignment in the predictive strength of the covari-

ates across these two mechanisms—the covariates that best predict the treatment

also predict the outcome well. In the other setting (“not as aligned”) the covariates

that best predict the treatment strongly and those that predict the response strongly

are less well aligned (for details see the description of the treatment assignment

mechanisms and response surfaces and Table 1,below).

6The third factor is the

ratio of treated to control (4:1 or 1:4) units. The fourth factor is the number of

predictors available to the researcher (10 versus 50, although in both cases only

6For a related discussion of the importance of alignment in causal inference see Kern et al. (2013).

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1403

TABLE 1

Nonzero coefﬁcients in γLand γLfor the treatment assignment mechanism as well as for βL

zand βNL

zfor the nonlinear,not parallel response surfaces.

Coefﬁcients for the parallel response surface are the same as those for Y(0)in the nonparallel response surface

x1x2x2

1x2

2x2x6x5x6x7x8x9x10 x2

5x2

6x5x6x5x6x7x2

7x3

7x2

8x7x8x2

9x9x10

Treatment assignment mechanisms

Linear 0.4 0.20.40.20.40.4

Nonlinear 0.4 0.20.40.20.40.4 0.8 0.8 0.5 0.3 0.8 0.2 0.4 0.3 0.8 0.5

Response surfaces, nonlinear and not parallel

Aligned

Y(0)0.5 2 0.5 2 0.4 0.8 0.5 0.5 0.5 0.7

Y(1)0.5 1 0.5 0.80.3

Not as aligned

Y(0)0.5 2 0.4 0.5 1 0.5 2 0.5 1.5 0.7

Y(1)0.5 0.5 0.5 2 0.3

1404 J. HILL AND Y.-S. SU

8 are relevant). The ﬁfth and ﬁnal factor is whether or not the nonlinear response

surfaces are parallel across treatment and control groups; nonparallel response sur-

faces imply heterogeneous treatment effects.

In all scenarios each covariate is generated independently from Xj∼N(0,1).

These column vectors comprise the matrix X. The general form of the linear treat-

ment assignment mechanism is Z∼Binomial(n, p) with p=logit−1(ω +XγL),

where the offset ωis speciﬁed to create the appropriate ratio of treated to control

units. The nonlinear form of this assignment mechanism simply includes some

nonlinear transformations of the covariates in X, denoted as Qwith correspond-

ing coefﬁcients γNL. The nonzero coefﬁcients for the terms in these models are

displayed in Table 1.

We simulate two distinct sets of response surfaces that differ in both their level

of alignment with the assignment mechanism and whether they are parallel. Both

sets used are nonlinear in the covariates and each set is generated generally as

EY(0)|X=NXβL

0+QβNL

0,1,

EY(1)|X=NXβL

1+QβNL

1+τ,1,

where βL

zis a vector of coefﬁcients for the untransformed versions of the pre-

dictors Xand βNL

zis a vector of coefﬁcients for the transformed versions of the

predictors captured in Q. In the scenarios with parallel response surfaces, τ(the

constant treatment effect) is 4, βL

0=βL

1,andβNL

0=βNL

1and both use the coefﬁ-

cients from Y(0)in Table 1(only nonzero coefﬁcients displayed). In the scenarios

with responses surfaces are not parallel, τ=0, and the nonzero coefﬁcients in the

βL

zand βNL

zare displayed in Table 1.

Tabl e 1helps us understand the alignment in predictor strength between the

assignment mechanism and response surfaces for each of the two scenarios. The

“aligned” version of the response surfaces places weight on the covariates most

predictive of the assignment mechanism (both the linear and nonlinear pieces).

There is no reason to believe that this alignment occurs in real examples. There-

fore, we explore a more realistic scenario where coefﬁcient strength is “not as

aligned.”

We replicate each of the 32 scenarios 200 times and in each simulation run we

implement each of 12 different modeling strategies. For each the goal is to estimate

the conditional average effect of the treatment on the subset of treated units that

were not discarded.

