Some Remarks on the Causal Inference
for Historical Persistence ∗Katsuo Kogure†
January 20, 2019
Abstract
A growing body of literature examines the relationships between historical events and contemporary economic outcomes. Recent studies estimate thecausal eﬀects using detailed historical data and contemporary microdata of
individuals and/or households. In this paper, we discuss conceptual and empirical issues inherent in the causal inference following the potential outcomesframework. Using an empirical example, we also illustrate a simple alternative
approach to avoid these issues that is coherent with the potential outcomesframework.
JEL Codes: B52, N01, C18
Keywords: history, economic development, causal eﬀect, Rubin causal model∗

I am grateful to Keisuke Hirano for his insightful comments on this issue. I am also grateful to
Jun Goto, Kosuke Imai, Nobuyoshi Kikuchi, Hisaki Kono, Masahiro Kubo, Fumiharu Mieno, Chiaki
Moriguchi, Ryo Nakajima, Fumio Ohtake, Yoshito Takasaki, Kensuke Teshima, Ken Yamada, andseminar participants at the 3rd Hitotsubashi Summer Institute 2017, Kyoto University, Kansai Labor
Workshop, and Nihon Fukushi University for helpful discussions and suggestions. In addition, I am
indebted to Melissa Dell and Econometrica for allowing me to access her data and programs. This
research is supported by Grants-in-Aid for Scientiﬁc Research No.15K17044, Japan Society for the
Promotion of Science.
†Center for Southeast Asian Studies, Kyoto University, 46 Shimoadachi-cho, Yoshida, Sakyo-ku,
Kyoto 606-8501, Japan. Tel: +81-75-753-7302. Email: katsukogure@gmail.com.

11. Introduction
Recent years have seen growing interest in the causal relationships between historicalevents and contemporary economic outcomes (see Nunn (2009, 2014) for reviews).
One feature of the more recent studies is the use of detailed historical data and contemporary microdata of individuals and/or households to identify the causal eﬀects
of history on outcomes (e.g., Dell (2010), Nunn and Wantchekon (2011)). This paper
discusses conceptual and empirical issues inherent in the causal inference following
the Rubin causal model, a framework for causal inference based on potential outcomes(Rubin (1974, 1977), Imbens and Rubin (2015)). The discussion presented is relevant
not only to the causal inference for historical persistence with microdata, but also to
the long-run impacts of treatments if the existence of the causal units of interest ispotentially aﬀected by treatments more generally (e.g., across generations).
We adopt the potential outcomes framework because it enables us to raise mosteﬀectively the issues inherent in the causal inference for historical persistence withmicrodata and many modern empirical works that examine causal questions adopt
this framework (see, e.g., Angrist and Pischke (2009), Duﬂo et al. (2008), Imbens andWooldridge (2009), Imbens and Rubin (2015)) (we do not adopt the econometric approach to causal modelling (see, e.g., Heckman and Vytlacil (2007), Heckman (2008)),
because historical impacts often go beyond the scope of relevant microeconomic theories and the existing studies do not follow it (see Nunn (2009, 2014))). Using anempirical example, we also illustrate a simple alternative approach with aggregateddata to avoid certain issues that is coherent with the Rubin causal model.
The paper proceeds as follows. For expository purposes, Section 2 provides abrief description of the Rubin causal model, specifying the major premises. Section
3 considers the causal inference for historical persistence with contemporary micro-

2

data and discusses fundamental problems inherent in the causal inference. We also
discuss a simple alternative approach to address these problems. Section 4 provides
an empirical example based on the approach and Section 5 concludes.

2. Overview of Causal Inference Using Potential Outcomes
Essential Elements of the Rubin Causal Model. The Rubin causal model
consists of three essential elements (e.g., Holland and Rubin (1988)). The ﬁrst isa set (population) of units, U , the size of which is denoted by N , indexed by i =1, . . . , N . Examples of units include individuals, households, ﬁrms, counties, states,
and countries. The second is a set of treatments, D, with each unit being exposed to
one of the treatments. For simplicity, we assume two treatments, Di = {1, 0}, where
Di = 1 if unit i is exposed to the treatment and Di = 0 if unit i is not. The third isa response variable, Y , that is recorded for each unit after its exposure to either of
the treatments.
Causal Inference. The Rubin causal model assumes that each unit i has two
potential outcomes, Yi (1) and Yi (0), where Yi (1) is the value of the response thatwould be observed if unit i received the treatment while Yi (0) is the value that would
be observed if the same unit did not. Let Yiobs denote the realized and observed
outcome: Yiobs = Yi (Di ) = Yi (1) · Di + Yi (0) · (1 − Di ). The potential outcomesenable us to deﬁne causal eﬀects at three levels: unit level, population level, andsubpopulation level (e.g., Holland and Rubin (1988)).
The unit-level causal inference is deﬁned as the diﬀerence between the two potential outcomes for the same unit:Yi (1) − Yi (0).
The population-level causal inference is deﬁned as the expectation of the diﬀerence3

in the unit-level causal eﬀect over population:
E[Yi (1) − Yi (0)].
The subpopulation-level causal inference is deﬁned in many ways. One deﬁnition isthe expectation of the diﬀerence in the unit-level causal eﬀect over the subpopulation
with covariates, Xi :E[Yi (1) − Yi (0)|Xi ].
Fundamental Problem of Causal Inference. For causal inference at any level,
we always face the problem that we can never observe both Yi (1) and Yi (0) at thesame time. We can observe, at most, either Yi (1) or Yi (0). Thus, it is impossible todirectly observe the causal eﬀects at all three levels (“fundamental problem of causal
inference,” Holland (1986)).
Assumptions. Causal inference relies on assumptions. Three key assumptions
are normally used. The ﬁrst is the stable unit treatment value assumption (SUTVA),
which requires that the potential outcomes of unit i are not aﬀected by the treatments
received by any other units and there are no multiple versions of treatments (Rubin(1980, 1986)). The second assumption is unconfoundedness (Rosenbaum and Rubin(1983)),1()
Yi (1), Yi (0) ⊥ Di |Xi .

