Constitutions, Politics, and Economics: A Review Essay on ...

Journal of Economic LiteratureVol. XLIII (December 2005), pp. 1025-1048

Constitutions, Politics, and Economics:A Review Essay on Persson and

Tabellini’s The Economic Effects ofConstitutions

DARON ACEMOGLU∗

In this essay, I review the new book by Torsten Persson and Guido Tabellini, TheEconomic Effects of Constitutions, which investigates the policy and economic con-sequences of different forms of government and electoral rules. I also take advantageof this opportunity to discuss the advantages and disadvantages of a number of popu-lar empirical strategies in the newly emerging field of comparative political economy.

1025

∗ Acemoglu: Massachusetts Institute of Technology. Ithank Joshua Angrist, Victor Chernozukov, Roger Gordon,Chad Jones, Torsten Persson, Guido Tabellini, SimonJohnson, and Pierre Yared for useful comments and PierreYared for excellent research assistance.

1 While there is renewed interest in political econo-my, in large part in the context of understanding thesources of large cross-country differences in policies,institutions and economic performance, this work is pre-ceded by the important results of the earlier “socialchoice” literature. David Austen-Smith and Jeffrey S.Banks (2000) provide an excellent introduction to themajor results in this literature.

1. Introduction

Political economy has now emerged as anactive and flourishing subdiscipline of

economics, with the ambition of offeringinsights into the causes of the large cross-country differences in major economic out-comes and policies.1 Torsten Persson andGuido Tabellini deserve much of the creditfor making this happen. Their book, PoliticalEconomics: Explaining Economic Policy,which was published by MIT Press in 2000,

is an excellent introduction to basic modelsof political decision-making and their impli-cations for economic outcomes. The objec-tive of their new book, The Economic Effectsof Constitutions, also published by MITPress, is to continue where the first book leftoff, and confront theory with data.

The book deserves enthusiastic receptionfor a number of reasons, including theauthors’ role in advancing the politicaleconomy research program, its ambitiousobjectives, its careful scholarship, and thelong list of findings that come out of theresearch methodology. Equally, however,such a bold attempt at confronting theorywith data requires a critical look. This moti-vates my review of their new book, focusingon the identification issues that arise bothin this context and more generally in recentpolitical economy research.

This review essay is organized as follows.Section 2 introduces the context and theobjectives of Persson and Tabellini’s new

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1026 Journal of Economic Literature, Vol. XLIII (December 2005)

book. Section 3 provides a detailed discus-sion of econometric issues and identificationproblems that Persson and Tabellini haverightly emphasized in their work. Section 4discusses the major empirical results of thebook. Sections 5–8 discuss a number ofproblems and challenges facing empiricalwork in political economy, and reevaluatePersson and Tabellini’s contribution in thislight. Sections 9 and 10 discuss two sets oftopics that I view as important areas forfuture research in political economy.

2. Background and Objectives

Persson and Tabellini (henceforth PT) setthe scene with figure 1.1 in their book,which I replicate here. The box on the left iswhere much of economics falls. We have agood, though far from perfect, understand-ing of how different organizations of marketslead to different economic outcomes. Butwhy are markets organized differently in dif-ferent societies? Economists and othersocial scientists have long realized theimportance of “policies.” If the governmentimposes rent control, this will impact how

the rental market works. The major advancethat came with political economy is encapsu-lated in a new question: why do policies dif-fer over time, across countries and morebroadly across polities? Why, for example, dosome governments impose rent controlwhile others do not intervene in rental mar-kets. Before, we had no better answer than“(some) politicians just don’t get it.” Politicaleconomy is about developing better answers.

This task requires a framework for think-ing about why policies differ across coun-tries. This is what much of political economydoes. Starting with Kenneth J. Arrow’s cele-brated (im)possibility theorem (Arrow 1963,Duncan Black 1948), Anthony Downs’smedian voter result (Downs 1957, HaroldHotelling 1929), and George J. Stigler’s workon regulation (Stigler 1970, 1972), the cen-tral working hypothesis has been thatagents—as voters, lobbyists, revolutionaries,politicians—have induced preferences overpolicies. This means that they understandthat different policies will map into differentoutcomes, and consequently their prefer-ences over policies are shaped by their pref-erences over the outcomes that will be

PolicyPreferences

Policy Decisions

EconomicOutcomes

Markets PoliticalOutcomes

ConstitutionalRules

Figure 1: The Policymaking Process (Figure 1.1, page 3)

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Acemoglu: Constitutions, Politics, and Economics: A Review 1027

2 This approach is referred to as “rational choice” inpolitical science. To economists, it is the natural approachwithout apologies.

induced by the policies.2 Political economyis then about understanding how theseinduced preferences over policies are aggre-gated. The recent work in political economyis also part of this research program, butmore explicitly investigates why collectivedecisions and policies differ across societies.

Much work in political science, on theother hand, as succinctly captured by the boxon the right in Persson and Tabellini’s figureis about how different political procedureslead to different political outcomes. Let usrefer to political procedures as “politicalinstitutions” and make the link betweenpolitical outcomes and policies. This gives usa natural framework for thinking about whydifferent societies choose different policies—they have different political institutions.

PT’s first book, Political Economics, devel-oped various models of collective decision-making and derived predictions on howdifferences in political institutions translateinto differences of policies and economicoutcomes. This new book is the next step topush this framework further by confrontingits predictions with data.

Although this type of comparative analysishas been vibrant in political science, thereare no systematic theoretical analyses deriv-ing precise predictions from micro-foundedmodels to confront with data. Here PT aremuch more ambitious. They take the pre-dictions of a set of theoretical models, inparticular, the probabilistic voting model ofAssar Lindbeck and Jörgen Weibull (1987),extensively studied in their first book, andan extended version of John Ferejohn’s(1986) model of politician accountability,studied in Persson, Gerard Roland, andTabellini (1997, 2000), seriously. Althoughone can have qualms about the specificassumptions that are important to derivepredictions in these models, PT’s is the rightapproach in social science in general, and in

3 See, for example, Avinash Dixit, Gene M. Grossman,and Faruk Gul (2000). This question perhaps is not first-order for PT because they focus on democracies that are“fully consolidated” and do not switch to dictatorship, andinvestigate how electoral rules affect policies within thedemocratic framework. Nevertheless, whether a society isa fully consolidated democracy is endogenous and poten-tially also depends on the form of government and elec-toral rules in democracy (see Acemoglu and Robinson2005 for a discussion).

comparative political economy more specif-ically. What makes this work even moreimpressive is the fact that the authors areinvestigating predictions of their earliermodels.

In reality, PT have an even more ambi-tious goal. Many scholars attempt to docu-ment a set of correlations in the data that arerelated to predictions of existing models.Instead, PT are interested in more than cor-relations. They undertake the ambitious taskof identifying the causal effects of the formof political institutions on economic andpolitical outcomes. They write on page 7:“Our ultimate goal is to draw conclusionsabout the causal effect of constitutions onspecific policy outcomes. We would like toanswer questions like the following: if theUnited Kingdom were to switch its electoralrule from majoritarian to proportional, howwould this affect the size of its welfare stateor its budget deficits? If Argentina were toabandon its presidential regime in favor of aparliamentary form of government, wouldthis facilitate the adoption of sound policytowards economic development?”

How would we get to the causal effects ofa set of political institutions on outcomes?PT have a well-specified strategy. First,they focus on a subset of political institu-tions; the constitutionally determined formof electoral rules and the form of govern-ment among democracies. This leaves out alarge part of political institutions, for exam-ple, those that relate to whether a countryis a democracy or not, and thus a lot ofinteresting questions related to whatmakes constitutions credible in the firstplace.3 Nevertheless, narrowing the scope



4 See, for example, Joshua D. Angrist and Guido W.Imbens (1995), Angrist, Imbens, and Donald B. Rubin(1996), Angrist and Alan B. Krueger (1999), James JHeckman (1997), and Jeffrey M. Wooldridge (2002), formore detailed treatments.

of the investigation is the right approach tobe able to estimate causal effects. Second,they use a variety of state-of-the-art tech-niques developed in the micro-economet-rics literature, in particular, matchingestimators, propensity score methods,instrumental variables estimation, andparametric selection corrections.

Since the identification of causal effectsis the major objective of this book, and alsobecause the econometric issues that arisehere are becoming increasingly importantin the political economy literature, in thenext section I discuss PT’s econometricmethodology in detail.

3. Econometric Methodology

3.1 The Basic Framework

PT’s major interest is to identify thecausal effect of two political institutions,presidentialism (versus parliamentary sys-tems) and majoritarian electoral rules (ver-sus proportional representation), on theamount and the composition of governmentspending, and on politicians’ rents andother political outcomes. Ultimately, part ofthe interest is also to estimate the effect ofthese different constitutional forms onaggregate productivity and income percapita levels.