5.2. Estimation strategies compared. We compare three basic causal infer-

ence strategies without discarding—BART [implemented as described above and

in Hill (2011) except using 100 trees], propensity score matching, and IPTW—

with nine strategies that involve discarding.

The ﬁrst three discarding approaches discard using the 1sdrule,theα=0.10

rule,andtheα=0.05 rule and each is coupled with a BART analysis of the causal

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1405

effect on the remaining sample.7The remaining 6 approaches are combinations of

3 propensity score discarding strategies and 2 analysis strategies. The 3 propensity

score discard strategies vary by the estimation strategy for the propensity score

model: standard logit, generalized boosted regression model [recommended for

propensity score estimation by McCaffrey, Ridgeway and Morral (2004)], and gen-

eralized additive models [recommended for propensity score estimation by Woo,

Reiter and Karr (2008)]. The 2 analysis strategies (each conditional on a given

propensity score estimation model) are one-to-one matching (followed by regres-

sion adjustment) and inverse-probability of treatment weighting (in the context of

a linear regression model). In all propensity score strategies the propensity score is

re-estimated after the initial units are discarded. The y-axis labels of the results ﬁg-

ures indicate these 12 different combinations of strategies. All strategies estimate

the effect of the treatment on the treated.

We implement these models in several packages in R [R Core Team (2012)]. We

use the bart() function in the BayesTree package [Chipman and McCulloch

(2009)] to ﬁt BART models. For each BART ﬁt, we allow the maximum number

of trees in the sum to be 100 as described in Section 3.1 above. To ensure the

convergence of the MCMC in BART without having to check for each simulation

run, we are conservative and let the algorithm run for 3500 iterations with the

ﬁrst 500 considered burn-in. To implement the GBM routine, we use the gbm()

function of the gbm package [Ridgeway (2007)]. In an attempt to optimize the

settings for esimating propensity scores, we adopt the suggestions of [McCaffrey,

Ridgeway and Morral (2004), 409] for the tuning parameters of the GBM: 100

trees, a maximum of 4 splits for each tree, a small shrinkage value of 0.0005, and

a random sample of 50% of the data set to be use for each ﬁt in each iteration.8

We use the gam() function of the gam package [Hastie (2009)] to implement the

GAM routine.

5.3. Simulation results. Figure 5presents results from 8 scenarios that have

the common elements of a linear treatment assignment mechanism and parallel

response surfaces. The linear treatment assignment mechanism should favor the

propensity score approaches. The top panel of 4 plots in this ﬁgure corresponds

to the setting where there is alignment in the predictive strength of the covariates;

this setting should favor the propensity score approach as well since it implicitly

uses information about the predictive strength of the covariates with regard to the

treatment assignment mechanism to gauge the importance of each covariate as a

confounder. The bottom panel of Figure 5reﬂects scenarios in which the predictive

7We do not re-estimate BART after discarding but simply limit our inference to MCMC results

from the nondiscarded observations.

8In response to a suggestion by a reviewer we also implemented this method using the twang

package in R[Ridgeway et al. (2012)] using the settings suggested in the vignette (n.trees =5000,

interaction.depth =2, shrinkage =0.01). This did not improve the GBM results.

1406 J. HILL AND Y.-S. SU

FIG.5. Simulation results for the scenarios in which the treatment assignment is linear and the

response surfaces are parallel.Solid dots represent average differences between estimated treatment

effects and the true ones standardized by the standard deviations of the outcomes.Bars are root mean

square errors (RMSE)of such estimates.The drop rates are the percentage discarded units.Discard

and analysis strategies are described in the text.Five modeling strategies are highlighted with hollow

bars for comparison:the three BART strategies and the most likely propensity scores versions to be

implemented (these are the same strategies illustrated in the examples in Section 4).

strength of the covariates is not as well aligned between the treatment assignment

mechanism and the response surface. This setup provides less of an advantage for

the propensity score methods. The potential for bias across all methods, however,

should be reduced.