Under this assumption, the treatment assignment, Di , is statistically independent of
the potential outcomes, Yi (1) and Yi (0), given Xi . The third assumption is overlap,
0 < P r(Di = 1|Xi ) < 1.
1

Unconfoundedness is closely related to the notion of exogeneity in the econometrics literature(Manski et al. (1992)). The term unconfoundedness is also referred to as “selection on observable”(Barnow et al. (1980)) and the “conditional independence assumption” (Lechner (2001), Angristand Pischke (2009)).

4

This assumption ensures overlap in the covariate distribution of treatments and controls. The combination of unconfoundedness and overlap is referred to as “strong
ignorability” (Rosenbaum and Rubin (1983)).
Identification. The three assumptions justify causal inference, as follows. Suppose that we are interested in learning the conditional average treatment eﬀect,
E[Yi (1) − Yi (0)|Xi ]. Under the three assumptions, the average treatment eﬀect canbe identiﬁed by relying only on observed outcomes:
E[Yi (1) − Yi (0)|Xi ] = E[Yi (1)|Xi ] − E[Yi (0)|Xi ]= E[Yi (1)|Xi , Di = 1] − E[Yi (0)|Xi , Di = 0]
= E[Yiobs |Xi , Di = 1] − E[Yiobs |Xi , Di = 0].
Since E[Yi (1)|Xi , Di = 1] and E[Yi (0)|Xi , Di = 0] do not depend on Di under theunconfoundedness assumption, the second equality holds. In addition, based on theoverlap assumption, we can estimate both E[Yiobs |Xi , Di = 1] and E[Yiobs |Xi , Di = 0]
for a subpopulation with covariates Xi .
Premises of the Rubin Causal Model. The Rubin causal model (summarized above) is based on two premises: (1) Units exist within a speciﬁc time periodand (2) the action of treatments and the measurement of outcomes take place on acommon unit (frameworks have also been developed to address any lack in parts of
the units within a speciﬁed time frame due to missing outcomes (dropout) following
non-compliance and “truncation-by-death” (e.g., Frangakis and Rubin (2002), Zhang
and Rubin (2003))). Holland (1986) discusses the two premises, emphasizing the signiﬁcance of the role of time in the causal inference versus the associational inference,the standard statistical model that simply relates two variables over population.
Types of Variables. Holland (1986) also discusses types of variables. Since
treatments must occur within a speciﬁc time period, variables are classiﬁed into two
5

types: pre-treatment variables and post-treatment variables (variables determined
before and after receiving the treatments, respectively). The latter may be aﬀected bytreatments while the former are not. Thus, it is possible to identify the causal eﬀects ofthe treatments by comparing post-treatment variables (outcomes) between treatment
and control groups with similar values of covariates (under the assumptions).

3. Causal Inference for Historical Persistence
Following the potential outcomes framework, this section considers the causal inference for historical persistence with contemporary microdata.

3.1 The Standard Approach
Let us ﬁrst look at the standard approach used in existing studies. These studies
consider historical events such as colonial institutions and Africa’s slave trade (e.g.,
Dell (2010), Nunn and Wantchekon (2011)). Here we assume a historical event (treatment) to be the protection of property rights in a speciﬁc country during the colonial
era and examine the long-run impacts on contemporary individual income (see, e.g.,
Acemoglu et al. (2005) for the importance of the protection of property rights for economic development). While some studies with aggregated data use historical eventsas instruments for the determinants of current domestic institutions (e.g., Acemoglu
et al. (2001)), we consider the direct impacts of a historical event on contemporary
individual outcomes following a standard regression framework (many existing studies follow it (see Nunn (2009, 2014))). For convenience, we assume no missing values
on the income and other relevant variables.
To examine the causal relationship, researchers may estimate something like thefollowing regression equation under linearity and constant treatment eﬀect assumptions:

6

′

′

Yij = α + ρDj + Xij β + Zj γ + ϵij ,(1)where Yij is the income of individual i in region j; Dj is the treatment variable, whichtakes the value 1 if individual i lives in region j where property rights were protectedduring the colonial era and 0 otherwise; Xij is a vector of relevant individual characteristics; Zj is a vector of relevant regional characteristics; ρ is the parameter of interest.
One major concern about the identiﬁcation of ρ is the endogeneity of the protectionof property rights, namely, that the exogenous assumption, ϵij ⊥ Dj |Xij , Zj , may nothold. Existing studies address such endogeneity problems on the variable of interest
through quasi-experimental designs (e.g., instrumental variable strategies, regression
discontinuity designs) with a limited subsample, which may satisfy the assumption.
Another concern is obtaining a valid inference. Since the variable of interest, Dj ,varies only at the regional level, not the individual level, researchers may be concernedthat the failure to account for the presence of common group errors generates estimated standard errors dramatically biased downward (Moulton (1986)). To correct
the standard errors, researchers may use cluster-robust standard errors for inference,
allowing for arbitrary correlation among the errors, ϵij , within each region.

3.2 Remarks on the Standard Approach
The standard approach, however, may face some fundamental problems. We illustrate the problems in Figure 1a, which depicts the time frame for the evaluation.
Unlike the evaluation of standard social programs such as job training (e.g., LaLonde(1986)), the evaluation of historical events involves a long time span, the durationof which often exceeds several hundred years (i.e., easily exceeds a human’s life expectancy). This innate distinctive feature can lead to the following conceptual andempirical issues.
Population. First, population is deﬁned for contemporary individual units (not7

those having been directly exposed to the treatments, unlike the evaluation of standard social programs). In this context, since all individual units (denoted by N )emerge after the treatments, their existence is potentially aﬀected by the treatments(and subsequent various factors including the characteristics of ancestors and previous regional characteristics (i.e., intermediate variables (mediators) prior to theemergence of the individual units), most of which are unobserved to researchers). In
other words, the distribution of the population (and samples drawn from the population) can be aﬀected by the treatments (and intermediate variables). Thus, with an
ill-deﬁned population, it is not feasible to apply the potential outcomes framework
to those individual units and the choice of individual units as causal units generally
introduces post-treatment bias (detailed below).
Covariate Selection. Second, covariate selection in empirical works is often
guided by relevant economic theories and ﬁndings in related literature (e.g., Cameron
and Trivedi (2005)). However, such covariate selection may not always apply in thiscontext, because the variables selected for covariates in other studies are often posttreatment variables for which the adjustments generally introduce post-treatment bias
(Rosenbaum (1984) or “bad control” (Angrist and Pischke (2009)); historical impacts
often go beyond the scope of the relevant economic theories and empirical studies.
In equation (1), the variables of individual characteristics, Xij , are post-treatment
variables. The variables of regional characteristics, Zj , may include not only pretreatment variables, Zjpre , but also post-treatment variables, Zjpost . The adjustments
for Xij and Zjpost in the regression generally introduce post-treatment bias.
SUTVA. Third, the validity of SUTVA may also be of concern. For example,
some individuals in a control (treatment) region might actually have been born in atreatment (control) region, spent some time there, and then migrated to the control(treatment) region. In this case, the assumption of no multiple versions of treat8