Following PT’s exposition in chapter 5, Isimplify the problem by focusing only onone binary constitutional feature, denotedby Si ∈{0,1}, and a generic outcome vari-able, Yi, with i denoting country in a cross-sectional dataset.4 PT consider a relativelygeneral econometric framework, incorpo-rating potentially heterogeneous effects.For the purposes of this review, let us focus 5 It is worth noting that equation (1) can be estimated

without the constant marginal effects and linearityassumptions to obtain “average treatment effects” withweights depending on the estimation strategy, see Angristand Krueger (1999).

6 In words, these are the residuals from the originalvariable’s linear projection on the vector Xi, given byty = (I − X(X�X)�1X)y, where X denotes the K × N matrixobtained from the X i’s.

on a model that is linear in the covariatesand features constant (marginal) effects.Let Xi be a K × 1 vector of (observable)exogenous covariates and suppose that thestructural relationship of interest isE(Yi|Xi) = �Si + X�

iββ, or:

(1)

where � measures the effect of Si on the out-come of interest, ββ is a K × 1 vector of coef-ficients associated with X, and ui capturesthe effect of all unobserved determinants aswell as random influences on Yi.

5

PT use four different empirical strategiesto estimate (1) or variants: ordinary least-squares (OLS), matching and propensityscore estimators to relax the linearityassumption in (1), instrumental variables(IV), and parametric selection correctionsdue to Heckman.

These strategies deal with the identifica-tion problem in (1) in two different ways,which can be classified as “selection onobservables” and “exclusion restrictions”(see Angrist and Krueger 1999).

3.2 Selection on Observables

The identifying assumption for strategy 1is that conditional on Xi, Si and ui are orthog-onal. This last condition implies that theOLS estimator is consistent. To see thisbriefly, let variables with the tildes denotethe original variable after the effect of thevector Xi has been partialed out.6 Then, (1)can be rewritten as:

(2)

which implies that

� � �Y S ui i i= +� ,

Y S ui i i i= + +� X�ββ ,



(3)

where the variance and covariance termsrefer to population values. Consequently,the identifying assumption for strategy 1 isCov(tSi, tui) = 0 (or that conditional on Xi, ui bestatistically independent from Si).

The fact that Si and ui need to be orthog-onal conditional on Xi highlights the impor-tance of selection on observables. It is quitepossible that Si is correlated with someother determinants of Yi, but once we con-dition on the covariates, this correlation dis-appears. Therefore, for this class ofstrategies controlling for the right set ofobservables is of primary importance.

What distinguishes the OLS and match-ing strategies is the way in which they con-trol for the effect of these observables. OLSregression, as in (1), imposes linearity,whereas the matching estimators allow fornon-linear effects of observables. Withmatching estimators, the parameters ofinterest are estimated conditional on a set ofobservables, and then the average effect isobtained by averaging these conditionalparameter estimates. The advantage of thisestimator is that it allows the parameter ofinterest to depend flexibly on the character-istics used for matching. Propensity scoremethods enable consistent estimation whenthere are many characteristics according towhich observations can be matched (seeAngrist and Krueger 1999, Wooldridge2002, chapter 18).

With both strategies, however, there arenumerous reasons why Cov(tSi, tui) = 0 maynot be valid. In this context this might be,for example, because the constitutional fea-tures of a country are partly determined byomitted factors that also influence policychoices and economic outcomes. These fac-tors may include differences in the nature ofeconomic opportunities across societies, the

plimCov

Var

Cov

ˆ,

,

�

�

OLS i i

i

i i

S Y

S

S u

=( )( )

= +

� ��

� �(( )( )Var �Si

,

distribution of noninstitutional politicalpower between various groups, differencesin culture, and differences in other institu-tional features affecting potential outcomes.Since the conceptual issues arising withboth linear regression and matching estima-tors are similar, in what follows I focus onthe identification issues with OLS, whichare simpler to discuss.

To highlight the potential bias in OLSestimation, suppose, again using the tildenotation:

(4)

where Li is some other potential determi-nant of the outcomes of interest, and L

~i

denotes its residuals from the projection onthe X i’s, while ωi satisfies Cov(tSi,ωi) = 0. Thisimplies that

Therefore, the OLS estimator will be incon-sistent if there exists a potential determinantLi of the outcome of interest (i.e., � ≠ 0),which is also correlated with the form of gov-ernment or electoral rules (i.e., ifCov(tSi, tLi) ≠ 0. This corresponds to the usualomitted variable bias. This notation can alsocapture the measurement error (attenua-tion) bias whereby we observe a noisy signalof the true institutions, tSi , while what wecare about is tTi = tSi − tτi, where tτi is a classicalmeasurement error term, with Cov( tTi ,tτi) = 0.In this case, tLi = − tτi and λ = �, so thatplim�OLS = �Var(tTi)/(Var(tTi)�Var(tτi)).

3.3 Exclusion Restrictions and InstrumentalVariables

The most important line of attack thatresearchers have against potential biases ofthe OLS estimator is to use an instrumentalvariables (IV) strategy, which is PT’s thirdstrategy. The IV strategy relies on a M × 1vector of instruments, Zi, which has predic-tive power for the endogenous regressors, butis orthogonal to ui in (1) (where naturally,

plimCov

Varˆ

,.� �OLS i i

i

S L

S= +

( )( )λ� ��

˜ ˜ ,u Li i i= +λ ω



M ≥ K + 1). The exclusion restriction refersto this last requirement, and is equivalent tothe condition E(Ziui) = 0. This means thatthe vector of instruments, Zi, has no effecton the outcomes of interest other than itsimpact through the endogenous regressors.

A common view in the applied economicsliterature is that the IV strategy is “atheoreti-cal.” This view originates from the fact thattypically the IV strategy does not necessi-tate a fully specified structural model.Nevertheless, as I will argue in greater detailbelow, every IV strategy requires an under-lying theory. In essence, the IV strategystarts with an essentially nontestable hypoth-esis, that the vector of instruments, Zi, isorthogonal to omitted influences capturedby the error term ui. This presumption mustbe based on some theoretical consideration,and the IV procedure would have no justifi-cation without a compelling (a priori) theory.This underlying theory can be extremelysimple, for example, the hypothesis that,everything else equal, a change in compulso-ry schooling laws or their enforcementshould affect schooling (e.g., Angrist andKrueger 1991, Acemoglu and Angrist 2000),but have no effect on earnings through otherchannels; or more involved, for example, thehypothesis that all information contained inthe past income realizations should alreadybe incorporated in the current consumptiondecisions and should have no predictivepower for consumption growth (e.g., RobertE. Hall 1978, Lars Peter Hansen andKenneth J. Singleton 1982). I return belowto the theoretical justifications of the instru-ments used in PT’s work and in other work inpolitical economy.

For now, let me simplify the discussionby assuming that all of the variables in Xi

are exogenous, and there is a single exclud-able instrument, Zi, for the only endoge-nous regressor, Si. So the instrument vectoris simply Zi = (Xi,Zi). Using the tilde nota-tion, the estimating equation can be writ-ten as (2), with a corresponding first-stagerelationship of

7 Note also that if ��0, then even though plim�IV��,in small samples �IV could systematically deviate from �,causing the “weak instruments” problem (see, for example,Douglas Staiger and James H. Stock 1997, Stock, JonathanH. Wright, and Motohiro Yogo 2002). The sister problemis the “too many instruments” problem, which arises whenthe vector Zi includes a large number of excluded instru-ments (relative to the number of observations), leading toa spurious first-stage relationship (e.g., Christian Hansen,Jerry Hausman, and Whitney Newey 2004).

(5)

where vi denotes the residuals from the linearregression of tSi on tZi, thus Cov( tZi, vi) = 0. Theprobability limit of the instrumental variableestimator of � is given by

(6)

This equation encapsulates the two require-ments for a valid instrument; (1) relevance,which requires that there should be a first-stage relationship, i.e., λ ≠ 0;7 (2) excludabil-ity, which means that Cov( tZi, tui) = 0 (whichis equivalent to Cov(Zi,ui|Xi) = 0, or toE(Ziui) = 0).

To illustrate the usefulness of the IV strat-egy, let us return to the model of the unob-served effect in equation (4), and supposethat Cov(tSi, tLi) ≠ 0, so that OLS is inconsis-tent. In this case, using the IV strategy leadsto an estimate of �, �IV, with the followingprobability limit:

Therefore, if Cov( tZi, tLi) = 0, the IV estimatorwill be consistent (given � ≠ 0). The condi-tion that Cov( tZi, tLi) = 0 is sometimes looselyreferred to as the requirement that “theinstrument should be orthogonal to omittedeffects.” Moreover, the above discussion ofmeasurement error illustrates that a valid

plimCov

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,.� �IV i i

i

Z L

Z= +

( )( )

λγ

� ��

Cov ,� iZ

= +� ��

�u

Zi

i

( )( )γ Var

.

plimCovCov

ˆ,

,� IV i i

i i

Z Y

Z S=

( )( )� ��

˜ ˜ ,S Z vi i i= +�



instrument also removes the attenuation biasarising from classical measurement error.