Within each plot, each bar represents the root mean square error (RMSE) of

the estimates for that scenario for a particular estimation strategy. The dots rep-

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1407

resent the absolute bias (the absolute value of the average difference between the

estimates and the CATT estimand). Drop rates for the discarding methods are in-

dicated on the right-hand side of each plot. We highlight (with unﬁlled bars) the

BART discard/analysis strategies as well as the two propensity score discard strate-

gies that rely on the logit speciﬁcation of the propensity score model (the most

commonly used model for estimating propensity scores).

The ﬁrst thing to note about Figure 5is that there is little bias in any of the

methods across all of these eight scenarios and likewise the RMSEs are all small.

Within this we do see some small differences in the absolute levels of bias across

methods in the aligned scenarios, with slightly less bias evidenced by the propen-

sity score approaches and smaller RMSEs for the BART approaches. In the non-

aligned scenarios the differences in bias nearly disappear (with a slight advantage

overall for BART) and the advantage with regard to RMSE becomes slightly more

pronounced. None of the methods drop a large percentage of treated observations,

but the BART rules discard the least (with one small exception).

The eight plots in Figure 6represent scenarios in which the nonlinear treatment

assignment mechanism was paired with parallel response surfaces. The nonlinear

treatment assignment presents a challenge to the naively speciﬁed propensity score

models. These plots vary between upper and lower panels in similar ways as seen

in Figure 5. Overall, these plots show substantial differences in results between the

BART and propensity score methods. The BART discard methods drop far fewer

observations and yield substantially less bias and smaller RMSE across the board.

The differences between propensity score methods are negligible.

Figure 7corresponds to scenarios with linear treatment assignment mechanism

and nonparallel response surfaces. The top panel shows little difference in RMSE

or bias for the BART 1sdrulecompared to the best propensity score strategies

(sometimes slightly better and sometimes slightly worse). The BART α=0.10

rule and α=0.05 rule perform slightly worse than the 1sdrulein all four sce-

narios. The bottom panel of Figure 7shows slightly more clear gains with regard

to RMSE for the BART discard methods; the results regarding bias, however, are

slightly more mixed, though the differences are not large. Across all scenarios the

BART 1sdruledrops a higher percentage of treated observations than the propen-

sity score rules; this difference is substantial in the scenarios where treated out-

number controls 4 to 1. The BART 1sdrulealways drops more than the ratio rules

when controls outnumber treated but not when the treated outnumber controls.

The eight plots in Figure 8all represent scenarios with nonlinear treatment as-

signment mechanism and nonparallel response surfaces. In the top panel the dif-

ferences between the BART methods and the best propensity score methods are

not large with regard to either bias or RMSE with BART performing worst in the

scenario with 50 potential predictors and more treated than controls. In the bottom

plots corresponding to misaligned strength of coefﬁcients BART displays consis-

tent gains over the propensity scores approaches both in terms of bias and RMSE.

All the methods discard a relatively high percentage of treated observations.

1408 J. HILL AND Y.-S. SU

FIG.6. Simulation results for the scenarios with nonlinear treatment assignment and parallel re-

sponse surfaces.Description otherwise the same as in Figure 5.

While it does not dominate at every combination of our design factors, the

BART 1sdruleappears to perform most reliably across all the methods overall.

In particular, it almost always performs better with regard to RMSE and it often

performs well with respect to bias as well.

6. Discarding and proﬁling when examining the effect of breastfeeding on

intelligence. The putative effect of breastfeeding on intelligence or cognitive

achievement has been heavily debated over the past few decades. This debate is

complicated by the fact that this question does not lend itself to direct experimen-

tation and, thus, the vast majority of the research that has been performed has relied

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1409

FIG.7. Simulation results for the scenarios with nonlinear treatment assignment and nonparallel

response surfaces.Description otherwise the same as in Figure 5.

on observational data. While many of these studies demonstrate small to medium-

sized positive effects [see, e.g., Anderson, Johnstone and Remley (1999), Lawlor

et al. (2006), Mortensen et al. (2002), among others] some contrary evidence exists