ment may be violated. In addition, potential outcomes of an individual might beaﬀected by others with diﬀerent versions of treatment through social interactions.
The assumption of no interference among individual units may also be violated.
Inference. Fourth, with an ill-defined population, statistical inference for parameters of the population may not be valid, because it is premised on a well-defined
population; the use of cluster-robust standard errors for inference may be irrelevant.

3.3 The Identification Problems
We now more formally consider the identiﬁcation problems following the potential
outcomes framework. Here we consider the problems for our choice of individual
units as causal units. We do not consider the problems for our adjustments forpost-treatment variables. This is because the latter problems have long been recognized and discussed in the existing literature (e.g., Rosenbaum (1984), Wooldridge(2005), Lechner (2008), Angrist and Pischke (2009), Elwert and Winship (2014), Huber (2015), Acharya et al. (2016), Montgomery et al. (2018)) but the former have not.
For simplicity, we assume that no pre-treatment variables are recorded.
First, in the causal inference, to avoid having an ill-deﬁned population (discussed
above), we specify a larger population consisting of all potential individuals (i.e.,
superpopulation, denoted by M ), each of whom can potentially exist at the time of
the “follow-up survey” (depicted in Figure 1a). Importantly, its distribution is not
aﬀected by the treatments (and intermediate variables). Thus, it is feasible to apply
the potential outcomes framework to those potential individuals.
An ideal experiment (hypothetical one) would be that all potential individuals inthe superpopulation are randomly assigned to the treatment or control group andthat all of them are actually observed at the time of the follow-up survey. Let Yij (Dj )denote the potential income of potential individual i in region j given Dj . The pa-

9rameter of our interest is the average treatment eﬀect (ATE) for the superpopulation,τsp = E[Yij (1) − Yij (0)] = E[Yij (1)] − E[Yij (0)],(we use the subscript “sp” (“fs” (given below)) for the superpopulation (ﬁnite sample)). However, what we can actually observe (in the real world) is quite diﬀerent, as
follows. Let Sij (Dj ) denote the potential outcome for the existence of potential individual i in region j given Dj . For the sake of brevity, we assume that the existence ofeach potential individual depends only on his or her treatment assignment, although
it potentially depends on both his or her treatment assignment and intermediatevariables. SUTVA is assumed to hold. Sij (1) = 1 (Sij (0) = 1) implies that potential
individual i in region j would actually exist when assigned treatment (control) while
Sij (1) = 0 (Sij (0) = 0) implies that the individual would not. Then, what we actuallyobserve is the average observed diﬀerence between individuals who actually existed
in the treatment and control groups,
τ̂f s = E[Yijobs |Sijobs = 1, Dj = 1] − E[Yijobs |Sijobs = 1, Dj = 0].
We again use the superscript “obs” to distinguish between potential outcomes, which
are not always observed, and the observed outcome.
We note that this comparison is problematic if the treatments aﬀect the existenceof potential individuals. For example, if a historical event signiﬁcantly aﬀected thesurvival of ancestors in such a way that poor, less educated, or low-ability peopleor people in poor health were more likely to die, then the observed and unobserved
characteristics of contemporary individuals (i.e., the descendants of survivors) that
may aﬀect the outcomes of interest can systematically diﬀer between the treatment
and control groups. Importantly, this sample selection problem (e.g., Heckman (1979))
can arise even when the historical event is randomized at the regional level.
10

To identify the ATE based on a ﬁnite sample of observed individuals, we would
require the assumption that the historical event is completely randomized at thecontemporary individual level:(Yij (1), Yij (0), Sij (1), Sij (0)) ⊥ Dj .
This assumption implies that the historical event has no systematic eﬀect on theexistence of potential individuals. However, in reality, whether or not each individual
exists depends on his or her treatment assignment and we cannot always deﬁne Yij (1)and Yij (0) for all potential individuals.
To see more details about this, we follow the idea of the principal stratiﬁcation
approach, a statistical framework for making causal inferences with intermediate variables, developed to address problems regarding noncompliance, censoring-by-death,and surrogate outcomes (Frangakis and Rubin (2002)). The approach ﬁrst partitionsindividual units into latent classes or subgroups (“principal strata”) deﬁned by thejoint potential values of an intermediate variable (e.g., a censoring indicator variable)
under both the observed and the counterfactual treatment conditions and then makes
causal inferences within the principal strata. The key idea is that because principal
strata are not aﬀected by treatment assignment, it is possible to make a causal inference within each stratum; the stratum variable can be treated as a pre-treatment
covariate. This appraoch generalizes the “local average treatment eﬀect” (LATE)
framework (Imbens and Angrist (1994), Angrist et al. (1996)); a causal eﬀect withina principal stratum can be interpreted as a LATE.
In our case, we can classify the individuals who actually existed (Sijobs = 1) into
the following three latent subgroups according to the joint values of the two potential
existence indicators:

