HIAS-E-44

Some Remarks on the Causal Inference for Historical
Persistence
Katsuo Kogure
Center for Southeast Asian Studies, Kyoto University, 46 Shimoadashi-cho, Yoshida, Sakyo-ku, Kyoto 606-8501,
Japan

May 2017
reviced in September 2017

Hitotsubashi Institute for Advanced Study, Hitotsubashi University
2-1, Naka, Kunitachi, Tokyo 186-8601, Japan
tel:+81 42 580 8604
http://hias.ad.hit-u.ac.jp/
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Some Remarks on the Causal Inference
for Historical Persistence ∗Katsuo Kogure†
September 20, 2017
Abstract
A growing body of literature examines the relationships between
historical events and contemporary economic outcomes. Recent studies
estimate the causal eﬀects using detailed historical data and contemporary microdata of individuals and/or households. In this paper, we
discuss conceptual and econometric issues inherent in the causal inference following the potential outcomes framework. Using an empiricalexample, we also discuss a simple alternative approach to avoid theseissues that is coherent with the potential outcomes framework.
JEL Codes: C01, N01
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, and seminar participants at the 3rd Hitotsubashi Summer Institute2017, 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 Grantin-Aids for Scientific Research No.15K17044, Ministry of Education, Science and Culture,
Japan.
†
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

Recent years have seen growing interest in the causal relationships between
historical events 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 toidentify the causal eﬀects of history on outcomes (e.g., Dell (2010), Nunn andWantchekon (2011)). This paper discusses conceptual and econometric issues
inherent in the causal inference following the Rubin causal model, a framework
for causal inference based on potential outcomes (Rubin (1974, 1977)).1
Although the existing empirical studies do not always explicitly follow thepotential outcomes framework, we follow the framework because it enables us
to raise most eﬀectively the issues inherent in the causal inference for historicalpersistence with microdata; many modern empirical works that examine causal
questions adopt this framework (see, e.g., Heckman et al. (1999), Angrist andPischke (2009), Duflo et al. (2008), Imbens and Wooldridge (2009), Imbens
and Rubin (2015)). Using an empirical example, we also discuss a simple
alternative approach to avoid certain issues that is coherent with the Rubincausal model.
The paper proceeds as follows. Section I provides a brief description of
the Rubin causal model, specifying the major premises. Section II considers
the causal inference for historical persistence with contemporary microdata
and discusses fundamental problems inherent in the causal inference. We also
discuss a simple alternative approach to address these problems. Section III
provides an empirical example based on the approach and Section IV concludes.
1

The potential outcomes were originally introduced by Fisher (1935) and Neyman (1923)
for randomized experiments and extended by Rubin (1974, 1977) for non-randomized studies. Holland (1986) labeled this framework the Rubin causal model.

2

I. 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 is a 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 thetreatment and Di = 0 if unit i is not. The third is a response variable, Y , thatis 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 that would 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 therealized and observed outcome: Yiobs = Yi (Di ) = Yi (1)·Di +Yi (0)·(1−Di ). The
potential outcomes enable us to define causal eﬀects at three levels: unit level,
population level, and subpopulation level (e.g., Holland and Rubin (1988)).
The unit-level causal inference is defined as the diﬀerence between the twopotential outcomes for the same unit:Yi (1) − Yi (0).
The population-level causal inference is defined as the expectation of the difference 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 is the expectation of the diﬀerence in the unit-level causal eﬀect over the3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 the same time. We can observe, at most, either Yi (1) or Yi (0).
Thus, it is impossible to directly 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 areno multiple versions of treatments (Rubin (1980, 1986)). The second assumption is unconfoundedness (Rosenbaum and Rubin (1983)),2!

"
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.
This assumption ensures overlap in the covariate distribution of treatments
and controls. The combination of unconfoundedness and overlap is referred toas “strong ignorability” (Rosenbaum and Rubin (1983)).
2

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), Angrist and Pischke (2009)).