[notably Der, Batty and Deary (2006), Drane and Logemann (2000), Jain, Concato

and Leventhal (2002)]. It has been hypothesized that the effects of breastfeeding

increase with the length of exposure, therefore, to maximize the chance of detect-

ing an effect, it makes sense to examine the effect of breastfeeding for extended

durations versus not at all. This approach is complicated by the fact that moth-

ers who breastfeed for longer periods of time tend to have substantially different

characteristics on average than those who never breastfeed (as an example see the

1410 J. HILL AND Y.-S. SU

FIG.8. Simulation results for the scenarios with nonlinear treatment assignment and nonparallel

response surfaces.Description otherwise the same as in Figure 5.

unmatched differences in means in Figure 9). Thus, identiﬁcation of areas of com-

mon support should be an important characteristic of any analysis attempting to

identify such effects.

Randomized experiments have been performed that address related questions.

Such studies have been used to establish a causal link, for instance, between two

fatty acids found in breast milk (docosahexaenoic acid and arachidonic acid) and

eyesight and motor development [see, e.g., Lundqvist-Persson et al. (2010)]; this

could represent a piece of the causal pathway between breastfeeding and sub-

sequent cognitive development. Furthermore, a recent large-scale study [Kramer

et al. (2008)] randomized encouragement to breastfeed and found signiﬁcant, pos-

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1411

FIG.9. Top panel:balance represented as standardized differences in means for each of three

samples:unmatched (open circles), post-discarding matched (solid circles), and post-discarding

re-weighted (plus signs). Discarding combined with matching and weighting substantially improve

the balance.Bottom panel:overlapping histograms of propensity scores (on the linear scale)for both

breastfeeding groups.

1412 J. HILL AND Y.-S. SU

itive estimates of the intention-to-treat effect (i.e., the effect of the randomized

encouragement) on verbal and performance IQ measures at six and a half years

old. Even a randomized study such as this, however, cannot directly address the

effects of prolonged breastfeeding on cognitive outcomes. This estimation would

still require comparisons between groups that are not randomly assigned. More-

over, an instrumental variables approach would not necessarily solve the problem

either. Binary instruments cannot be used to identify effects at different dosage

levels of a treatment without further assumptions. However, dichotomization of

breastfeeding duration would almost certainly lead to a violation of the exclusion

restriction.

We examine the effect of breastfeeding for 9 months or more (compared to not

breastfeeding at all) on child math and reading achievement scores at age 5 or 6.

Our “treatment” group consists of 271 mothers who breastfed at least 38 weeks

and our “control” group consists of 1832 mothers who reported 0 weeks of breast-

feeding. To create a cleaner comparison, we remove from our analysis sample

mothers who breastfed greater than 0 weeks or less than 38 weeks. Given that the

most salient policy question is whether new mothers should be (more strongly)

encouraged to breastfeed their infants, the estimand of interest is the effect of the

treatment on the controls. That is, we would like to know what would have hap-

pened to the mothers in the sample who were observed to not breastfeed their

children if they had instead breastfed for at least 9 months.

We used data from the National Longitudinal Survey of Youth (NLSY) Child

Supplement [for more information see Chase-Lansdale et al. (1991)]. The NLSY

is a longitudinal survey that began in 1979 with a cohort of approximately 12,600

young men and women aged 14 to 21 and continued annually until 1994 and bian-

nually thereafter. The NLSY started collecting information on the children of fe-

male respondents in 1986. Our sample comprises 2103 children of the NLSY born

from 1982 to 1993 who had been tested in reading and math at age 5 or 6 by the

year 2000 and whose mothers fell into our two breastfeeding categories (no months

or 9 plus months).

In addition to information on number of weeks each mother breastfed her child,

we also have access to detailed information on potential confounders. The co-

variates included are similar to those used in other studies on breastfeeding using

the NLSY [see, e.g., Der, Batty and Deary (2006)], however, we excluded several

post-treatment variables that are often used, such as child care and home envi-

ronment measures since these could bias causal estimates [Rosenbaum (1984)].