11• EE = {i : Sij (1) = Sij (0) = 1}, those who would exist regardless of theirtreatment assignment; both Yij (1) and Yij (0) are deﬁned in R (the set of real
numbers);• EN = {i : Sij (1) = 1 and Sij (0) = 0}, those who would exist if assigned
treatment but would not exist if assigned control; Yij (1) ∈ R and Yij (0) = ∗ (forSij (Dj ) = 0, we deﬁne the outcome as “∗” (“missing” or “censored”) following
the truncation-by-death literature (e.g., Zhang and Rubin (2003)));• N E = {i : Sij (1) = 0 and Sij (0) = 1}, those who would exist if assigned control
but would not exist if assigned treatment; Yij (1) = ∗ and Yij (0) ∈ R.
As discussed above, since principal strata are not aﬀected by the treatment assignment (although deﬁned by a post-treatment variable), it is possible to make a causal
inference within each stratum. However, because causal eﬀects are deﬁned as comparisons of potential outcomes on a common set of units (e.g., Rubin (1974, 2005)),
the individual-level causal eﬀect is well deﬁned on R only for the EE group.
In reality, we cannot directly observe the principal strata for the individuals because we cannot observe both Sij (1) and Sij (0) at the same time. We can only observe
the following two groups based on the observed treatment assignment and the observed existence indicator (OBS(Dj , Sijobs )):• OBS(1, 1) = {i : Dj = 1, Sijobs = 1}, those who existed in the treatment group;• OBS(0, 1) = {i : Dj = 0, Sijobs = 1}, those who existed in the control group.
Each individual is observed to fall into one of the two groups but also belongs to an
unobserved principal stratum. Their relationship is summarized in Table 1.
Table 1 reveals that OBS(1, 1) and OBS(0, 1) consist of a mixture of the EE, EN
groups and the EE, N E groups, respectively; these two groups involve diﬀerent combinations of principal strata, suggesting that a comparison of the two outcomes is not12

an “apples-to-apples” comparison, but an “apples-to-oranges” comparison. Therefore,
the average observed diﬀerence, E[Yijobs |Sijobs = 1, Dj = 1] − E[Yijobs |Sijobs = 1, Dj = 0],
is not the average causal eﬀects, E[Yij (1)] − E[Yij (0)].
To compare the outcomes for a common set of groups, which is a causal inference,
one can assume that each individual would always exist regardless of his or her treatment assignment: Sij (Dj ) = 1 for all Dj . This existence assumption reduces the threeprincipal strata only to EE and thus allows us to identify the causal eﬀects for theEE group, where both Yij (1) and Yij (0) are well deﬁned in R. This assumption would
also require that all potential individuals always exist. In this case, the population is
identical to the superpopulation and its distribution is not aﬀected by the treatment
assignment: The population is well deﬁned for contemporary individual units.

3.4 An Alternative Approach
The assumptions discussed above to justify the causal inference cannot be empiricallyexamined regarding their validity. To avoid imposing such untenable assumptions,this subsection considers a simple alternative approach that makes the causal inference with clusters or groups (i.e., regions), rather than individual units. In manycases, the requirements of the Rubin causal model are met: (1) The clusters or groups
stably exist throughout a speciﬁed time frame and (2) the action of treatments andthe measurement of outcomes take place on a common unit.2 Although we are required to change the causal question of interest to that at the cluster or group level,
we can identify the causal eﬀects through a more transparent analysis, as follows.
Data Structure. Figure 1b depicts the data structure. The individual-level data
in Figure 1a are now aggregated at the cluster (regional) level: The unit of analysis iscluster, not individual. We use Cj , where j = 1, . . . , G, to denote each cluster, the size
2

In some cases, the formation of geographic units (e.g., state formation) may be aﬀected byhistorical events (e.g., Alesina and Spolaore (2003)).

13

of which is denoted by Nj , where∑G

j=1 Nj = N .

We assume that regional-level pre-treatment variables, Zjpre , and post-treatment variables, Zjpost , are available. Whileindividual characteristics, Xij , and outcome, Yij , are still observed at the individuallevel, the aggregated data are used for analysis. For simplicity, we assume that allindividual units (who actually existed) within all clusters are sampled.
Essential Elements. The three essential elements of the Rubin causal model are
as follows: (1) The population of units is G clusters, U = {C1 , . . . , CG }, (2) the set oftreatments is Dj = {1, 0}, where Dj = 1 if cluster j protected property rights during
the colonial era and Dj = 0 if cluster j did not, and (3) the response variable, Yj , isregional income, which is deﬁned using the individual-level outcome, Yij . We can alsodeﬁne various response variables using other post-treatment variables in Zjpost and Xij .
Assumptions. The three key assumptions (SUTVA, unconfoundedness, andoverlap) are assumed to hold. The plausibility of the unconfoundedness and overlap assumptions is assumed to be improved by innovative quasi-experimental designs,
as generally done in existing studies (see Nunn (2009, 2014)). Formally, the unconfoundedness assumption is described as()
Yj (1), Yj (0) ⊥ Dj |Zjpre .

The overlap assumption is given as
0 < P r(Dj = 1|Zjpre ) < 1.
Identification. Under the three assumptions, the conditional average treatmenteﬀect, E[Yj (1) − Yj (0)|Zjpre ], can be identiﬁed as follows:
E[Yj (1) − Yj (0)|Zjpre ] = E[Yj (1)|Zjpre ] − E[Yj (0)|Zjpre ]= E[Yj (1)|Zjpre , Dj = 1] − E[Yj (0)|Zjpre , Dj = 0]
= E[Yjobs |Zjpre , Dj = 1] − E[Yjobs |Zjpre , Dj = 0].
14

Estimation. For simplicity, we suppose that the treatment eﬀect is constant andthe outcome is linear in Dj and Zjpre , where Zjpre is a K-dimensional column vector.
Provided G > K + 2, we estimate the following regression equation to identify theaverage treatment eﬀect:′
Yj = α + ρDj + Zjpre γ + ϵj ,∑Njwhere Yj =i=1 Yij

Nj

.

(2)

Here we consider the group average, Yj , as the dependent variable. The unconfoundedness assumption implies that the exogenous assumption, ϵj ⊥ Dj |Zjpre , holds andthe clusters are assumed to be independent of each other. Under the assumptions,the unweighted between-groups estimator consistently estimates the average treatment eﬀect (it is noted that the number of individual units at each cluster (regional)
level is potentially aﬀected by the treatments).
Here we touch on the diﬀerence between this approach and that proposed in Donald and Lang (2007). Both approaches estimate between-groups estimators despite
individual-level data being available, speciﬁcally, when an outcome variable varies
among individual units and the variable of interest varies only at the cluster level.
The two approaches have diﬀerent motivations. Our motivation is simple: The population of our interest is clusters or groups, not individual units. In contrast, theirmotivation is to obtain a valid inference in the context of cluster sampling with asmall number of clusters, as is typically the case for diﬀerence-in-diﬀerences estimation. Their population of interest is still individual units, not clusters or groups; unlike
our case, the population is assumed to be well deﬁned for individual units. They are
motivated by the cluster-robust inference being valid when the number of clusters
is large (Hansen (2007)) but not when it is small. To solve the inference problem,
they propose estimating the between-groups estimator (see Donald and Lang (2007),
Wooldridge (2010, Chapter 20) for details).
15