In all of this, the set of covariates included inXi is important because one can imagine that Zi

could be correlated with the error term in thesecond stage, but this correlation disappearsonce we condition on a set of covariates (i.e.,we may have that while Cov(Zi,ui|X1

i) ≠ 0,Cov(Zi,ui|X2

i) = 0 for some (not necessarilymutually exclusive) different sets of covariatesX1

i and X2i). Interestingly, this issue does not

arise when there is random assignment due toreal experiments or because of natural experi-ments. This makes the identification problemmore difficult and subtle in political economymodels than in many other contexts, andmakes the distinction between the selection onobservables and exclusion restriction strategiesI tried to highlight above less clear-cut.

PT include income per capita, democracyscore, age of democracy, measures of trade,measures of age composition of the popula-tion, a dummy for federal structure and adummy for OECD in Xi in their main spec-ifications. The instruments are various com-binations of the timing of adoption of thecountry’s constitution, fraction of the popu-lations that speak English or anotherEuropean language, and latitude.

I will discuss the validity of these instru-ments below. Before doing this, however, animportant estimation issue needs to beraised. The above derivation of the consis-tency of the instrumental variable estimatormade it clear that the same set of covariates,Xi, needs to be included both in the first andthe second stage. This was made explicit bythe “tilde” notation above, where the regres-sions include the variables after the vector Xi

has been partialed out. Equations (5) and (6)show immediately why the IV estimator,given the identification assumptionCov( tZi, tui) = 0, is consistent in this case.

PT, instead, choose a nonstandard econo-metric method, and exclude some of the Xi‘sfrom the first stage. In particular, suppose thatthe vector of covariates is partitioned asXi = (X1

i,X2i), and only X1

i is included in the

8 In particular, let the true (statistical) first-stage rela-tionship be Si��Zi�(X1

i)�ππ1�(X2i)�ππ2��i, with Si��Zi

�(X1i)�ππ1�(X2

i)�ππ2 denoting the predicted component of Si.The second-stage equation of the traditional 2SLS proce-dure is Yi��Si�(X1

i)�ββ1�(X2i)�ββ2�ui. The assumption

E(Ziui)�0 ensures consistent estimation of �(�,ββ) withthe standard IV procedure. In contrast, the predictedvalue from the PT procedure is Sbi��bZi�(X1

i)�bππ1

�Si�(�b��)Zi�(X1i)�( bππ1� bππ1)�(X2

i)�ππ2, where the secondequality substitutes for the definition of Sbi. So the secondstage in this case becomes: Yi��Si�(X1

i)�ββ1� (X2i)�ββ2�ub i,

where ub i�ui��((�b��)Zi�(X1i)�(bππ1�ππ1)�(X2

i)�ππ2). DefiningWb i�(Xi,Sbi), PT’s estimator is

For this estimator to be consistent, we need E(Wb iub i)�0.However, when ππ2�0, ub i will be no longer be orthogonal toX2

i, and this will imply that the entire vector of coefficientsηη is not estimated consistently. In other words, we will typ-ically have E(Wb iub i)�0 and plim�PT��, even if E(Ziui)�0.

9 For example, Wooldridge (2002, p. 91) notes: “Inpractice, it is best to use a software package with a 2SLSrather than explicitly carry out the two-step procedure.Carrying out the two-step procedure explicitly makes onesusceptible to harmful mistakes. For example, the follow-ing seemingly sensible, two-step procedure is generallyinconsistent: (1) regress xK on 1, z1,…,zM [the set of exclud-ed instruments for xK] and obtain the fitted values, say txK ;(2) run the regression [of the dependent variable on theother covariates and on txK]...” This example is equivalent tothe procedure that PT implement.

= ⎛⎝⎜

⎞⎠⎟

−

=

−

−

=∑ ∑ηη ++ N Ni

N

i ii

N

i i1

1

1

1

1

� � � �W W W u⎛⎛⎝⎜

⎞⎠⎟

.

ηηPT

i

N

i ii

N

i iN N Y= ⎛⎝⎜

⎞⎠⎟

⎛⎝⎜

−

=

−

−

=∑ ∑1

1

1

1

1

� � �W W W

⎞⎞⎠⎟

first-stage relationship (while the entire Xi isincluded in the second stage). In practice, theprocedure is the following: first, Si is predict-ed on the basis of X1

i and Zi (using linearregression). Denote the predicted values by Si.Then the parameters of interest are estimatedusing an OLS regression with Si instead of Si.It can be shown that for this estimator, �PT, tobe consistent the Xi’s that are omitted from thefirst stage should have no predictive power forthe endogenous regressors (conditional on theother covariates).8 Otherwise, the residualsfrom the first stage, which mechanically gointo the second stage, are no longer orthogo-nal to the covariates, and this biases the esti-mate of the vector ββ, and the bias from ββcarries over to the estimate of the parameterof interest, �.9 Therefore, the estimator used



10 PT justify this econometric method by arguing that,because the major source of bias is not reverse causality butomitted variables, excluding some second-stage covariatesfrom the first stage might be justifiable. This may be anargument for why we should expect ππ2 = 0 in terms of thenotation in footnote 8. They further suggest that this mightbe useful because it would lead to a stronger first-stagerelationship, avoiding weak instrument problems.

by PT may be inconsistent even when thestandard identification assumption,Cov( tZi, tui) = 0 or E(Ziui) = 0, is satisfied.10

One might wonder whether this is an impor-tant source of bias in practice, and I returnto this problem below.

Finally, PT’s Strategy 4, parametric selec-tion corrections, is related to the IV strategy.This is an attempt to deal with the failure ofthe assumption Cov(tSi, tui) = 0 by positing afunctional form for selection on unobserv-ables, based on the work by Heckman (1976,1979). Specifically, PT posit that Si = 1 if G(Zi) + vi ≥ 0, and Si = 0 otherwise. Fol-lowing the common practice, they assumethat the vi’s are normally distributed, whichenables a parametric correction for selection(see, e.g., Wooldridge 2002). Parametricselection approaches exploit the functionalform assumptions on vi, but otherwise relyon the same set of exclusion restrictions.Consequently, though they are a usefulcheck on standard IV estimates, they willalso lead to inconsistent estimates if theunderlying exclusion restrictions are notvalid. This motivates my focus on the linearIV approach for most of the discussion,though I will also contrast the results of theparametric selection approach to the OLSand IV estimates.

4. Main Results and Assessment

Using all four strategies, PT obtain a num-ber of results that paint a broadly consistentpicture. The most important results are:

1)Presidential and majoritarian systemshave smaller governments than parlia-mentary and proportional representa-tion systems (where government size is

measured as government spending as afraction of GDP). Majoritarian systemsalso appear to have smaller welfare statespendings and budget deficits.

2)While presidential or majoritarian sys-tems in general do not have a robusteffect on political rents, corruption andaggregate productivity, certain details ofthe electoral system, in particular thesize of the electoral districts andwhether voters cast their ballots forindividual politicians or for party lists,do have significant effects.

3)Countries with parliamentary systemshave more persistent fiscal outcomesthan countries with a presidential sys-tem. Namely, in parliamentary systems,increases in government spending dur-ing downturns are not reversed duringbooms. There is a similar, but weakerpattern, for countries with proportionalrepresentation (relative to those withmajoritarian elections). Finally, consis-tent with the predictions of the politicalbusiness cycle models, proportionalrepresentation also appears to generatea greater expansion in welfare spendingin the proximity of elections.

These results are exposed with great clari-ty, and PT show that they are robust. Forexample, the results are similar with linearregressions, or with the matching andpropensity score methods. Importantly,results are also similar with the instrumentalvariables and parametric selection correctionstrategies, though sometimes less precise.

What makes these results even moreimportant than this brief description wouldsuggest is that they are closely related tothe predictions of the models that havemotivated PT’s study. For example, themodels that are most popular in the litera-ture suggest that electoral rules, in particu-lar, how broad or narrow districts are,should affect both the overall size of gov-ernment, the composition of spending andthe extent of political rents. These are con-firmed by the empirical results in the book.



In addition, models based on the impor-tance of separation of power, such asPersson, Roland, and Tabellini (1997,2000), suggest that presidential systemswhere there is typically greater separationof powers should have smaller govern-ments, which is also the pattern that PTfind in the data.

These are remarkable results. Only a verybrave or uninformed scholar could attemptto write on comparative political economywithout seriously studying this book, andonly a very stubborn researcher would havehis or her posteriors remain unchangedafter studying it. PT have already achievedsomething very few scholars can: a body ofwork for not only the current generation ofresearchers, but also for the next genera-tion. In fact, the impact of the book mighteven be greater than this discussion sug-gests. If the results indeed correspond tothe causal effects of the form of governmentand electoral rules on policies and econom-ic outcomes as PT claim, we have learnedmore with this book than from the entirecomparative politics literature of the pastfifty years.