Measurements regarding the child at birth include birth order, race/ethnicity, sex,

days in hospital, weeks preterm, and birth weight. Measurements on the mother in-

clude her age at the time of birth, race/ethnicity, Armed Forces Qualiﬁcation Test

(AFQT) score, whether she worked before the child was born, days in hospital

after birth, and educational level at birth. Household measures include income (at

birth), whether a spouse or partner was present at the time of the birth of the child,

and whether grandparents were present one year before birth.

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1413

The children in the NLSY subsample were tested on a variety of cognitive mea-

sures at each survey point (every two years starting with age 3 or 4). We make use

of the Peabody Individual Achievement Test (PIAT) math and reading scores from

assessments that took place either at age 5 or 6 (depending on the timing of the

survey relative to the age of the child).

To allow focus on issues of common support and causal inference and to avoid

debate about the best way to deal with the missing data, we simply limit our sample

to complete cases. Due to this restriction, this sample should not be considered to

be representative of all children in the NLSY child sample whose mothers fell into

the categories deﬁned.

Comparing the two groups based on the baseline characteristics reveals im-

balance. Figure 9displays the balance for the unmatched (open circles), post-

discarding matched (solid circles), and post-discarding re-weighted (plus signs)

samples. The matched and reweighted samples are much more closely balanced

than the unmatched sample, particularly for the household and race variables.

The bottom panel of Figure 9displays the overlap in propensity scores estimated

by logistic regression (displayed on the linear scale). The histogram for the con-

trol units has been shaded in with grey, while the histogram for the treated units

is simply outlined in black. This plot suggests lack of common support for the

control units with respect to the estimated propensity score. The question remains,

however, whether sufﬁcient common support on relevant covariates exists.

We use both propensity score and BART approaches to address this question.

The results of our analyses are summarized in Table 2which displays for each

method and test score (reading or math) combination: treatment effect estimate,

standard error,9and number of units discarded. Without discarding there is a sub-

stantial degree of heterogeneity between BART, linear regression after one-to-

one nearest neighbor propensity score matching with replacement (Match), IPTW

(propensity scores estimated in all cases using logistic regression), regression and

standard linear regression. For reading test scores the treatment effect estimates

are (3.5, 2.5, 1.5, and 3.2) with standard errors ranging between roughly 0.9 and

1.6. For math test scores the estimates are (2.4, 3.4, 2.6, and 2.2) with standard

errors ranging between roughly 0.9 and 1.9.

For the analysis of the effect on reading, the BART α=0.10 rule would discard

93 observations, however, neither the BART 1sdruleor the α=0.05 rule would

discard any. Regardless of the discard strategy, however, the BART estimate is

about 3.5 with posterior standard deviation of a little over 1. Levels of discarding

are similar for math test scores, although for this outcome the BART α=0.10 rule

9We calculate standard errors for the propensity score analyses by treating the weights (for match-

ing the weights are equal to the number of times each observation is used in the analysis) as survey

weights. This was implemented using the survey package in R. Technically speaking, uncertainty

of each BART estimates is expressed by the standard deviation of the posterior distribution of the

treatment effect.

1414 J. HILL AND Y.-S. SU

TABLE 2

Table displays treatment effect estimates,associated standard errors,and number of units discarded

for each method and test score (reading or math)combination

Reading Math

Treatment Standard Number Treatment Standard Number

Method effect error discarded effect error discarded

BART 3.5 1.07 0 2.4 1.05 0

BART-D1 3.5 1.07 0 2.4 1.05 0

BART-D2 3.5 1.04 93 2.4 1.04 53

BART-D3 3.5 1.07 0 2.4 1.05 0

Match 2.5 1.62 0 3.4 1.74 0

Match-D 3.6 1.50 168 1.5 1.13 168

Match-D-RE 3.8 1.43 168 1.5 1.18 168

IPTW 1.5 1.57 0 2.6 1.92 0

IPTW-D 1.6 1.52 168 2.6 1.85 168

IPTW-D-RE 1.6 1.51 168 2.6 1.80 168

OLS 3.2 0.87 0 2.2 0.89 0

would discard 53. Similarly, the effect estimates (2.4) and associated uncertainty

estimates (a little over 1) are almost identical across strategies.