4. An Empirical Example
This section provides an empirical example based on the alternative approach as wellas the standard one using the inﬂuential Dell (2010) paper, which explicitly follows
the potential outcomes framework for studying historical persistence at the microlevel. Dell examines the long-run impacts of the mita, an extensive forced mining
labor system the Spanish government instituted in Peru and Bolivia between 1573
and 1812, on contemporary individual outcomes. Focusing on a sharp change in themita boundary, she uses a regression discontinuity (RD) approach to examine thehistorical persistence (see, e.g., Imbens and Lemieux (2008), Lee and Lemieux (2010)
for a description of regression discontinuity designs using the potential outcomesframework). Although she also examines the underlying mechanisms, we focus on
estimation of the causal eﬀects of the mita on current living standards (equivalenthousehold consumption in 2001 and the prevalence of stunting among children aged
6-9 in 2005).
Estimation. We additionally estimate the following regression equation:′

cdb = α + γmitad + Xd β + f (geographic locationd ) + ϕb + ϵdb ,∑Nd
i=1 cidb
where cdb =
.
Nd

(3)

Unlike Dell’s (2010) approach, we use clusters (districts) as the causal units. The
population of our interest is districts, not individual units: Our interest is in thecausal eﬀects of the mita on current living standards for districts, not individuals.
The clusters are assumed to meet the requirements of the Rubin causal model.
Nd denotes the number of individual units in district d. cdb is the mean outcome
for district d along segment b of the mita boundary. mitad is an indicator variableequal to 1 if district d contributed to the mita and 0 otherwise. Xd is a vector of16

covariates that includes elevation and slope for district d. f (geographic locationd ) is
the RD polynomial, which controls for smooth functions of geographic location. ϕb
is a set of boundary segment ﬁxed eﬀects. The descriptive statistics are presented inAppendix Table A1; see Dell (2010) for detailed data information.
Assumptions. The ﬁrst key identifying assumption in the RD approach is that all
relevant factors are continuous at the mita boundary. Based on Dell’s careful work inchecking the validity of the assumption (see Dell (2010, Section 3.2)), we assume thatthe smoothness assumption holds (although Dell uses individuals as causal units, sheconsiders the validity of the smoothness assumption for district-level pre-treatment
variables). The second key identifying assumption is that the functional form of theregression model is correct. Because she considers various functional forms regarding
the RD polynomial, we simply follow her three speciﬁcations: (1) cubic polynomial
in latitude and longitude, (2) cubic polynomial in distance to Potosı́ (km), and (3)cubic polynomial in distance to the mita boundary (km).
An additional assumption to validate the RD design is no selective sorting aroundthe mita boundary. Since we use geographic units (clusters) as causal units, it isplausible to assume that the no-manipulation assumption holds. If we consider thisassumption from the individual-unit point of view, the assumption is relevant to theindividual units having been directly exposed to the treatments, not the contemporary
individual units. For that reason, Dell (2010), using contemporary individual units as
causal units, provides an unusual discussion regarding the validity of the assumption,3
which is not generally found in the standard regression discontinuity design literature
3“(A)n additional assumption often employed in RD is no selective sorting across the treatment
threshold. This would be violated if a direct mita eﬀect provoked substantial out-migration ofrelatively productive individuals, leading to a larger indirect eﬀect. Because this assumption may
not be fully reasonable, I do not emphasize it. Rather, I explore the possibility of migration as aninteresting channel of persistence, to the extent that the data permit.” (Dell (2010, p. 1876)). Thisimplies that SUTVA (discussed above) might be violated, although it seems that migration was low.

17

(e.g., Imbens and Lemieux (2008), Lee and Lemieux (2010)).
Results. Table 2 reports the estimated impacts of the mita on equivalent household consumption (panel A) and prevalence of stunting in children aged 6-9 (panel B).
We report the estimates based on individual-level data in columns 1-3 and districtlevel data in columns 4-6. Panels A/B-1, -2, and -3 report the estimates based on
the three diﬀerent speciﬁcations mentioned above. In the former estimation, basedon our discussions above, to justify the causal inference, we simply assume that the
population is identical to the superpopulation: Potential individuals always existed.
The main ﬁndings are summarized as follows. First, the estimates in columns 1-3
in panel A diﬀer slightly from those in Dell (2010) (columns 1-3 of Table 2). This isbecause we avoid adjusting for demographic variables (the number of infants, children,
and adults in the household), which are post-treatment variables. However, because
these variables are little aﬀected by the mita (columns 1-3 of Appendix Table A2),4 thetwo results are quite similar in regard to the magnitude of the impacts and the levelof statistical signiﬁcance. We also perform the same exercises for the district-level
regressions and ﬁnd similar results (columns 4-6 of Appendix Table A2), implyingthat the adverse impacts of the mita are not driven by its potential eﬀects on the
post-treatment variables.
Second, the estimated impacts of the mita on the equivalent household consumption are similar in columns 1-3 and 4-6 (panel A). However, the estimated impacts ofthe mita on the prevalence of stunting in children diﬀer between columns 1-3 and 4-6(panel B). Unlike Dell’s results, we ﬁnd positive impacts for the speciﬁcation of a cubic polynomial in latitude and longitude; these impacts are, however, not statisticallysigniﬁcant. In addition, although negative impacts are found for the speciﬁcations of
4

Signiﬁcant impacts are found only for the number of children in the speciﬁcation of a cubic
polynomial in latitude and longitude (panel B).