4

Identification. The three assumptions justify causal inference, as follows.
Suppose that we are interested in learning the conditional average treatmenteﬀect, E[Yi (1)−Yi (0)|Xi ]. Under the three assumptions, the average treatmenteﬀect can be 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].
Here, since E[Yi (1)|Xi , Di = 1] and E[Yi (0)|Xi , Di = 0] do not depend on Di
under the unconfoundedness assumption, the second equality holds. In addition, based on the overlap 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
period and (2) the action of treatments and the measurement of outcomestake place on a common unit.3 Holland (1986) discusses these 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 types: pre-treatment variables and post-treatment variables(variables determined before and after receiving the treatments, respectively).
The latter may be aﬀected by treatments while the former are not. Thus, it
3

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 treatment non-complianceand “truncation-by-death” (e.g., Frangakis and Rubin (2002), Zhang and Rubin (2003)).

5

is possible to identify the causal eﬀects of the treatments by comparing posttreatment variables (outcomes) between treatment and control groups withsimilar values of covariates (under the assumptions).
II. Causal Inference for Historical Persistence
Following the potential outcomes framework, we now consider the causal inference for historical persistence with contemporary microdata.
A. The Standard Approach
Let us first look at the standard approach used in existing studies. Thesestudies examine historical events such as colonial institutions and Africa’s
slave trade (e.g., Dell (2010), Nunn and Wantchekon (2011); for reviews, see
Nunn (2009, 2014)). Here we assume a historical event (treatment) to be theprotection of property rights in a specific country during the colonial era andexamine the long-run impacts on contemporary individual income.4
To identify the causal eﬀects, researchers may estimate something like thefollowing regression equation under linearity and constant treatment eﬀect
assumptions:′′

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, which takes the value 1 if individual i lives in region j where property
rights were protected during 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.
4

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. For convenience, we assume no missing values on the income and other relevant
variables.

6

B. An Alternative Approach

A. The Standard Approach

Figure 1: Two Approaches to Causal Inference for Historical Persistence
One major concern about the identification of ρ is the endogeneity ofthe protection of property rights, namely, that the exogenous assumption,
ϵij ⊥ Dj |Xij , Zj , may not hold. 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 concerned that 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.
B. Remarks on the Standard Approach
The standard approach, however, faces 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
7