Using propensity scores (estimated using a logistic model linear in the covari-

ates) to identify common support discards 168 of the control units. This strat-

egy does not change depending on the outcome variable. Using propensity scores

estimated on the remaining units, matching (followed by regression adjustment;

Match-D-RE) and IPTW regression (IPTW-D-RE) yield reading treatment effect

estimates for the reduced sample of 3.8 (s.e. 1.43) and 1.6 (s.e. 1.51), respectively.

If we do not re-estimate the propensity score after discarding, these estimates

(Match-D and IPTW-D) are 3.6 (s.e. 1.50) and 1.6 (s.e. 1.52), respectively. The

results for math are quite heterogeneous as well, with matching and IPTW yield-

ing estimates of 1.5 (s.e. 1.18) and 2.6 (s.e. 1.80), respectively. Re-estimating the

propensity scores did not change the results for this outcome (when rounding to

the ﬁrst decimal place).

It is important to remember that the methods that discard units are estimating

different estimands than those that do not, therefore, direct comparisons between

the BART and propensity score estimates are not particularly informative. Impor-

tantly, however, both propensity score methods are estimating the same effect (they

discarded the exact same units), therefore, the differences between these estimates

are a bit disconcerting. One possible explanation for these discrepancies is that the

two propensity score methods do yield somewhat different results with regard to

balance as displayed in Figure 9; IPTW yields slightly closer balance on average

(though not for every covariate).

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1415

What might account for the differences in which units were discarded between

the BART and propensity score approaches? To better understand, we more closely

examine which variables each strategy identiﬁes as being important with regard

to common support by considering the predictive strength of each covariate with

regard to both propensity score and BART models in combination with ﬁtting re-

gression trees with the discard statistics as response variables just as in Section 4.3.

BART identiﬁes birth order, mother’s AFQT score, household income, mother’s

educational attainment at time of birth, and the number of days the child spent in

the hospital as the most important continuous predictors for both outcomes (al-

though the relative importance of each changes a bit between outcomes). Recall,

however, that the BART discard rules are driven by circumstances in which the

level of information about the outcome changes drastically across observations in

different treatment groups. The overlap across treatment groups for most of these

variables is actually quite good. While some, like AFQT, are quite imbalanced,

overlap still exists for all of the inferential (control) observations. More problem-

atic in terms of common support is the variable that reﬂects the number of days

the child spent in the hospital; 30 children of mothers who did not breastfeed had

values for this variable higher than the maximum value (30 days) for the children

of mothers who did breastfeed for nine or more months. Not surprisingly, this vari-

able is the primary driving force behind the BART 1sdruleas seen in Figure 10,

particularly for mothers who did not have a spouse living in the household at the

time of birth. Mother’s education plays a more important role for the BART ratio

rules for the reading outcome. This variable also has some issues with incomplete

overlap and it is slightly more important in predicting reading outcomes than math

outcomes.

A look at the ﬁtted propensity score model, on the other hand, reveals that

breastfeeding for nine or more months is predicted most strongly by the mother’s

AFQT scores, her educational attainment, and her age at the time of the birth of

her child. Thus, these variables drive the discard rule. In particular, the critical role

of mom’s AFQT is evidenced in the regression tree for the discard rule at the bot-

tom of Figure 10. Children whose mothers were not married at birth and whose

AFQT scores were less than 50 were most likely to be discarded from the group

of nonbreastfeeding mothers about whom we would like to make inferences.

What conclusions can we draw from this example? Substantively, if we feel

conﬁdent about the ignorability assumption, the BART results suggest a moderate

positive impact of breastfeeding 9 or more months on both reading and math out-

comes at age 5 or 6. The propensity score results for the sample that remain after

discarding for common support are more mixed, with only the matching estimates

on reading outcomes showing up as positive and statistically signiﬁcant.