Despite these remarkable results, thereare reasons to question whether thisresearch has successfully uncovered causaleffects. The OLS and matching estimatesultimately rely on the exogeneity of politi-cal institutions. Nevertheless, politicalinstitutions are equilibrium outcomes,determined by various social factors thatare not fully controlled for in the empiricalmodels. This makes me believe that,although the OLS results uncover interest-ing patterns, they do not typically identifycausal effects. For causal effects, we haveto turn to estimates using the exclusionrestrictions. Here PT’s work is again thestate-of-the-art, but the exclusion restric-tions are not necessarily compelling, mak-ing it unlikely that the IV estimates areuncovering causal effects either. The nextthree sections discuss these problems ingreater detail.

5. Identification in Political Economy

5.1 General Issues

PT have put identification of causal effectsas the primary objective of their work. In thisthey are not alone. Much recent research ofpolitical economy is about understandingthe effects of various policies or institutionalfeatures on economic development. Theissues of identification are therefore at theforefront. I will argue that even though PThave undertaken a careful and thoroughinvestigation of the questions at hand, theymay have not estimated the causal effect ofthe constitutional features on the outcomesof interest. Moreover, the identificationproblems that arise in this work are sharedby many other studies in political economy.

Let us start by recalling that the basicapproach is to understand differences inpolicies and economic outcomes as a func-tion of the underlying political institutions ofsocieties. This methodological approachbuilds on the notion that agents haveinduced preferences over policies becausethey recognize the implications of these poli-cies for their well-being. Although I whole-heartedly agree with this methodology, I alsothink that there is an immediate next stepthat one can (and should) take. By exactlythe same token, agents should have inducedpreferences over political institutions. This isbecause different political institutions willgenerate different policies, and thus lead todifferent economic outcomes, and rationaleconomic (and political) agents shouldunderstand not only the implications of dif-ferent policies but also the implications ofdifferent political institutions. The logic ofpolitical economy therefore forces us to alsothink of political institutions as endogenous.

This leads to an important issue: while alarge body of empirical literature argues thatpolitical institutions are “predetermined” orgiven by history and treats them as exoge-nous, the reasoning of the political economyapproach implies that these institutions arealso endogenous and likely determined by the



same factors that make policies unappealingvariables to treat as exogenous.

This point has featured in one way oranother in the comparative politics litera-ture. It is emphasized in its most generalform by the Charles A. Beard’s classic 1913study, An Economic Interpretation of theU.S. Constitution, where he argues that theprimary objective of the government and theconstitution is to ensure favorable economicconditions for those holding political power,and the form of government should be seenas a (secondary) feature serving the sameobjective—by “secondary” Beard does notmean less important, but chosen in the sameway and for the same objectives as the over-all structure of political power. He writes:(1913, p. 13)

Inasmuch as the primary object of a govern-ment, beyond the mere repression of physicalviolence, is the making of the rules that deter-mine the property relations of society, thedominant classes whose rights are thus to bedetermined must perforce obtain from thegovernment such rules as are consonant withthe larger interests necessary to the continu-ance of their economic processes, or theymust themselves control the organs of gov-ernment. In a stable despotism the formertakes place; under any other system of gov-ernment, where political power is shared byany portion of the population, the methodsand nature of this control become the prob-lem of prime importance—in fact, the funda-mental problem in constitutional law. Thesocial structure by which one type of legisla-tion is secured and another prevented—is asecondary or derivative feature arising fromthe nature of the economic groups seekingpositive action and negative restraint.

If Beard is correct in his assessment, thenmany features of constitutions will be influ-enced by factors that also have a directimpact on policy and economic outcomes.To illustrate this possibility, imagine a worldconsisting of a group of politically powerfulelite and citizens. The elite oppose redistrib-ution, while the citizens favor it. When theelite are more powerful, they will be able tolimit the amount of redistribution and thesize of government. Imagine also that the

11 A similar argument, though with the opposite impli-cation, is suggested by another major figure in comparativepolitical science, Stein Rokkan. Rokkan argued in his 1970book that the emergence of proportional representation inContinental Europe was a result of the previous elites’attempts to manage the transition to democracy in a man-ner that was consistent with their interests. He suggeststhat a key objective of the proportional representation sys-tem was to make the emergence of a socialist majoritymore difficult. If Rokkan is correct, then because propor-tional representation emerged in societies where the eliteswere more powerful, we may expect a negative correlationbetween proportional representation and redistribution, asopposed to the positive correlation documented by PT.

elite prefer presidential systems to parlia-mentary systems. In this case, when the eliteare more powerful, the equilibrium form ofgovernment is more likely to be presidential.If, in addition, the strength of the elite ispersistent, there will be an empirical corre-lation between presidentialism and smallergovernments, not only at the time the con-stitution is written, but also in the subse-quent decades. But this correlation wouldnot necessarily reflect the causal effect ofpresidentialism on equilibrium policies.11 Interms of the econometric discussion above,the requirement that Cov(tSi, tui) = 0 in equa-tion (2), is violated because there is an omit-ted factor, like tLi in equation (4), in this casethe political strength of the elite, which willaffect both the form of government and theoutcomes of interest. The same concernsgeneralize to the other potential outcomevariables.

In this light, the OLS (non-IV) estimatesof the causal effects of the form of govern-ment and electoral systems should not beinterpreted as causal. Instead, they likelycorrespond to interesting robust correlationsin the data. For causal estimates, we have torely on IV approaches.

5.2 The Instrumental Variables Approach inPractice

PT attempt to estimate the causal effectsof the form of government and electoral sys-tems by using a simple IV approach. Theirpotential instruments are three constitution-al dating variables, indicating whether a

de05_Article3 11/16/05 3:59 PM 34


12 Another potential problem is that, as discussed insection 3, a successful IV strategy also requires E(X iui)�0,i.e., the covariates that are treated as exogenous to beorthogonal to the error term. These covariates hereinclude income per capita and trade, which are jointlydetermined with the size and composition of governmentspending, and their inclusion in the equation may lead tobiased estimates. Nevertheless, reestimating PT’s IV mod-els excluding income per capita and trade leads to resultssimilar to their baseline IV estimates.

country adopted its current form of govern-ment and current electoral rule after 1981,between 1951–80, between 1921–50, withbefore 1921 as the omitted category; two lan-guage variables, indicating the fraction of thepopulation in the country speaking one ofthe major European languages, and the frac-tion speaking English as a native language;and latitude (distance from the equator).

Although the IV approach adopted by PTis important on methodological grounds, Iwill argue that it is unlikely to be estimatingthe causal effect of the form of governmentand electoral rules on policy and economicoutcomes for two reasons: first, because thethree constitutional timing variables havelittle effect on the endogenous regressors,identification ultimately relies on the frac-tion of the population with European lan-guage as native tongue and latitude, whichare not convincing instruments for institu-tional features in general; second, even ifthey were valid for some general institu-tional features, by implication they couldnot be valid instruments for specific institu-tional features such as the form of govern-ment or electoral rules.12 In thissubsection, I show the importance of thelanguage and latitude instruments for iden-tification, and also briefly look at the impli-cations of not including second stagecovariates in the first stage.

Let us begin with the reasoning for theseinstruments. The three timing variablescould be relevant for the form of govern-ment and for the electoral system becausethere may have been waves (or “fads”) inthe type of constitutions, and different

13 Lack of a first-stage relationship even at the conven-tional significance levels is an extreme form of the weakinstruments problem mentioned in footnote 7.

countries fell into different waves depend-ing on when they adopted their constitutionor declared their independence. The twolanguage variables and latitude are includedas proxies for “European influence” follow-ing the arguments in Hall and Charles I.Jones (1999). Hall and Jones use these vari-ables as instruments for the overall qualityof institutions (social infrastructure), andPT argue that these could also have affect-ed the form of government and electoralrule. The reasoning for these Hall–Jonesinstruments is discussed in the next section.

These potential instruments are highlycorrelated with the form of democratic insti-tutions. Typically, countries farther awayfrom the equator and those with a greaterfraction of the population speaking Englishas a native language (but not those with otherEuropean languages) are less likely to havepresidential systems. For majoritarian sys-tems, the effects of English and otherEuropean languages are reversed. There issome effect from the constitutional datingvariables, but these are typically weaker, andless consistent (depending on what covariatesare included in the first and second stages).

The general pattern suggests that withonly the constitutional variables, there is nofirst stage for the instrumental variable strat-egy.13 This is illustrated in table 1 where I usePT’s data to replicate and further investigatetheir first-stage relationships. Columns 1a and1b are identical to the first two columns ofPT’s table 5.1, and separately estimate OLSfirst-stage relationships with dummy variablesfor presidential and majoritarian systems onthe right-hand side (respectively PRES andMAJ). Both columns include seven variables;three dummies for the dates of the adoptionof the constitution, latitude, fraction of thepopulation speaking English and fraction ofthe population speaking another European



language as native languages, and age ofdemocracy (the latter is included as a covari-ate in the second stage equations as well,while the others are excluded instruments).They also report F-tests for joint signifi-cance of all the excluded instruments andthe constitutional variables at the bottom.

