del Servizio Studi
Political Institutions and Policy Outcomes:
What are the Stylized Facts?
by Torsten Persson and Guido Tabellini
Number 412 - August 2001
ThepurposeoftheTemididiscussioneseriesistopromote the circulationofworking
papers prepared within the Bank of Italy or presented in Bank seminars by outside
economists with the aim of stimulating comments and suggestions.
The views expressed in the articles are those of the authors and do not involve the
responsibility of the Bank.
ANDREA BRANDOLINI, FABRIZIO BALASSONE, MATTEO BUGAMELLI, FABIO BUSETTI, RICCARDO
CRISTADORO, LUCA DEDOLA, FABIO FORNARI, PATRIZIO PAGANO; RAFFAELA BISCEGLIA
POLITICAL INST ITUTIONS AND POLICY OUT COME S: W HAT ARE T HE
by Torsten Persson∗and Guido Tabellini∗∗
in a panel of 61 democracies from 1960 and onwards. In presidential regimes, the size
of government is smaller and less responsive to income shocks, compared to parliamentary
regimes. Under majoritarian elections, social transfers are smaller and aggregate spending
less responsive to to income shocks than under proportional elections.
shape electoral cycles: only in presidential regimes is fiscal adjustment delayed until after
the elections, and only in proportional and parliamentary systems do social transfers expand
around elections. Several of these empirical regularities are in line with recent theoretical
work; others are still awaiting a theoretical explanation.
JEL classification: H0.
Keywords: comparative politics, constitution, fiscal policy, elections, democracies.
1. Introduction......................................................................... 7
2. Motivation .......................................................................... 9
3. Data ............................................................................... 14
4. Methodology ...................................................................... 20
5. Results............................................................................. 23
5.1 Size and surplus of government ................................................. 23
5.2 Composition of spending ....................................................... 34
6. Conclusion......................................................................... 36
Data Appendix ........................................................................ 39
Tables and figures ..................................................................... 41
References ............................................................................ 61
IIES, Stock ho lm University, London School o f Economics, CEPR and NBER.
∗∗IGIER, Univers ità Bocconi, CEPR and Ces-If o.
A recent literature on comparative politics has asked how political institutions might
shape economic policy. In particular, a number of theoretical contributions by economists
predict that electoral rules and political regimes systematically influence fiscal policy
outcomes: see Persson and Tabellini (2000) for a survey. But empirical work is still scant.
Whereas a large and interesting literature discusses how constitutional features of state and
local governments correlate with policy outcomes (see for instance Bohn and Inman, 1996,
Pommerhene, 1990, Feld and Matsusaka, 2000), only a few empirical studies have compared
fiscal policy in large samples of countries governed by different electoral rules or political
regime. Some recent exceptions are Poterba and Von Hagen (1999), Milesi-Ferretti, Perotti
and Rostagno (2000), and Persson and Tabellini (1999).2
Political scientists have done extensive empirical work on comparative politics for a
long time. But their focus has been on political phenomena, such as the number of parties,
the frequency of elections, or the attributes of governments under different constitutions,
and does not touch on fiscal policy. Castels (1998) and Lijphart (1999) are among the rare
exceptions, but their analyses are confined to correlations and bivariate regressions, relating
a few economic policy outcomes to constitutional features. As a result, very little is known
about whether and how fiscal policy varies across political institutions, particularly when the
analysis is extended to non-OECD countries.
We try to fill this gap. Specifically, we try to establish some stylized facts regarding the
mapping from electoral rules and political regimes to policy outcomes. We look exclusively at
the effects on fiscal policy: the size and composition of government spending and government
deficits. A companion paper (Persson, Tabellini and Trebbi, 2000) studies the incidence of
corruptionacrossdifferent political institutions. Whilesome ofourestimates aimat direct tests
WearegratefulforusefulcommentsfromAlbertoAlesina, Per-AndersEdin, FelixOberholzer-Gee, David
Strömberg, Jakob Svensson, and from participants in seminars at the Bank of England, Berkeley, Bonn, the
EuropeanCentralBank, Stanford,Stockholm, UCL,Uppsala, Warwick,andconferencesinToulouseandLugano.
We would also like to thank Christina Lönnblad for editorial assistance and Gani Aldashev, Alessia Amighini,
Thomas Eisensee, Giovanni Favara, Alessandro Riboni, and Francesco Trebbi for research assistance at various
stages of the project. This research is supported by a TMR-grant from the European Commission, and by grants
from Bocconi University, MURST, and the Swedish Council for Research in the Humanities and Social Sciences.