(e.g., LaLonde (1986)), the evaluation of historical events involves a long timespan, the duration of which often exceeds several hundred years (i.e., easily
exceeds a human’s life expectancy). This innate distinctive feature can leadto the following conceptual and econometric issues.
Population. First, population is defined for contemporary individual
units (not those having been directly exposed to the treatments, unlike theevaluation of standard social programs). In this context, since all individual
units (denoted by N ) emerge after the treatments, their existence is potentiallyaﬀected by the treatments (and subsequent various factors such as intermediate variables or mediators, most of which are unobserved to researchers).
Specifically, the distribution of the population (and samples drawn from the
population) can be aﬀected by the treatments. Thus, the choice of individual
units as causal units generally introduces post-treatment bias (detailed below).
Covariate Selection. Second, covariate selection in empirical works isoften guided by relevant economic theories and relevant previous researchfindings (e.g., Cameron and Trivedi (2005)). Such covariate selection, however, does not always apply in this context. This is because the variables
selected for covariates in other studies are often post-treatment variables forwhich 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 posttreatment variables. The variables of regional characteristics, Zj , may include
not only pre-treatment variables, Zjpre , but also post-treatment variables, Zjpost .
The adjustments for Xij and Zjpost in the regression generally introduce posttreatment bias.
SUTVA. Third, since the treatment assignment varies at the cluster (re8gional) level, we require two additional assumptions regarding SUTVA: (1)no interference between clusters and (2) intact clusters (Hong and Raudenbush (2006)). In this context, the validity of the latter assumption may beof concern. For example, some individuals in a control (treatment) region
might actually have been born in a treatment (control) region, spent sometime there, and then migrated to the control (treatment) region. In this case,the assumption of no multiple versions of treatment may be violated. Also,
potential outcomes of an individual might be aﬀected by others with diﬀerent
versions of treatment through social interactions.
Inference. Fourth, since the existence of contemporary individual units
can be aﬀected by the treatments, the nature of dependence within regions(within-cluster correlation) can also be aﬀected by the treatments. Thus, theestimated cluster-robust standard errors can be aﬀected by the treatments.
C. The Identification Problems
This subsection more formally considers the identification problems in using
microdata of individuals to identify the causal eﬀects of history on their outcomes. Here we only 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 problem has long beenrecognized and discussed in the existing literature (e.g., Rosenbaum (1984),
Wooldridge (2005), Angrist and Pischke (2009), Elwert and Winship (2014),
Acharya et al. (2016), Montgomery et al. (2017)) but the former has 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 potentially9exist at the time of the “follow-up survey” (depicted in Figure 1A). Its distribution is not aﬀected by the treatments (or the mediators). Thus, it is feasible
to apply the potential outcomes framework to those potential individuals.
In this case, an ideal experiment (hypothetical one) would be that all thesepotential individuals (superpopulation) are randomly assigned to the treatment or control group and that all of them are actually observed at the timeof the follow-up survey. We let Yij (Dj ) denote the potential income of potential individual i in region j given Dj . The parameter of our interest is theaverage treatment eﬀect (ATE) for the superpopulation,
τ = E[Yij (1) − Yij (0)] = E[Yij (1)] − E[Yij (0)].
However, what we can actually observe is quite diﬀerent, as follows. Let
Sij (Dj ) denote the potential outcome for the existence of potential individual
i in region j given Dj ;5 for example, 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 actually observe is the average observed diﬀerence between
individuals who actually existed in the treatment and control groups,
ˆ = E[Y obs |S obs = 1, Dj = 1] − E[Y obs |S obs = 1, Dj = 0].
△
ij
ij
ij
ij
Here again we 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 existence of potential individuals. For example, if a historical event significantly
aﬀected the survival of ancestors in such a way that poor, less educated, or
5

To keep the notation simple, we do not explicitly specify the mediators. Here we assume
that SUTVA holds.

10low-ability people or people in poor health were more likely to die, then theobserved and unobserved characteristics of contemporary individuals (i.e., thedescendants 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 thehistorical event is randomized (at the regional level).
To identify the ATE based on a finite sample of observed individuals, wewould require the assumption that the historical event is completely randomized (at the contemporary individual level):(Yij (1), Yij (0), Sij (1), Sij (0)) ⊥ Dj .
This assumption implies that the historical event has no systematic eﬀect on
the existence of potential individuals. However, in reality, whether or noteach individual exists does depend on his or her treatment assignment and/or
subsequent various factors; we cannot always define Yij (1) and Yij (0) for all
potential individuals.
To see more details about this, let us follow the idea of the principal stratification approach (Frangakis and Rubin (2002)), which allows us to classify
the individuals who actually existed (Sijobs = 1) into the following six groups
according to the joint values of the two potential existence indicators:• EE = {i : Sij (1) = Sij (0) = 1}, those who would exist regardless of

their treatment assignment; both Yij (1) and Yij (0) are defined in R (theset of real numbers);• EN = {i : Sij (1) = 1 and Sij (0) = 0}, those who would exist if as-

signed treatment but would not exist if assigned control; Yij (1) ∈ R and

6

Yij (0) = ∗;6

For Sij (Dj ) = 0, we define the outcome as “∗,” following the notation used in the11• ?N = {i : Sij (1) = 1 or 0 and Sij (0) = 0}, those who may or may not exist depending on subsequent situations (mediators) when assigned treatment (they would not exist if assigned control); Yij (1) ∈ R or Yij (1) = ∗and Yij (0) = ∗;• 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;