These two columns show a reasonablystrong first-stage relationships, which arethen used by PT in their 2SLS estimation(the R2 is 0.48 in the first column and 0.40in the second column). However, we cansee that the major determinants of theendogenous regressors are the Hall–Jonesinstruments, not the constitution timingdummies. In both columns 1a and 1b, thesix instruments are jointly significant at lessthan 1 percent, but the three constitutionaldummies are only significant at 2 percent incolumn 1a (for the presidential dummy)and very far from statistically significant incolumn 1b (for the majoritarian dummy).

Columns 2a and 2b show that the joint sig-nificance of the excluded instruments, andespecially of the constitutional variables, issignificantly reduced when the second-stagecovariates are also included in the first stage.Recall that these second-stage covariates arelog income per capita, the proportions of thepopulation between the ages of fifteen andsixty-four, and over the age of sixty-five, thesum of exports plus imports divided by GDP,the average of political and civil libertiesindices of Freedom House, and dummies fora federal structure and OECD (see PT, espe-cially table 6.2 and the data appendix fordetails). As discussed above, PT includethese covariates in the second stage, but notin the first-stage relationship. Once they arealso included in the first stage, the constitu-tional dummies are no longer jointly signifi-cant for either presidential or majoritariandummies.

I will argue in greater detail in sections 6and 7 that latitude and European languagesmay not be valid instruments for the form ofgovernment and electoral rules. In this light,it is important to understand whether they

are essential in the first-stage relationshipsreported by PT. Columns 3a,b and 4a,b showthat they are, and that once these variablesare left out, there is a very weak or no first-stage relationship left. Without the second-stage covariates, the constitution dummiesare significant at 3 percent and 5 percentrespectively in columns 3a and 3b, and whenthe second-stage covariates are included,they are highly insignificant.

This implies that an instrumental-vari-ables strategy relying only on the constitu-tional timing dummies would not achieveidentification.

Table 2 shows the corresponding 2SLSestimates of the form of government and theelectoral system on the size of government.Column 1 replicates PT’s results (the corre-sponding first stages are in columns 1a,b oftable 1). Column 2 shows that the estimatesare slightly less precise when the second-stage covariates are included in the first stage,though the dummy for a presidential systemcontinues to be statistically significant. Thisshows that leaving the second-stage covari-ates out of the first stage is unlikely to havecaused a major bias in this case.

Columns 3 and 4 exclude the Hall–Jonesinstruments and show that there is no longera significant effect of the form of govern-ment or the electoral system on the size ofgovernment. For example, the coefficient onthe presidential dummy in column 3 is –2.01(standard error = 5.11) as compared to –8.65(standard error = 3.61) in column 1.Evidently, the Hall–Jones instruments areessential for PT’s instrumentation strategy.

Table 3 shows the 2SLS results for theother major outcome variable that PT look atin their chapter 6, the composition of spend-ing, proxied by the share of social spendingand welfare in GDP. The structure of thistable is identical to that of table 2. It alsoshows that the IV estimates of the effect ofconstitutional features on policy outcomesare sensitive to excluding the Hall–Jonesinstruments. Furthermore, in this case,including the second-stage covariates in



TAB

LE

1C

ON

STIT

UT

ION

SEL

EC

TIO

N: F

IRST

STA

GE

EST

IMAT

ES

Pers

son

and

Tabe

llini

(20

03)

Sam

ple

Cro

ss-S

ectio

n O

LS

(1a)

(1b)

(2a)

(2b)

(3a)

(3b)

(4a)

(4b)

Dep

ende

nt V

aria

ble

is C

onst

itutio

nPR

ES

MA

J PR

ES

MA

J PR

ES

MA

J PR

ES

MA

J

CO

N21

50

–0.3

9 –0

.161

–0

.070

–0

.132

0.

095

–0.3

23

0.02

2 –0

.319

(0.1

38)

(0.1

62)

(0.1

49)

(0.1

61)

(0.1

45)

(0.1

53)

(0.1

32)

(0.1

69)

CO

N51

80

–0.1

20

0.07

4 –0

.095

0.

302

0.27

7 0.

169

0.19

7 0.

131

(0.1

82)

(0.2

36)

(0.2

20)

(0.2

48

(0.1

67)

(0.1

52)

(0.1

65)

(0.2

22)

CO

N81

0.

266

0.05

5 0.

161

0.23

8 0.

589

0.00

4 0.

358

–0.0

29(0

.203

) (0

.252

) (0

.245

) (0

.263

) (0

.205

) (0

.183

) (0

.206

) (0

.272

)

LAT

01–1

.366

–0

.884

–0

.786

–0

.410

(0.3

35)

(0.3

88)

(0.5

20)

(0.6

19)

EN

GF

RA

C

–0.6

92

0.91

6 –0

.644

1.

035

(0.1

19)

(0.1

22)

(0.1

27)

(0.1

74)

EU

RF

RA

C

0.42

5 –0

.349

0.

431

–0.4

09(0

.113

) (0

.134

) (0

.153

) (0

.186

)

AG

E

0.54

0 0.

197

0.70

3 0.

083

0.28

0 0.

150

0.60

2 0.

358

(0.3

08)

(0.2

95)

(0.3

20)

(0.2

45)

(0.4

01)

(0.3

29)

(0.3

26)

(0.4

13)

Seco

nd s

tage

cov

aria

tes

NO

N

O

YES

YES

NO

N

O

YES

YES

F-t

est o

n al

l con

stitu

tion

vari

able

s 3.

66

0.52

1.

23

1.35

3.

35

2.61

1.

09

2.20

[0.0

2]

[0.6

7]

[0.3

0]

[0.2

7]

[0.0

2]

[0.0

6]

[0.3

6][0

.10]

F-t

est o

n al

l ins

trum

ents

24

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26.6

9 7.

97

12.0

7[0

.00]

[0

.00]

[0

.00]

[0

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Obs

erva

tions

78

78

77

77

78

78

77

77

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0.48

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40

0.55

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23

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4, P

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and

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se. M

AJ

is a

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my

vari

able

whi

ch is

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1 if

all

the

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ero

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s.



TABLE 2SIZE OF GOVERNMENT AND CONSTITUTIONS: SECOND STAGE INSTRUMENTAL VARIABLE ESTIMATES

Persson and Tabellini (2003) Sample

Cross-Section 2SLS (1) (2) (3) (4)

Dependent Variable is Central Government Expenditure as % GDP

PRES –8.653 –8.653 –2.005 –4.098 (3.614) (4.713) (5.108) (9.183)

MAJ –3.901 –4.233 –9.384 –9.194 (3.448) (3.466) (6.900) (7.896)

Constitution instruments in first stage YES YES YES YES

Hall-Jones instruments in first stage YES YES NO NO

Second stage covariates in first stage NO YES NO YES

Observations 75 75 75 75

Standard errors in parentheses. All columns include but do not report AGE, LYP, TRADE, PROP1564, PROP65,GASTIL, FEDERAL, and OECD in the second stage. All columns include CON2150, CON5180, CON81, andAGE in the first stage. Columns 1 and 2 include LAT01, ENGFRAC, EURFRAC in the first stage. Columns 2and 4 include all second stage covariates in the first stage. See Table 1 for first stage regressions. PRES is adummy variable which is equal to 1 in presidential regimes and zero otheriwse. MAJ is a dummy variable whichis equal to 1 if all the lower house is elected under plurality rule and zero otherwise. See Persson and Tabellini(2003) for data and definitions.

14 PT are upfront about this issue, and argue that“Admittedly, these [Hall–Jones] variables could be corre-lated with other unobserved historical determinants of fis-cal policy or corruption . . . [As] we are confident about theexogeneity of the time dummies for constitutional adop-tion, we can test the validity of the additional instrumentsby exploiting the overidentifying restrictions” (p. 131). Inaddition, the parametric selection models that they reportalso yield very similar estimates to the linear IV estimates.Nevertheless, these checks are unlikely to be sufficient tovalidate the IV estimates. The overidentifying restrictionshave very little power, since, as we saw above, the consti-tutional timing variables have little explanatory power inthe first stage. The parametric selection models, on theother hand, also use the same exclusion restrictions inaddition to the parametric restrictions, so the similarity inthe results is not too surprising.

the first stage also matters to some extent,and the effect of a majoritarian electoralsystem is no longer significant at 5 percentin column 2.

This brief discussion illustrates theimportance of the Hall–Jones instrumentsfor PT’s identification strategy,14 (and also

touches upon the importance of includingsecond-stage covariates in the first stage ofthe IV estimation). The implication is thatthe IV strategy in PT’s book heavily relieson the validity of the Hall–Jones instru-ments. Could these instruments be valid inthe current context?

I believe there are two fundamental rea-sons for these instruments not to be valid.The first is that the Hall–Jones instrumentsare unlikely to be valid for the overall qual-ity of institutions. The second is that evenif these instruments were valid for theoverall quality of institutions, they wouldby implication be invalid for a specific fea-ture of the institutional structure such aspresidentialism or a majoritarian electoralsystem. I discuss these two issues in thenext two sections. This discussion is notonly relevant to PT’s work, but also to anumber of recent papers adopting similarstrategies.