Tanzi and Schuknecht (2000) provide an extensive and detailed description of fiscal policy in a very large
sample of countries, but they do not ask how policy varies across constitutions.
of specific hypotheses, we also go beyond such tests in our search for systematic relationships
in the data.
The political constitution seems to matters a great deal for policy. We find striking
similarities between presidential regimes and majoritarian electoral rules. Both institutions are
associated with smaller governments, compared to parliamentary and proportional systems.
The quantitative effect is particularly large and robust for presidential regimes and for the
growth of government over time: towards the end of our sample, presidential regimes have
a smaller size of government of about 10 percent of GDP. How government spending
reacts to economic and political events is also systematically correlated with institutions.
Presidential and majoritarian systems react in a more dampened and less persistent fashion
to income shocks, compared to proportional and parliamentary systems. This could reflect a
different composition of spending (social transfer programs tend to be smaller in presidential
and majoritarian democracies), or a different response of the collective decision process
to changing economic circumstances. The peculiar dynamic and stochastic properties of
government spending are also reflected in budget deficits, which are smaller in absolute
value and react less to shocks in presidential and majoritarian democracies. Finally, electoral
cycles in fiscal policy are also institution-dependent. In all countries, tax revenue goes down
(as a fraction of GDP) at the time of the elections. But in presidential regimes, we also
observe spending cuts and painful fiscal adjustments postponed until after the election. And
in parliamentary regimes with proportional elections, social transfers are boosted before and
after the elections. While some of these findings are consistent with the predictions of existing
theories, others indicate interesting puzzles.
Section 2 provides a background, by sketching some of the main ideas in recent
theoretical work. Section 3 describes our data set, in which the measures of fiscal policy
outcomesaswellas political institutionsareclearlymotivatedbythetheory. Section4 explains
our statistical methodology. Section 5 presents our empirical results. Section 6 summarizes
our results and makes suggestions for future research.
Why would political institutions shape economic policy? The basic idea is that policy
choices entail conflicts among different groups of voters, between voters and politicians
(agency problems), and among different politicians. The way these conflicts are resolved,
and thus what fiscal policy we observe, hinges on the political institutions in place. Political
constitutions are like incomplete contracts. They do not impose specific policy choices.
Rather, they spell out how the “control rights” over policy are acquired through elections,
and how they can be exercised in the course of the legislature. Thus, which politicians get the
power to make policy decisions is determined by voters, but is crucially influenced by rules
for elections. Policy choices are made by elected politicians, but are crucially influenced by
rules for rule-making and legislation; that is, what political scientists call the regime type.
the consequences of these institutions for fiscal policy choices. It has focused on the level of
taxation and on the composition of spending, distinguishing between three types of programs:
(i) broad, non-targeted programs benefiting large groups of the electorate; (ii) narrow, targeted
programs benefiting small groups; (iii) programs benefiting mainly incumbent politicians.
Political institutions are modeled as the rules for a specific policy game, where voters elect
politicalrepresentativeswhointurntakedecisions onfiscalpolicy. Inthisliterature, alternative
constitutions amount to alternative rules for how to play this game and “comparative politics”
amounts to comparing equilibrium outcomes. Below, we describe the main ideas in a handful
of recent studies which have applied this comparative politics approach. We just outline the
results, emphasizing the specific predictions regarding the size and composition of public
spending. Interested readers can find the details in Persson and Tabellini (2000, Part III).
Legislative elections around the world differ in several dimensions. The political science
literature emphasizes two: district size and the electoral formula.3
District size simply
determines how many legislators acquire a seat in a voting district. The electoral formula
determines how votes are translated into seats. Under plurality rule, only the individual(s)
winning the highest vote share(s) get the seat(s) in a given district, whereas proportional
Other aspects of the electoral system that differ across countries include thresholds for representation and
the rules governing party lists. See e.g Cox (1997) and Blais and Massicotte (1996) for recent descriptions of
variations in electoral rules across countries.
representation (PR) instead awards seats to parties in proportion to their vote shares. Existing
theoretical papers have formulated specific predictions about the effects of district size and the
electoral formula on policy choices in political equilibrium.