• N ? = {i : Sij (1) = 0 and Sij (0) = 1 or 0}, those who may or may
not exist depending on subsequent situations (mediators) when assigned
control (they would not exist if assigned treatment); Yij (1) = ∗ and
Yij (0) ∈ R or Yij (0) = ∗;• ?? = {i : Sij (1) = 1 or 0 and Sij (0) = 1 or 0}, those who may or may
not exist depending on subsequent situations (mediators) under both
treatment arms; Yij (1) ∈ R or Yij (1) = ∗ and Yij (0) ∈ R or Yij (0) = ∗.
Because principal strata are not aﬀected by treatment assignment (althoughdefined by a post-treatment variable), it is possible to identify the causal eﬀects
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 treatmentgroup;
truncation-by-death literature (e.g., Zhang and Rubin (2003)).

12

• 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 toan unobserved principal stratum. Their relationship is summarized in Table 1.
Table 1: Observed Data Pattern and Unobserved Principal Strata
OBS(Dj , Sijobs )OBS(1, 1)
OBS(0, 1)

Dj
10

Sijobs1
1

Yijobs∈R∈R

Unobserved Principal Strata
EE, EN, ?N, ??
EE, N E, N ?, ??

Table 1 reveals that OBS(1, 1) and OBS(0, 1) consist of a mixture of
the EE, EN, ?N, ?? groups and the EE, N E, N ?, ?? groups, respectively;
these two groups involve diﬀerent combinations of principal strata, suggestingthat a comparison of the two outcomes is not an “apples-to-apples” 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 regardlessof his or her treatment assignment: Sij (Dj ) = 1 for all Dj . This existence
assumption reduces the six principal strata only to EE and thus allows us
to identify the causal eﬀects for the EE group, where both Yij (1) and Yij (0)are well defined in R. This assumption would also require that all potential individuals always exist. Thus, in this case, the population is identicalto the superpopulation and its distribution is not aﬀected by the treatment
assignment (or mediators).
D. An Alternative Approach
The assumptions discussed above to justify the causal inference for historical13

persistence with microdata cannot be empirically examined (even partially)
regarding their validity. To avoid imposing such untenable assumptions, as asimple alternative approach, it might be better to make the causal inferencewith clusters or groups (i.e., regions), rather than individual units. This isbecause, in many cases, 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 and the measurement of outcomes take place on
a common unit.7 Although we are required to change the causal question ofinterest 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 individuallevel data in Figure 1A are now aggregated at the cluster (regional) level. We
use Cj , where j = 1, . . . , G, to denote each cluster, the size of which is denoted#Gby Nj , where
j=1 Nj = N . We assume that regional-level pre-treatment
variables, Zjpre , and post-treatment variables, Zjpost , are available. Individual

characteristics, Xij , and outcome, Yij , are observed at the individual level. For
simplicity, we assume that all individual units (who actually existed) withinall 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 of treatments 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 , is regional income, which is defined using theindividual-level outcome, Yij . We can also define various response variables
using other post-treatment variables in Zjpost and Xij .
7

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

14

Assumptions. The three key assumptions (SUTVA, unconfoundedness,and overlap) are assumed to hold. The plausibility of the unconfoundedness and overlap assumptions is assumed to be improved by innovative quasiexperimental 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 averagetreatment eﬀect, 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].
Estimation. For simplicity, we suppose that the treatment eﬀect is constant and the 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 the average treatment eﬀect:′
Yj = α + ρDj + Zjpre γ + ϵj ,where Yj =# Nj

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 and the clusters are assumed to be independent of each other. Under theassumptions, the unweighted between-groups estimator consistently estimates
the average treatment eﬀect.
15