TABLE 3 COMPOSITION OF GOVERNMENT SPENDING AND CONSTITUTIONS:

SECOND STAGE INSTRUMENTAL VARIABLE ESTIMATES

Persson and Tabellini (2003) Sample

Cross-Section 2SLS (1) (2) (3) (4)

Dependent Variable is Central Government Expenditure on SocialServices and Welfare as % GDP

PRES 0.296 0.527 0.615 1.585 (1.791) (2.609) (2.461) (4.734)

MAJ –3.633 –3.645 –3.920 –3.857 (1.663) (1.928) (2.493) (3.041)

Constitution instruments in first stage YES YES YES YES

Hall-Jones instruments in first stage YES YES NO NO

Second stage covariates in first stage NO YES NO YES

Observations 64 64 64 64

Standard errors in parentheses. All columns include but do not report AGE, LYP, TRADE, PROP1564, PROP65,GASTIL, FEDERAL, and OECD in the second stage. All columns include CON2150, CON5180, CON81, andAGE in the first stage. Columns 1 and 2 include LAT01, ENGFRAC, EURFRAC in the first stage. Columns 2and 4 include all second stage covariates in the first stage. See Table 1 for first stage regressions. PRES is adummy variable which is equal to 1 in presidential regimes and zero otheriwse. MAJ is a dummy variable whichis equal to 1 if all the lower house is elected under plurality rule and zero otherwise. See Persson and Tabellini(2003) for data and definitions.

6. Are the Hall–Jones Variables ValidInstruments for Institutions?

Hall and Jones wrote a very importantand influential article emphasizing theimportance of social infrastructure, or insti-tutions on aggregate productivity and eco-nomic growth. Hall and Jones suggestedthat the origins of good institutions aroundthe world lie in Europe, so “proximity” toEurope, as measured by the fraction ofthose speaking European languages and lat-itude, can be used as instruments for thequality of institutions.

Hall and Jones’s paper has alreadybecome a classic. It is not only cited exten-sively, but their arguments are often invokedto use latitude and the fraction of the popu-lation speaking European languages asnative tongues as instrument for variousinstitutional features in the recent empiricalliterature.

This makes it useful to reconsider the the-oretical justification of these instruments.What is the theory underlying theHall–Jones instruments? In broad strokes,Hall and Jones’s theory is as follows. “Goodinstitutions” originated in Western Europeand spread from there to other countries.Therefore, a potential determinant of thequality of institutions is the extent to which acountry has been influenced by Europe’sculture, values and institutions. Hall andJones isolate two channels of Europeaninfluence. The first is through a shared lan-guage, and the second is through geography.Consequently, they argue, countries with agreater fraction of the population speakingEuropean languages and those farther fromthe equator, which were less densely popu-lated and geographically more similar toEurope hence more conducive to Europeanmigration, have benefited from a



benign/beneficial European influence.Based on this theory, they use the fractionsof the population speaking European lan-guages and distance from the equator (lati-tude) as instruments for the overall qualityof institutions.

Some studies, including PT, cite my workwith Simon Johnson and James A. Robinsonas supporting this view. Nevertheless, thetheory, and therefore the instrumentationstrategy, in Acemoglu, Johnson, andRobinson (AJR) (2001) is different. First, inAJR we focus on former European colonieswhere European powers had a large effecton institutional development, often byimposing the institutions and running theseareas as colonies. Second, we do not arguethat European influence was positive (ornegative). Instead, the argument is thatEuropeans had very different effects on dif-ferent colonies depending on what was themost attractive colonization strategy. Inplaces where they faced high mortality rates,they could not settle, and they were morelikely to opt for an extractive strategy, withassociated extractive/bad institutions. Inplaces with low mortality rates, they weremore likely to settle, and good institutionswere more likely to emerge, because thesewere institutions that Europeans themselveswould live under. This contrast is illustratedby a comparison of the United States orAustralia to the European colonies inCentral America, the Caribbean, South Asia,or Africa. In a companion paper, AJR (2002),we documented the similar effect of indige-nous population density. Europeans weremore likely to settle and less likely to pursueextractive strategies in colonies that wereless densely populated.

Let us now revisit the theoretical founda-tions of the Hall–Jones instruments in thelight of this discussion. Neither the resultsin these papers nor historical evidence sup-port the theory that European influencewas generally beneficial (see also Stanley L.Engerman and Kenneth L. Sokoloff 1997).Indeed, the history of the Caribbean

Islands clearly illustrates the adverse effectsof Europeans, which set up repressiveregimes based on slavery and forced labor.Instead, the evidence is more consistentwith the theory that European influencecould be either beneficial or harmful toinstitutional development. Whether or notit was beneficial depended on theEuropean powers’ colonization strategy.

Is it possible that the use of these instru-ments leads to consistent estimates, eventhough the story for identification is notentirely substantiated? There is an argumentto be made here. For example, AJR (2001)show that in the sample of former Europeancolonies, once mortality of European settlersis used as an instrument for institutions, lat-itude has no additional effect on income percapita today. It may then be argued that lat-itude could be used as an instrument andwould capture the same sort of variation assettler mortality. This argument is not com-pelling, however, mostly because latitude isbeing used as an instrument for the wholeworld sample whereas the “experiment” inquestion, European colonization, appliesonly to the former European colonies. Thereis no valid theoretical argument for extend-ing this experiment to the entire world (andfor the sample of former European colonies,there is no reason to use latitude instead ofsettler mortality). For example, for othercountries not affected by European colo-nization, geographic considerations mayhave had other, different effects, which mayor may not be orthogonal to omitted deter-minants of the outcome variables (see, forexample, AJR 2004 on the changing effect ofaccess to the Atlantic for European nationsduring the early modern period).Consequently, there is no justification forusing latitude, or for that matter anything todo with settler mortality rates, in a samplethat includes countries that were themselvesEuropean or were never European colonies.

Overall, the theoretical foundations of theHall–Jones instruments are not entirelycompelling, especially when used for the



entire world, and consequently, there aregood reasons to suspect that they may not beexcludable from the regressions of interest.

7. Cluster of Institutions Versus SpecificInstitutions

The above discussion centered around thequestion of whether the Hall–Jones variablesare valid instruments for the overall qualityof institutions. I now turn to a discussion ofthe problems involved in using these vari-ables as instruments for specific institutions.This has become a common practice in thenewly flourishing empirical political econo-my literature. PT also follow this practiceand use these variables as instruments forthe form of government and electoral rules(indicators of presidential or majoritariansystems). I will argue that there are seriousproblems in this procedure because of inher-ent complementarities between differenttypes of institutions.

To develop this argument, let us put asidethe concerns raised in the previous sectionand suppose that the Hall–Jones instruments(or perhaps settler mortality rates in the for-mer European colonies sample) are valid forthe overall quality of institutions (or thebroad cluster of institutions). This means wenow suppose that they are excludable from asecond-stage regression of economic out-comes (such as aggregate output or produc-tivity) with the broad measure of institutionsas the endogenous regressor.

Here the distinction between a broadcluster of institutions and specific institu-tions is crucial. In AJR (2001), we defined abroad cluster of institutions as a combinationof economic, political, social and legal insti-tutions that are mutually reinforcing. Forexample, it is impossible to think of a systemlike the plantation economies in theCaribbean Islands until the nineteenth cen-tury together with democratic political insti-tutions. This is because a set of economicinstitutions, like the plantation system, thatlead to a very unequal distribution of income

and wealth cannot easily survive with a set ofpolitical institutions that distribute politicalpower equally. Those with political powerwould be greatly tempted to use their powerto redistribute income and change the eco-nomic institutions in line with their interests.Economic institutions that lead to a veryunequal distribution of income and wealthare only consistent with a similarly unequaldistribution of political power, i.e., with dic-tatorships and other repressive regimes. Inthis case, sources of variation that affect abroad cluster of institutions (e.g., economicand political institutions together) would notbe useful in identifying the role of specificinstitutional features.

As an example of the difficulty of this typeof strategy to estimate the effect of specificinstitutions, consider the quasi-naturalexperiment due to international politics, thedivision of Korea into North and South. Thetwo parts of Korea before the division wereethnically, culturally, economically, andsocially very similar. But because of thegeopolitical balance between the UnitedStates and Soviet Union, the South ended uplargely capitalist, while the North becamecommunist. In the following forty years, wewitnessed a large divergence between thesetwo countries. This is a good source of varia-tion to understand the effect of the broadcluster of institutions at the level of “quasi-capitalist” versus “communist” systems.Suppose now that we try to use this source ofvariation to understand the effect of somespecific institutional feature, say financialdevelopment, on economic growth. Itshould be clear that this strategy will lead toa highly biased estimate. It is true that SouthKorea is financially more developed thanNorth Korea. It is also true that the reasonfor this is the division in 1946 (had it notbeen for the division, the North and theSouth would probably have similar levels offinancial development). But this does notmake the division a good experiment tounderstand the effect of financial develop-ment, because this division also caused many



other institutional changes. It is a good labo-ratory for the study of broad institutions, butnot for a study of the specific institutions.