Methodologically, this is an example in which propensity score rules yield more

discards than BART rules. The most reliable rule based on our simulation results

(the BART 1sdrule) would not discard any units. A closer look at the overlap for

speciﬁc covariates and at regression trees for the discard statistics indicates that

1416 J. HILL AND Y.-S. SU

FIG. 10. Regression trees explore the characteristics of units at risk of failing to satisfy common

(causal)support.The top two trees use the two statistics from the BART discard rules for the reading

outcome variable as the response;the next two trees use the two statistics from the BART discard

rules for the math outcome variable.The bottom tree uses the estimated propensity score subtracted

from the cutoff (maximum estimated propensity score for the controls). The predictors of the trees are

all the potential confounding covariates.For all trees the larger the statistic the more likely the unit

will be discarded,so focus is on the rightmost part of each tree.

ASSESSING LACK OF COMMON SUPPORT IN CAUSAL INFERENCE 1417

the BART discard rules may represent a better reﬂection of the actual relationships

between the variables. The lack of stability of the propensity score estimates is also

cause for concern. We emphasize, however, that we have used rather naive propen-

sity score approaches which are not intended to represent best practice. Given the

current lack of guidance with regard to optimal choices for propensity score mod-

els and speciﬁc matching and weighting methods, we chose instead to use imple-

mentations that were as straightforward as the BART approach.

7. Discussion. Evaluation of empirical evidence for the common support as-

sumption has been given short shrift in the causal inference literature although the

implications can be important. Failure to detect areas that lack common causal sup-

port can lead to biased inference due to imbalance or inappropriate model extrapo-

lation. On the other extreme, overly conservative assessment of neighborhoods or

units that seem to lack common support may be equally problematic.

This paper distinguishes between the concepts of common support and common

causal support. It introduces a new approach for identifying common causal sup-

port that relies on Bayesian Additive Regression Trees (BART). We believe that

this method’s ﬂexible functional form and its ability to take advantage of infor-

mation in the response surface allows it to better target areas of common causal

support than traditional propensity-score-based methods. We also propose a sim-

ple approach to proﬁling discarded units based on regression trees. The potential

usefulness of these strategies has been demonstrated through examples and simu-

lation evidence and the approach has been illustrated in a real example.

While this paper provides some evidence that BART may outperform propensity

score methods in the situations tested, we do not claim that it is uniformly supe-

rior or that it is the only strategy for incorporating information about the outcome

variable. We acknowledge that there are many ways of using propensity scores

that we did not test, however, our focus was on examination of methods that were

straightforward to implement and do not require complicated interplay between

the researcher’s substantive knowledge and the choice of how to implement (what

propensity score model to ﬁt, which matching or weighting method to use, which

variables to privilege in balancing, which balance statistics to use). We hope that

this paper is a starting point for further explorations into better approaches for iden-

tifying common support, investigating the role of the outcome variable in causal

inference methods, and development of more effective ways of proﬁling units that

we deem to lack common causal support.

There is a connection between this work and that of others [e.g., Brookhart et al.

(2006)] who have pointed out the danger of strategies that implicitly assign greater

importance to variables that most strongly inﬂuence the treatment variable but that

may have little or no direct association with the outcome variable. In response,

some authors such as Kelcey (2011) have outlined approaches to choosing con-

founders in ways that make use of the observed association between the possible

confounders and the potential outcomes. Another option that is close in spirit to

1418 J. HILL AND Y.-S. SU

the propensity score techniques but makes use of outcome data (at least in the con-

trol group) would be a prognostic score approach [Hansen (2008)]. To date, there

has been no formal discussion of use of prognostic cores for this purpose, but this

might be a useful avenue for further research.10

Acknowledgments. The authors would like to thank two anonymous referees

and our Associate Editor, Susan Paddock, for their helpful comments and sugges-

tions.

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