Here let us 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 orgroups, not individual units. In contrast, their motivation is to obtain a valid
inference in the context of cluster sampling with a small number of clusters, as
is typically the case for diﬀerence-in-diﬀerences estimation. Their populationof interest is still individual units, not clusters or groups. 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 andLang (2007), Wooldridge (2010, Chapter 20) for details).
III. An Empirical Example
This section provides an empirical example based on the alternative approach
as well as the standard one using the influential Dell (2010) paper, which follows the potential outcomes framework for studying historical persistence at
the micro level. 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 the mita boundary, she uses a regression discontinuity(RD) approach to examine the historical persistence.8 Although she also examines the underlying mechanisms, we focus on estimation of the causal eﬀects
8See, e.g., Imbens and Lemieux (2008), Lee and Lemieux (2010) for a description ofregression discontinuity designs using the potential outcomes framework.

16

of the mita on current living standards (equivalent household consumption in2001 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)

In this estimation, 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 the causal eﬀects of the mita on current living
standards for districts, not individuals. The clusters are assumed to meet therequirements of the Rubin causal model.
Nd denotes the number of individual units in district d. cdb is the meanoutcome for district d along segment b of the mita boundary. mitad is anindicator variable equal to 1 if district d contributed to the mita and 0 otherwise. Xd is a vector of covariates that includes elevation and slope for districtd. f (geographic locationd ) is the RD polynomial, which controls for smoothfunctions of geographic location. φb is a set of boundary segment fixed eﬀects.
The descriptive statistics are presented in Appendix Table A1; see Dell (2010)
for detailed data information.
Assumptions. The first key identifying assumption in the RD approachis that all relevant factors are continuous at the mita boundary. Based on
Dell’s careful work in checking the validity of the assumption (see Dell (2010,
Section 3.2)), we assume that the smoothness assumption holds.9 The second
key identifying assumption is that the functional form of the regression model
is correct. Because she considers various functional forms regarding the RD
9

Although Dell uses individuals as causal units, she considers the validity of the smoothness assumption for district-level pre-treatment variables.

17

polynomial, we simply follow her three specifications: (1) cubic polynomial inlatitude 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
around the mita boundary. Since we use geographic units (clusters) as causal
units, it is plausible to assume that the no-manipulation assumption holds.
If we consider this assumption from the individual-unit point of view, theassumption is relevant to the individual units having been directly exposedto the treatments, not the contemporary individual units. For that reason,
Dell (2010), using contemporary individual units as causal units, provides anunusual discussion regarding the validity of the assumption,10 which is not
generally found in the standard regression discontinuity design literature (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 datain columns 1-3 and district-level 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, based on our discussions above, to justify
the causal inference, we simply assume that the population is identical to thesuperpopulation: Potential individuals always existed.

10“(A)n additional assumption often employed in RD is no selective sorting across thetreatment threshold. This would be violated if a direct mita eﬀect provoked substantial outmigration of relatively 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 an interesting channel of persistence, to the extent that thedata permit.” (Dell (2010, p. 1876)). This implies that the assumption of intact clusters
regarding SUTVA might be violated, although it seems that migration was low.

18

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. *** = Significant at the 1% level. ** = Significant at the 5% level. * =Significant at the 10% level.

19

The main findings are summarized as follows. First, the estimates incolumns 1-3 in panel A diﬀer slightly from those in Dell (2010) (columns
1-3 of Table 2). This is because we avoid adjusting for demographic variables(the number of infants, children, and adults in the household), which are posttreatment variables. However, because these variables are little aﬀected by themita (not reported),11 the two results are quite similar in regard to the magnitude of the impacts and the level of statistical significance. We also performthe same exercises for the district-level regressions and find similar results,12
implying that 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 estimatedimpacts of the 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 statistically significant. In addition, although negative
impacts are found for the specifications of a cubic polynomial in distance toPotosı́ 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 km of the mitaboundary. These results imply that more conservative discussions regarding
the mita impacts might be needed because the untenable assumptions imposedin the analyses might be violated.
Although the population of interest as well as the units of analysis diﬀer
11

Significant impacts are found only for the number of children in the specification of a
cubic polynomial in latitude and longitude. The results are available from the author uponrequest.
12
The results are available from the author upon request.