Another example directly related to PT’sempirical work may also be useful. In thefirst-stage relationships shown in table 1, thefraction of the population speaking English isa strong predictor of a majoritarian system,and this fraction may be a predeterminedvariable, shaped, for example, by colonial his-tory. Nevertheless, this is not sufficient for itto be an excludable instrument in estimatingthe causal effect of majoritarian systems,even if as Hall and Jones claim, English influ-ence is conducive to the development ofgood institutions overall. For example, as weknow from Rafael La Porta, FlorencioLopez-de-Silanes, Andrei Shleifer, andRobert W. Vishny (1998), countries moreinfluenced by the English heritage also havemore developed financial markets. So thecorrelation between majoritarian electoralsystems (instrumented by fraction of thepopulation speaking English) and the size ofgovernment may reflect the effect of finan-cial development, which is omitted from theregressions.

To make these issues a little more precise,consider the following structural model:

(7) ,

where Yi denotes the outcome of interest, ββis again a vector of coefficients associatedwith X, which is now assumed to stand for aset of noninstitutional covariates. Gi is ameasure of a broad “cluster of institutions.”Moreover, suppose that there are K > 1 specif-ic institutions, each denoted by Sk, and

(8)

where ν k denotes the effect of specific insti-tution Sk on the cluster of institutions.Suppose that Cov(ui,i) ≠ 0 and/orCov(ui,S

ki) ≠ 0 for some k, so that equation

(cluster) cannot be estimated consistentlyby OLS.

G Sik

Kk

ik

i= +=

∑1

ν µ

Y G ui i i i= + +� X�ββ

Next, suppose that we have an instrumentZi, in particular a country-specific variable,which is potentially related to each of thespecific institutions, i.e.,

(9)

and is a valid instrument for the cluster ofinstitutions, Gi, i.e., Cov(Zi,ui) = 0. So if wehave a good measure of Gi, equation (7) canbe estimated consistently by IV.

However, the objective here is to estimatethe effect of specific institutions. To simplifythe discussion, also assume that Cov(Zi,µi)= 0, and Cov(i,vk

i) = Cov(Zi,vki) = 0 for all k

and Cov(vki,vj

i) = 0 for all j ≠ k. Note that Ski’s

are correlated even if vki ’s are independent,

since they are all affected by Zi. This corre-lation is at the root of the identificationproblems facing IV estimates of the impactof specific institutions.

In the last section, I questioned whetherlatitude could play the role of Zi to estimatethe structural relationship in (7). Now let usput aside the issues raised there, and sup-pose that indeed Cov(Zi,ui) = 0. Can we thenuse Zi as an instrument for a specific institu-tion, say S1? The answer is no. If we were todo this, all of the Sk’s would also load onto S1.

More explicitly, we are now estimating

with IV using Zi as the excluded instru-ment. Given (7) above, the true value of α1

is �1 = ��1. Moreover, from equations (8)and (9),

(10)

We can now see that since, by construction,�

Kk�2νkSk

i is correlated with tZi, plimα1,IV��1,IV. In particular

plimCov

Varˆ

,,� �

��

1 11

1

1

IV i i

i

k

Z u

Z= +

( )( )

= +

� ��ζ

==∑ ( )( )

21

K k ki

i

Z

Z

ν ζζ

VarVar

��

u u Si ik

Kk

ik

i1

2

= + +=

∑� �ν µ .

Y S ui i i i= + +�1 1 1 1X�ββ

S Zik k

i ik= +ζ υ ,



where the second equality exploits (10) andthe fact that Cov(Zi,ui) = Cov(Zi,i) = 0.

Note that in the most extreme case where�1→ 0, even though Cov(Zi,ui) = 0, we canget arbitrarily biased estimates of the effectof S1 on the outcome of interest.

This discussion also makes it clear that theproblem of instrumenting for a specificinstitution, such as S1

i, is in many ways simi-lar to the omitted variable bias, since otherspecific institutions that make up the clusterof institutions, Gi, are omitted from theregression. Even if we include proxies forsome of them, unless we can correctly esti-mate the causal effects of all of those, IVregressions will fail to estimate the causaleffect of the specific institution of interest,S1

i, consistently.For the identification strategy of using Zi

as an instrument for S1 to be valid, we needin addition that �k= 0 for all k = 2, . . . K.Consequently, even if we were convincedthat the Hall–Jones instruments are valid forthe broad cluster of institutions, there is lit-tle justification for using them as an instru-ment for specific institutions such aspresidential or majoritarian systems. Thisdiscussion implies that in IV approaches inpolitical economy, there is often a first-orderquestion of unbundling, meaning going froman understanding of the role of a broad clus-ter of institutions to pinpointing which spe-cific institutions are more important for theeconomic outcomes of interest. I discuss thisproblem further below.

8. What Have We Learned?

I have so far argued that some of the com-mon empirical strategies in the politicaleconomy literature will have difficulty inuncovering the causal effect of specific insti-tutions. Relatedly, PT’s work may not haveestimated the causal effect of majoritarian

== + ∑1 21

kK k kν ζζ

��

,,and presidential systems on the amount ofredistribution, political rents and aggregateproductivity. So one might argue that judgedon the basis of their strong objective of esti-mating causal effects, the book is only a par-tial success. This would be the wrongconclusion, however.

When the body of work in the book istaken as a whole, it is a tremendous success.The correlations that PT document betweenthe form of government and electoral sys-tems and various economic outcomes arevery important. Few comparative politicaleconomy papers can be written from now onthat do not take these stylized facts serious-ly. PT have not necessarily estimated thecausal effects of the form of government andelectoral systems. But even noncausal butrobust relationships are important and valu-able inputs into our thinking and into ourmodels.

Therefore, I believe that overall PT havelargely achieved their ambitious aim of revo-lutionizing comparative political economy,and this book is the most significant contri-bution to this field since Lipset’s work almostfifty years ago. PT have not only pushedcomparative political economy forward, butthey have provided a set of findings that willchallenge all economists and social scien-tists, and likely pave the way for a large bodyof new work in this area. With such animportant contribution, it is then the righttime to wonder what will (and perhapsshould) come next.

9. Unbundling Institutions

I argued above that a source of variationin the broad cluster of institutions is notsufficient to separately estimate the effectsof specific institutional features. In otherwords, we can find clever instruments,from history, sometimes from geography,or international politics, that affect thewhole social organization of a society, butthis is only the first step. It does not enableus to conclude that one specific institution



is more important than another.However, what we want to know in prac-

tice is not only that “institutions” (definedas a broad cluster, and therefore almost nec-essarily as a black box) matter, but whichspecific dimensions of institutions matterfor which outcomes. It is only the latter typeof knowledge that will enable better theo-ries of institutions to be developed andpractical policy recommendations toemerge from this new area. Consequently,the issue of “unbundling institutions,” thatis, understanding the role of specific com-ponents of the broad bundle, is of firstorder importance.

We therefore need to find other strategies,even more clever instruments, or other, per-haps new, econometric techniques to decidewhich specific dimensions of these institu-tions matter. I believe that there is going tobe a lot of exciting research in this area inthe next ten years. Let me discuss a coupleof potential questions, and in some cases,potential avenues for investigation.

1) Contracting institutions versus propertyrights institutions: a key question thatemerges from works that emphasize theimportance of institutions concerns therelative importance and specific effects ofinstitutions that regulate interactionsbetween private citizens (“contractinginstitutions”) and those that constrain thebehavior of political and economic elites(“property rights institutions”). Evidencethat a broad cluster of institutions mattersfor long-run economic development isconsistent with the primary role of bothtypes of institutions. Moreover, there aremany reasons to expect societies thathave better property rights institutions toalso have better contracting institutions,so these two types of institutions are like-ly to covary in practice. So unbundling inthis context is very important.Acemoglu and Johnson (2004) attemptthis type of unbundling. The idea is tocombine the strategy in AJR (2001, 2002),which exploits the effect of local condi-

tions at the colonies on institutional devel-opment together with the strategy of LaPorta, Lopez-de-Silanes, Shleifer, andVishny (1998), which exploits differencesin the identity of the colonizer. While localconditions, in particular the disease envi-ronment and the indigenous populationdensity at the time of colonization, affectthe property rights institutions, the identi-ty of the colonizer is important for thelegal origin and therefore for the con-tracting institutions. We show that thereare almost perfectly “separable” first-stages whereby the identity of the coloniz-er has almost no effect on property rightsinstitutions, while local conditions have noeffect on contracting institutions. Thisenables a multiple IV strategy to separate-ly identify the effects of both types ofinstitutions. The results suggest that whileproperty rights institutions have a first-order impact on all aspects of economicand financial development, contractinginstitutions mainly affect the form offinancial intermediation (and have noeffect on long-run economic growth, oninvestment and on the overall amount offinancial development).