18

a cubic polynomial in distance to Potosı́ and the mita boundary, the estimated impacts become smaller when the sample is limited to that closer to the mita boundary.
Also, the signiﬁcant impacts vanish when the sample is limited to that within 50 kmof the mita boundary. These results imply that more careful consideration regarding
the mita impacts might be needed because the untenable assumptions imposed in theanalyses might be violated.
Although the population of interest as well as the units of analysis diﬀer between
the estimations based on individual-level data and aggregated data, we touch on thereasons why the estimated impacts of the mita are similar in panel A, but diﬀerent
in panel B. First, we note that the two estimators are identical when all clusters havethe same number of observations (see, e.g., Donald and Lang (2007) and Wooldridge(2010, Chapter 20) for related discussions). Given this, the following two facts mainly
cause the diﬀerent results: (1) The number of individual units is relatively similar inpanel A, but quite diﬀerent in panel B and (2) the covariate distribution for the speciﬁcation of a cubic polynomial in latitude and longitude is sensitive to the diﬀerencein group size, while that for the speciﬁcations of a cubic polynomial in distance toPotosı́ and the mita boundary is not (see Appendix Table A1).

5. Concluding Remarks
In this paper, we have raised issues inherent in the causal inference for historicalpersistence with microdata following the potential outcomes framework. When microdata are available, it is tempting to directly use such microdata for the analysis
to utilize the information most eﬀectively. However, in this distinct context, thechoice of individual units as causal units generally introduces bias because their existence is potentially aﬀected by the treatments. Also, covariate selection guided

19

by relevant economic theories and empirical ﬁndings often contains post-treatment
variables, which may introduce another potential bias. Using an empirical example,
we have illustrated a simple alternative approach to avoid such problems that makes
the causal inference with clusters or groups, not individual units. The approach iscoherent with the Rubin causal model.
The discussion presented here is relevant not only to the causal inference for historical persistence with microdata, but also to the long-run impacts of treatments if
the existence of the causal units of interest is potentially aﬀected by treatments moregenerally (e.g., across generations). We believe our discussion can help in designing/analyzing future relevant observational and experimental studies/data and leadto more transparent research. We will also develop a general framework to address
such causal inference at the micro level in our future work.

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25

Table 1: Observed Data Pattern and Unobserved Principal Strata

OBS(Dj , Sijobs ) Dj Sijobs Yijobs Unobserved Principal Strata
OBS(1, 1)1
1 ∈R
EE, EN
OBS(0, 1)0
1 ∈R
EE, N E

26

Table 2: Impacts of the Mita on Living Standards
Units:
Sample within:Mita
R-squared
Mita
R-squared
Mita
R-squared
Clusters
Observations
Units:
Mita
R-squared
Mita
R-squared
Mita
R-squared
Clusters
Observations

A. Log Equivalent Household Consumption (2001)
Households
Districts< 100 km < 75 km< 50 km< 100 km < 75 km< 50 kmof Bound. of Bound. of Bound.
of Bound. of Bound. of Bound.
(1)
(2)
(3)
(4)
(5)
(6)
A-1. Cubic Polynomial in Latitude and Longitude-0.282-0.217-0.335-0.166-0.115-0.192(0.201)(0.210)(0.220)(0.196)(0.217)(0.236)
0.059
0.059
0.068
0.391
0.370
0.413
A-2. Cubic Polynomial in Distance to Potosı́
-0.337*** -0.308*** -0.330***-0.339*** -0.300*** -0.318***(0.088)(0.102)(0.098)(0.092)(0.102)(0.103)
0.046
0.035
0.045
0.276
0.214
0.283
A-3. Cubic Polynomial in Distance to Mita Boundary-0.278***-0.232**-0.225**-0.295***-0.230**-0.223**(0.079)(0.090)(0.093)(0.089)(0.098)(0.102)
0.044
0.041
0.038
0.277
0.249
0.194
71
60
52
71
60
52
1,478
1,161
1,013
71
60
52
B. Children Aged 6-9 Having Stunted Growth (2005)
ChildrenDistricts
B-1. Cubic Polynomial in Latitude and Longitude
0.070
0.084*
0.087*-0.012-0.008-0.021(0.043)(0.046)(0.048)(0.025)(0.027)(0.029)
0.051
0.020
0.017
0.388
0.298
0.211
B-2. Cubic Polynomial in Distance to Potosı́
0.080***
0.078***
0.078***
0.046***
0.031*
0.025(0.021)(0.022)(0.024)(0.016)(0.016)(0.018)
0.049
0.017
0.013
0.330
0.261
0.156
B-3. Cubic Polynomial in Distance to Mita Boundary
0.073***
0.061***
0.064***
0.047***
0.025*
0.021(0.023)(0.022)(0.023)(0.015)(0.015)(0.018)
0.040
0.015
0.013
0.293
0.236
0.147
289
239
185
289
239
185
158,848
115,761
100,446
289
239
185

Notes: The table reports ordinary least squares (OLS) estimates where the unit of observation is the household (child) in columns 1-3 and the district in columns 4-6. Robust
standard errors, adjusted for clustering by district, are reported in parentheses in columns
1-3 and robust standard errors are reported in parentheses in columns 4-6. The dependent
variable in panel A is log equivalent household consumption in columns 1-3 and the district
mean of log equivalent household consumption in columns 4-6. The dependent variable inpanel B is an indicator variable equal to 1 if the child has stunted growth and 0 otherwise
in columns 1-3 and the district mean of children aged 6-9 having stunted growth in columns
4-6. Mita is an indicator variable equal to 1 if the (household’s/child’s) district contributed
to the mita and 0 otherwise. Panel A/B-1 includes a cubic polynomial in the latitude andlongitude of the observation’s district capital. Panel A/B-2 includes a cubic polynomial
in Euclidean distance (km) from the observation’s district capital to Potosı́. Panel A/B-3
includes a cubic polynomial in Euclidean distance (km) to the nearest mita boundary. All
regressions include controls for elevation, slope, and boundary segment ﬁxed eﬀects. The
sample in columns 1 and 4 includes observations whose district capitals are located within
100 km of the mita; this threshold is reduced to 75 km in columns 2 and 5 and 50 km incolumns 3 and 6. *** p < 0.01; ** p < 0.05; and * p < 0.1.