20

between the estimations based on individual-level data and aggregated data,
we touch on the reasons why the estimated impacts of the mita are similarin panel A, but diﬀerent in panel B. First, we note that the two estimators
are identical when all clusters have the 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 in panel A, butquite diﬀerent in panel B and (2) the covariate distribution for the specificationof a cubic polynomial in latitude and longitude is sensitive to the diﬀerence ingroup size, while that for the specifications of a cubic polynomial in distanceto Potosı́ and the mita boundary is not (see Appendix Table A1).
IV. Concluding Remarks
In this paper, we have raised issues inherent in the causal inference for historical persistence 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, the choice of individual units as causal units generally introduces bias because their existence is potentially aﬀected by the treatments.
Also, covariate selection guided by relevant economic theories and empiricalfindings often contains post-treatment variables, which may introduce anotherpotential bias. Using an empirical example, we have discussed a simple alternative approach to avoid such problems that makes the causal inference withclusters or groups, not individual units. The approach is coherent 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
21

of treatments if the existence of the causal units of interest is potentiallyaﬀected by treatments more generally (e.g., across generations). We believe
our discussion can help in designing/analyzing future relevant observationaland experimental studies/data and lead to more transparent research. We will
also development a general framework to address such causal inference at the
micro level in future work.
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27

For Online Publication
Table A1: Descriptive Statistics
Units:
Sample Within:
Variable
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< 100 kmof Bound.
(1)

5.877
(1.010)0.752(0.432)3.841(0.378)7.130(4.124)-0.335(1.203)-0.054(0.820)1.559(1.742)0.675(0.533)-0.617(1.071)-1.956(4.497)0.163(1.004)0.900(2.407)-0.451(1.384)8.964(1.450)82.453(24.911)775.093(328.449)
0.406(0.286)0.247(0.288)0.181(0.264)0.086(0.280)0.289(0.453)0.384(0.487)
1,478

A. Log Equivalent Household Consumption (2001)
Households
Districts< 75 km< 50 km< 100 km
< 75 kmof Bound.
of Bound.
of Bound.
of Bound.
(2)
(3)
(4)
(5)
20.81719.350(12.312)(9.251)
5.799
5.848
5.839
5.805
(0.915)(0.855)(0.401)(0.362)
0.716
0.674
0.718
0.700
(0.451)(0.469)(0.453)(0.462)
3.824
3.827
3.792
3.786
(0.389)(0.383)(0.408)(0.400)
8.319
8.548
7.784
8.615
(3.699)(3.649)(4.106)(3.771)0.046
0.106-0.1050.123(0.921)(0.777)(1.110)(0.885)-0.340-0.412-0.202-0.393(0.638)(0.578)(0.765)(0.621)
0.849
0.614
1.226
0.785
(0.900)(0.491)(1.473)(0.822)
0.522
0.503
0.618
0.534
(0.368)(0.335)(0.488)(0.387)-0.252-0.113-0.435-0.242(0.689)(0.527)(0.883)(0.652)-0.1420.188-1.0080.046(2.041)(0.836)(3.724)(1.794)-0.200-0.284-0.015-0.242(0.584)(0.479)(0.893)(0.600)-0.012-0.1880.385-0.096(1.147)(0.519)(1.874)(1.030)0.014
0.114-0.1560.063(0.703)(0.416)(1.062)(0.659)
9.484
9.587
9.262
9.586
(1.036)(0.814)(1.300)(0.983)91.01792.57087.45092.836(18.779)(15.357)(22.829)(18.004)
882.584899.934
839.133
907.258(259.657)(218.859)(307.124)(251.264)
0.281
0.233
0.380
0.290
(0.174)(0.126)(0.263)(0.170)
0.109
0.070
0.213
0.113
(0.122)(0.065)(0.262)(0.118)
0.051
0.024
0.147
0.052
(0.079)(0.031)(0.239)(0.075)
0.078
0.083
0.099
0.083
(0.269)(0.276)(0.300)(0.279)
0.138
0.100
0.197
0.100
(0.345)(0.300)(0.401)(0.303)
0.477
0.484
0.451
0.517
(0.500)(0.500)(0.501)(0.504)
1,161