2) Financial development versus contract-ing institutions: a similar unbundlingissue arises in evaluating the role of finan-cial development (and financial institu-tions) and economic development. Alarge literature surveyed in Ross Levine(1997, 2004) documents a robust correla-tion between financial development andeconomic growth. But is this the effect offinancial development, or the directeffect of better contracting institutionsthat enable financial development in thefirst place? More explicitly, better con-tracting institutions will lead to betternonfinancial contracts (such as betweendownstream and upstream firms, firmsand workers, etc.) as well as to improvedfinancial contracts, so in the data whenwe see a society with greater financialdevelopment, it will also have better



nonfinancial contracts. This makes it dif-ficult to identify the effect of financialdevelopment.A potential strategy for unbundling in thiscontext might be to investigate the effectof purely financial reforms that do notchange the scope for nonfinancial con-tracts. Reforms in capital accounts thatare imposed (or “encouraged”) by theIMF or other international bodies, with-out other reforms, could provide oneuseful source of variation.

3) Economic versus political institutions: aneven more formidable task is to separate-ly identify the effects of economic andpolitical institutions. There is a clear com-plementarity between these two types ofinstitutions. For example, an economicsystem like slavery or forced labor cannotbe sustained in a democratic society.Nevertheless, many relevant theoreticaland policy questions require the potentialeffects of economic and political institu-tions to be unbundled. For example,what would be the effects of improvingeconomic institutions under a given set ofpolitical institutions, for example as inChina? This is an area for futureresearch.

4) Different types of economic institutions:the question is which economic institu-tions matter more. Entry barriers? Labormarket regulations? Property rightsenforcement? Limits on governmentcorruption? These are important, butalso very difficult questions. It seemsthat these questions will be almostimpossible to answer with cross-countrydata alone, and micro data investigations,for example, exploiting differences inregulations across markets and regionsappear to be the most promising avenue.Interesting recent work using within-country variation to look at some of theseissues include, among others, work byTimothy Besley and Robin Burgess(2004), who look at the implications ofdifferent labor market regulations across

Indian states, by Thomas J. Holmes(1998), who investigates the implicationsof union laws on the location of manu-facturing plants in the United States, byMarianne Bertrand and Francis Kramarz(2002), who look at labor market effectsof product market regulations, and byJakob Svensson (2003), who exploits dif-ferences across industries to investigatethe amount of bribes that firms inUganda have to pay to officials

5) Formal versus informal political institu-tions: finally, returning to the theme ofPT’s book, how important are formalinstitutions? PT’s work suggests that theyare essential. However, in practice, for-mal and informal institutions are highlycorrelated, and one may conjecture thatchanging constitutions or formal rules ofpolitical decision-making might have lim-ited effects if society at large expects thechanges not to be durable or not to beobeyed. The important results in thisbook notwithstanding, this is also animportant area for future research.

10. Weakly Institutionalized PolitiesAnother area for future research is what

might be referred to as politics in “weaklyinstitutionalized polities.” The body of workthat PT have surveyed and developed furtherin their two books is largely for the analysis of“strongly institutionalized polities,” wherepolitical institutions make politicians, at leastpartially, accountable to citizens. It is not sur-prising that this has been the first focus ofWestern academics, who almost all live instrongly institutionalized polities. But thesame is not true for a large fraction of the pop-ulation of the world. The situation in manycountries in Africa, Central America, and theCaribbean corresponds much more clearly toone of “weakly institutionalized polities,”where state–society relations are fundamen-tally different. Examples of this include, butare not limited to, the extreme kleptocraticregimes of Mobutu in the DemocraticRepublic of the Congo (Zaire), Rafael Trujillo



15 Models of strongly institutionalized polities wouldsuggest that poorly performing leaders should be replacedmore often. In contrast, many disastrous kleptocracies lastfor long periods; Mobutu ruled for thirty-two years,Trujillo for thirty-one, and the Somozas for forty-two years. This longevity is made even more surprising by the fact that many kleptocratic regimes lack both a core constituency of supporters and a firm command of the military.

in the Dominican Republic, the Duvaliers inHaiti, the Somozas in Nicaragua, CharlesTaylor in Liberia, and Ferdinand Marcos inthe Philippines.

Much historical evidence suggests that asystematic study of the political economy ofsuch regimes must depart from some of themodeling approaches of politics in stronglyinstitutionalized polities. While in stronglyinstitutionalized polities, formal political insti-tutions, such as the constitution, the structureof the legislature, or electoral rules, placeconstraints on the behavior of politicians andpolitical elites, and directly influence politicaloutcomes, the same does not appear to be thecase in weakly institutionalized polities.Instead, the nature of politics appears to bedifferent between strongly and weakly institu-tionalized polities. Most importantly, wheninstitutions are strong, citizens have thepower to punish politicians by voting themout of power; when institutions are weak,politicians pursue clientelistic policies thatpunish citizens who fail to support them (seeRobert H. Jackson and Carl G. Rosberg 1982and Acemoglu, Robinson, and ThierryVerdier 2004).

In modeling politics in weakly institutional-ized polities, the first question that emerges istheoretical: how can we understand policymaking and collective decisions in such soci-eties? There are only a few papers thatattempt to develop answers this question. InAcemoglu, Robinson, and Verdier (2004), weconstruct a dynamic model of politics inweakly institutionalized polities based on theidea of “divide and rule.” The key focus is tounderstand how kleptocratic regimes thatimpoverish their citizens can remain in powerfor so long.15 The answer we suggest is that,

16 Bates described the web of inefficient transfers andpolicies in effect in many parts of Africa, but most notablyin Ghana and Zambia. For example, the Ghanaian govern-ment heavily taxed cocoa producers, while at the sametime subsidizing their inputs of seeds and fertilizers. Whilethe simultaneous use of taxes and subsidies may be to alle-viate the negative effects of taxes on investments, theinterpretation in the literature is that the extent of thesepractices in sub-Saharan Africa is beyond what can be jus-tified as an optimal mix of taxes and subsidies.

owing to the absence of strong institutions,rulers can deploy strategies, in particular“divide-and-rule,” to defuse opposition totheir regime. The logic of the divide-and-rulestrategy is to enable a ruler to bribe political-ly pivotal groups off the equilibrium path,ensuring that he can remain in power againstchallenges. By providing selective incentivesand punishments, the divide-and-rule strate-gy exploits the fragility of social cooperationin weakly-institutionalized polities: whenfaced with the threat of being ousted, thekleptocratic ruler intensifies the collectiveaction problem and destroys the coalitionagainst him by bribing the pivotal groups.

A different and innovative answer is givenby Gerard Padro-i-Miquel (2004), who alsoconstructs a dynamic model of politics.Ethnic divisions are the key feature in hismodel. Each ethnic group is afraid of replac-ing their own leader when in power, becausethis increases the probability of a switch ofpower from their own ethnic group to a rivalgroup. This makes the standard method ofcontrolling political elites in strongly-institu-tionalized polities ineffective, and enablesleaders to not only exploit other ethnicgroups but also their own ethnic group.Padro-i-Miquel shows how this frameworkcan account for a puzzling feature of Africanpolitics first highlighted in Robert H. Bates’classic study Markets and States in TropicalAfrica (1981): the simultaneous use of ineffi-cient transfers to and taxes on the samegroup.16 In the logic of Padro-i-Miquel’smodel, this strategy makes sense becauseleaders need to keep their own group happyto remain in power. This sets a limit on theamount of net taxes they can impose on their



own group. However, taxes across groups arelinked, since much lower taxes on one groupwill encourage other groups to switch eco-nomic activity. This then motivates leaders toinefficiently subsidize their own ethnic groupso that they can increase the tax rate on theirown ethnic group, and consequently taxother groups more intensively.

A second crucial area is to constructmodels to understand how weak institu-tions can be strengthened. Although thereis now a number of formal models of thecreation and consolidation of democracy(see the literature review in Acemoglu andRobinson 2005), many of these models arestill motivated by the practice of stronglyinstitutionalized polities.

Finally, there is almost no work on howchanges in formal political institutions affectpolicy and economic outcomes in weaklyinstitutionalized polities. These are all fruitfulareas for future research.

11. Conclusion

This book is an important landmark inpolitical economy. It takes a body of theoreti-cal literature seriously and carefully confrontstheir predictions with data. PT set themselvesthe very ambitious goal of estimating thecausal effects of constitutions, in particular,the form of government and electoral rules.

Bearing in mind the difficulties of estimat-ing causal effects in social sciences, especial-ly in cross-country data, the book is atremendous success. It documents impor-tant and robust correlations between theform of government and electoral systems,on the one hand, and various policy and eco-nomic outcomes, on the other. It also usesstate-of-the-art econometric techniques toestimate causal effects.

I argued above that these methods maynot have been sufficient to arrive at causaleffects, both because of certain conceptualand practical problems. Nevertheless, theachievement here should not be underesti-mated. Even noncausal robust relationshipsare rare in comparative political economy,

and those documented by PT appear to behighly robust and of central importance forour theoretical understanding. Few politicaleconomy papers can be written from nowon that do not take this book, both itsmethodological and empirical contributions,seriously.

Equally important, with the addition ofthis book, (comparative) political economyhas taken one more step toward establishingitself as a major field of economics, and itoffers exciting and important research areasfor further inquiry.

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