2728(b) An Alternative Approach

Figure 1: Two Approaches to Causal Inference for Historical Persistence(a) The Standard ApproachAppendix
Table A1: Descriptive Statistics
Units:
Sample Within:
Number of households
Log equivalenthousehold consumption
Mita
Elevation
SlopeLongitude
LatitudeLongitude2
Latitude2
Longitude*Latitude
Longitude3
Latitude3
Longitude2 *Latitude
Longitude*Latitude2
Distance to Potosı́
Distance to Potosı́2Distance to Potosı́3
Distance to mita bound.
Distance to mita bound.2
Distance to mita bound.3
Bound. segm. dummy I
Bound. segm. dummy II
Bound. segm. dummy III
Observations

A. Log Equivalent Household Consumption (2001)
Households
Districts< 100 km < 75 km< 50 km< 100 km < 75 kmof Bound. of Bound. of Bound.
of Bound. of Bound.
20.81719.350(12.312)(9.251)
5.877
5.799
5.848
5.839
5.805
(1.010)(0.915)(0.855)(0.401)(0.362)
0.752
0.716
0.674
0.718
0.700
(0.432)(0.451)(0.469)(0.453)(0.462)
3.841
3.824
3.827
3.792
3.786
(0.378)(0.389)(0.383)(0.408)(0.400)
7.130
8.319
8.548
7.784
8.615
(4.124)(3.699)(3.649)(4.106)(3.771)-0.3350.046
0.106-0.1050.123(1.203)(0.921)(0.777)(1.110)(0.885)-0.054-0.340-0.412-0.202-0.393(0.820)(0.638)(0.578)(0.765)(0.621)
1.559
0.849
0.614
1.226
0.785
(1.742)(0.900)(0.491)(1.473)(0.822)
0.675
0.522
0.503
0.618
0.534
(0.533)(0.368)(0.335)(0.488)(0.387)-0.617-0.252-0.113-0.435-0.242(1.071)(0.689)(0.527)(0.883)(0.652)-1.956-0.1420.188-1.0080.046(4.497)(2.041)(0.836)(3.724)(1.794)0.163-0.200-0.284-0.015-0.242(1.004)(0.584)(0.479)(0.893)(0.600)0.900-0.012-0.1880.385-0.096(2.407)(1.147)(0.519)(1.874)(1.030)-0.451
0.014
0.114-0.1560.063(1.384)(0.703)(0.416)(1.062)(0.659)
8.964
9.484
9.587
9.262
9.586
(1.450)(1.036)(0.814)(1.300)(0.983)82.45391.01792.57087.45092.836(24.911)(18.779)(15.357)(22.829)(18.004)775.093882.584899.934
839.133
907.258(328.449) (259.657) (218.859)(307.124) (251.264)
0.406
0.281
0.233
0.380
0.290
(0.286)(0.174)(0.126)(0.263)(0.170)
0.247
0.109
0.070
0.213
0.113
(0.288)(0.122)(0.065)(0.262)(0.118)
0.181
0.051
0.024
0.147
0.052
(0.264)(0.079)(0.031)(0.239)(0.075)
0.086
0.078
0.083
0.099
0.083
(0.280)(0.269)(0.276)(0.300)(0.279)
0.289
0.138
0.100
0.197
0.100
(0.453)(0.345)(0.300)(0.401)(0.303)
0.384
0.477
0.484
0.451
0.517
(0.487)(0.500)(0.500)(0.501)(0.504)
1,478

1,161

1,013

A–1

71

60

< 50 kmof Bound.
19.481(9.373)5.848(0.358)0.654(0.480)3.794(0.391)
8.742(3.798)0.132(0.767)-0.447(0.586)0.594(0.510)0.537(0.363)-0.133(0.535)0.221(0.839)-0.309(0.535)-0.195(0.540)0.122(0.441)
9.632(0.815)93.430(15.372)912.200(219.335)
0.243(0.127)0.075(0.066)0.026(0.031)0.077(0.269)0.077(0.269)0.519(0.505)52
Continue

Table A1: Descriptive Statistics
Units:
Sample Within:
Number of childrenChildren having
stunted growth
Mita
Elevation
SlopeLongitude
LatitudeLongitude2
Latitude2
Longitude*Latitude
Longitude3
Latitude3
Longitude2 *Latitude
Longitude*Latitude2
Distance to Potosı́
Distance to Potosı́2Distance to Potosı́3
Distance to mita bound.
Distance to mita bound.2
Distance to mita bound.3
Bound. segm. dummy I
Bound. segm. dummy II
Bound. segm. dummy III
Observations

B. Children Aged 6-9 Having Stunted Growth (2005)
Children Aged 6-9
Districts< 100 km < 75 km< 50 km< 100 km
< 75 km< 50 kmof Bound. of Bound. of Bound.
of Bound. of Bound. of Bound.
549.647484.356542.951(1365.381) (678.517) (736.596)
0.346
0.391
0.403
0.380
0.392
0.412
(0.476)(0.488)(0.491)(0.125)(0.120)(0.116)
0.780
0.707
0.684
0.702
0.678
0.665
(0.414)(0.455)(0.465)(0.458)(0.468)(0.473)
3.911
3.908
3.896
3.864
3.899
3.908
(0.388)(0.427)(0.411)(0.482)(0.475)(0.447)
6.414
7.724
7.890
8.021
8.210
8.245
(3.917)(3.489)(3.478)(3.800)(3.585)(3.591)-0.547-0.149-0.0800.014
0.009-0.003(1.225)(0.903)(0.798)(1.077)(0.921)(0.808)0.017-0.312-0.4180.029-0.037-0.154(0.822)(0.636)(0.552)(0.763)(0.744)(0.688)
1.800
0.837
0.643
1.157
0.845
0.650
(1.846)(0.880)(0.600)(1.266)(0.902)(0.639)
0.676
0.501
0.479
0.580
0.553
0.494
(0.584)(0.441)(0.393)(0.538)(0.499)(0.405)-0.694-0.187-0.089-0.285-0.168-0.018(1.159)(0.662)(0.549)(0.822)(0.732)(0.604)-2.451-0.2800.007-0.372-0.151-0.033(4.842)(1.898)(1.097)(3.160)(1.993)(1.206)0.230-0.187-0.3010.213
0.117-0.063(1.050)(0.677)(0.527)(0.901)(0.831)(0.648)1.186-0.013-0.172
0.310
0.175
0.059
(2.606)(1.047)(0.636)(1.529)(1.158)(0.734)-0.657-0.0370.039-0.136-0.0800.016(1.491)(0.698)(0.499)(0.926)(0.806)(0.569)
8.735
9.301
9.434
9.204
9.247
9.320
(1.486)(1.022)(0.858)(1.201)(1.035)(0.847)78.51387.55989.73886.15686.56687.580(25.386)(18.606)(16.060)(21.373)(18.555)(15.410)723.445833.387
860.361818.516819.519829.211(333.028) (257.969) (227.659)(290.890)(253.693) (213.211)
0.447
0.292
0.244
0.417
0.326
0.243
(0.299)(0.183)(0.141)(0.273)(0.202)(0.144)
0.290
0.119
0.079
0.248
0.147
0.079
(0.302)(0.127)(0.076)(0.263)(0.146)(0.074)
0.218
0.057
0.030
0.173
0.076
0.029
(0.277)(0.083)(0.037)(0.238)(0.099)(0.035)
0.097
0.109
0.109
0.225
0.230
0.249
(0.296)(0.311)(0.311)(0.418)(0.422)(0.433)
0.342
0.156
0.093
0.225
0.192
0.119
(0.475)(0.362)(0.290)(0.418)(0.395)(0.325)
0.278
0.348
0.369
0.329
0.310
0.297
(0.448)(0.476)(0.483)(0.471)(0.463)(0.458)
158,848