A–1

1,013

71

60

< 50 kmof Bound.
(6)
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:
SampleWithin:Variable
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 kmof Bound.
of Bound.
of Bound.
of Bound.
of Bound.
(1)
(2)
(3)
(4)
(5)
549.647484.356(1365.381)(678.517)
0.346
0.391
0.403
0.380
0.392
(0.476)(0.488)(0.491)(0.125)(0.120)
0.780
0.707
0.684
0.702
0.678
(0.414)(0.455)(0.465)(0.458)(0.468)
3.911
3.908
3.896
3.864
3.899
(0.388)(0.427)(0.411)(0.482)(0.475)
6.414
7.724
7.890
8.021
8.210
(3.917)(3.489)(3.478)(3.800)(3.585)-0.547-0.149-0.0800.014
0.009(1.225)(0.903)(0.798)(1.077)(0.921)0.017-0.312-0.4180.029-0.037(0.822)(0.636)(0.552)(0.763)(0.744)
1.800
0.837
0.643
1.157
0.845
(1.846)(0.880)(0.600)(1.266)(0.902)
0.676
0.501
0.479
0.580
0.553
(0.584)(0.441)(0.393)(0.538)(0.499)-0.694-0.187-0.089-0.285-0.168(1.159)(0.662)(0.549)(0.822)(0.732)-2.451-0.2800.007-0.372-0.151(4.842)(1.898)(1.097)(3.160)(1.993)0.230-0.187-0.3010.213
0.117(1.050)(0.677)(0.527)(0.901)(0.831)1.186-0.013-0.1720.310
0.175(2.606)(1.047)(0.636)(1.529)(1.158)-0.657-0.0370.039-0.136-0.080(1.491)(0.698)(0.499)(0.926)(0.806)
8.735
9.301
9.434
9.204
9.247
(1.486)(1.022)(0.858)(1.201)(1.035)78.51387.55989.73886.15686.566(25.386)(18.606)(16.060)(21.373)(18.555)
723.445833.387
860.361818.516819.519(333.028)(257.969)(227.659)(290.890)(253.693)
0.447
0.292
0.244
0.417
0.326
(0.299)(0.183)(0.141)(0.273)(0.202)
0.290
0.119
0.079
0.248
0.147
(0.302)(0.127)(0.076)(0.263)(0.146)
0.218
0.057
0.030
0.173
0.076
(0.277)(0.083)(0.037)(0.238)(0.099)
0.097
0.109
0.109
0.225
0.230
(0.296)(0.311)(0.311)(0.418)(0.422)
0.342
0.156
0.093
0.225
0.192
(0.475)(0.362)(0.290)(0.418)(0.395)
0.278
0.348
0.369
0.329
0.310
(0.448)(0.476)(0.483)(0.471)(0.463)
158,848

115,761

100,446289

239< 50 kmof Bound.
(6)542.951(736.596)
0.412(0.116)0.665(0.473)3.908(0.447)8.245(3.591)-0.003(0.808)-0.154(0.688)0.650(0.639)0.494(0.405)-0.018(0.604)-0.033(1.206)-0.063(0.648)0.059(0.734)0.016(0.569)9.320(0.847)87.580(15.410)829.211(213.211)
0.243(0.144)0.079(0.074)0.029(0.035)0.249(0.433)0.119(0.325)0.297(0.458)185

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

A–2