115,761

100,446

289

239

185

Notes: Panels A and B present the means and standard deviations for the variables used in the regressions
with equivalent household consumption and children aged 6-9 having stunted growth, the latter of which arereported in parentheses. The unit of observation is the household (child) in columns 1-3 and the district incolumns 4-6. The sample in columns 1 and 4 includes observations from those whose district capitals arelocated within 100 km of the mita; this threshold is reduced to 75 km in columns 2 and 5 and 50 km incolumns 3 and 6.

A–2

Table A2: Impacts of the Mita on Demographic Characteristics
Units:
Sample within:Mita
R-squared
Mita
R-squared
Mita
R-squared
Clusters
Observations
Units:
Mita
R-squared
Mita
R-squared
Mita
R-squared
Clusters
Observations

A. Number of Infants (2001)
Households
Districts< 100 km < 75 km< 50 km< 100 km < 75 km< 50 kmof Bound. of Bound. of Bound.
of Bound. of Bound. of Bound.
(1)
(2)
(3)
(4)
(5)
(6)
A-1. Cubic Polynomial in Latitude and Longitude
0.033
0.105
0.096
0.075
0.147
0.149
(0.087)(0.104)(0.118)(0.096)(0.113)(0.127)
0.028
0.026
0.031
0.430
0.416
0.483
A-2. Cubic Polynomial in Distance to Potosı́
0.020
0.014
0.015
0.041
0.044
0.030
(0.050)(0.059)(0.057)(0.056)(0.062)(0.063)
0.023
0.018
0.024
0.343
0.303
0.376
A-3. Cubic Polynomial in Distance to Mita Boundary
0.018
0.013
0.020
0.034
0.033
0.041
(0.050)(0.054)(0.054)(0.054)(0.060)(0.062)
0.021
0.019
0.023
0.341
0.308
0.305
71
60
52
71
60
52
1,478
1,161
1,013
71
60
52
B. Number of Children (2001)
Households
Districts
B-1. Cubic Polynomial in Latitude and Longitude
0.264*
0.326**
0.340*
0.290*
0.377*
0.435**(0.138)(0.157)(0.175)(0.169)(0.196)(0.209)
0.038
0.028
0.032
0.537
0.501
0.527
B-2. Cubic Polynomial in Distance to Potosı́
0.055
0.074
0.072
0.014
0.046
0.062
(0.084)(0.104)(0.110)(0.095)(0.116)(0.130)
0.026
0.017
0.021
0.338
0.300
0.339
B-3. Cubic Polynomial in Distance to Mita Boundary
0.029
0.075
0.076
-0.0020.049
0.053(0.077)(0.089)(0.090)(0.089)(0.102)(0.104)
0.027
0.019
0.019
0.362
0.314
0.298
71
60
52
71
60
52
1,478
1,161
1,013
71
60
52
Continue

A–3

Table A2: Impacts of the Mita on Demographic Characteristics
C. Number of Adults (2001)
Households
Districts< 100 km < 75 km< 50 km< 100 km < 75 km< 50 kmSample within: of Bound. of Bound. of Bound.
of Bound. of Bound. of Bound.
(1)
(2)
(3)
(4)
(5)
(6)
C-1. Cubic Polynomial in Latitude and Longitude
Mita-0.100
0.086
0.164
0.105
0.299
0.343
(0.188)(0.203)(0.217)(0.233)(0.229)(0.233)R-squared
0.026
0.026
0.045
0.214
0.279
0.452
C-2. Cubic Polynomial in Distance to Potosı́
Mita-0.039-0.015-0.030-0.011
0.017-0.009(0.089)(0.098)(0.093)(0.134)(0.148)(0.138)R-squared
0.026
0.020
0.026
0.175
0.122
0.219
C-3. Cubic Polynomial in Distance to Mita BoundaryMita-0.054-0.080-0.070-0.055-0.110-0.098(0.082)(0.090)(0.091)(0.138)(0.153)(0.150)R-squared
0.024
0.019
0.024
0.147
0.075
0.150
Clusters
71
60
52
71
60
52
Observations
1,478
1,161
1,013
71
60
52
Notes: The table reports OLS estimates where the unit of observation is the household in columns
1-3 and the district in columns 4-6. Robust standard errors, adjusted for clustering by district,are reported in parentheses in columns 1-3 and robust standard errors are reported in parentheses
in columns 4-6. The dependent variable in panel A/B/C is the number of infants/children/adults
in the household in columns 1-3 and the district mean of the number of infants/children/adults
in the households in the district in columns 4-6. Mita is an indicator variable equal to 1 if the(household’s) district contributed to the mita and 0 otherwise. Panel A/B/C-1 includes a cubic
polynomial in the latitude and longitude of the observation’s district capital. Panel A/B/C-2
includes a cubic polynomial in Euclidean distance (km) from the observation’s district capital toPotosı́. Panel A/B/C-3 includes a cubic polynomial in Euclidean distance (km) to the nearest mitaboundary. All regressions include controls for elevation, slope, and boundary segment ﬁxed eﬀects.
The sample in columns 1 and 4 includes observations whose district capitals are located within 100
km of the mita; this threshold is reduced to 75 km in columns 2 and 5 and 50 km in columns 3 and6. *** p < 0.01; ** p < 0.05; and * p < 0.1.
Units:

A–4