Consider district size first. Persson and Tabellini (1999), (2000, Ch.8) predict
that it influences the composition of government spending. They study two party electoral
competition. Larger voting districts diffuse electoral competition, inducing both parties to
seek support from broad coalitions in the population. Smaller districts instead steer electoral
competition towards narrower, geographical constituencies. With small districts, typically a
party is a sure winner in some districts and a sure loser in others. Electoral competition is
thus concentrated only in some pivotal districts, and both parties have strong incentives to
target redistribution towards such districts. Clearly, broad programs are more effective in
seeking broad support and targeted programs more effective in seeking narrow support. An
example of spending that benefits broad coalitions and cannot easily target specific district is
welfare spending, which is thus predicted to grow with district size. Milesi-Ferretti, Perotti
and Rostagno (2000) reach a similar conclusion, but with a different reasoning. They argue
that with large electoral districts legislators mainly represent socio-economic groups in the
population, while with small districts they mainly represent groups in specific geographic
locations. Thus, with large electoral districts government policy targets powerful socio-
economic groups, while with small districts it targets powerful geographical groups.
How about the electoral formula? One effect of the winner-takes-all property of plurality
rule is to reduce the minimal coalition of voters needed to win the election. Under single-
member districts and plurality, a party can win with only 25 percent of the national vote:
50 percent in 50 percent of the districts. Under full PR it needs 50 percent of the national
vote; politicians are thus induced to internalize the policy benefits for a larger segment of the
population, which lead them to put stronger emphasis on broad programs than under plurality
(Lizzeri and Persico, 2000, Persson and Tabellini, 2000, Ch. 9).
The electoral formula matters for a second reason. Under plurality rule, voters choose
among individual candidates. Under PR, they choose among party lists. Such lists may dilute
the incentives for individual incumbents to perform well, because they entail a double layer
of delegation: individual legislators are accountable to parties, who in turn are accountable to
voters. Persson and Tabellini (2000, Ch. 9) examine the policy consequences in a Holmström
(1982)-style, career-concern models. They derive the predictions that opportunistic electoral
cycles, showing up in spending or taxes, are weaker under PR. The reason is that incumbents’
career concerns are stronger under plurality rule and are at their strongest just before elections.
Even though these two features of electoral rules have logically distinct consequences,
they are highly correlated across real-world electoral systems. Some systems can be described
as majoritarian, combining small voting districts with plurality rule. Archetypes here are
elections to the UK parliament or the US Congress, where the candidate collecting the largest
vote share in a district gets the single seat. Some electoral systems are instead decidedly
proportional, combining large electoral districts with proportional representation. Archetypes
are the Dutch and Israeli elections, where parties obtain seats in proportion to their vote shares
in a single national voting district. While we find some intermediate systems, most countries
fall quite unambiguously into this crude, binary classification. Fortunately, the different
predictions about composition above tend toreinforceeachother. Thus, proportional elections
– with larger districts and PR – should be associated with broader programs and larger welfare
states, and weaker electoral cycles.
A pitfall of the recent theoretical literature is that it has neglected the implications of the
electoral rule on the party structure. Many empirical contributions by political scientists deal
with precisely this aspect (see for instance Lijphart, 1994,1999), emphasizingthat majoritarian
elections are associated with a smaller number of parties. Electoral rules may thus also shape
policy indirectly, through the party structure. On the one hand, proportional elections entail
lower barriers to entry for new parties catering to specific groups of voters. On the other
hand, majoritarian (parliamentary) systems are more likely to produce single-party majority
governments, whereas coalition governments are more likely under proportional elections.
The likely consequences for economic policy have been stressed in several studies. First,
Austen-Smith (2000) takes party structure as exogenous, but assumes that fewer parties are
represented under plurality rule (two parties) than under PR (three parties). He then shows
that the interaction between elections, redistributive taxation, and the formation of economic
groups is likely to produce politico-economic equilibria with higher taxation under PR than
under plurality. Second, the common-pool problem in fiscal policy might be more pervasive
under coalition governments. Kontopoulos and Perotti (1999) have argued that this could lead
to larger government spending, and Scartascini and Crain (2001) provide further evidence
of this effect. Third, as coalition governments have more veto players, the status-quo bias
in the face of adverse shocks could be more pronounced (Roubini and Sachs, 1989, Alesina
and Drazen, 1991). Fourth, government crises are more likely and indeed empirically more
frequent under proportional elections, which could lead to greater policy myopia and larger
budget deficits (Alesina and Tabellini, 1990, Grilli, Masciandaro and Tabellini, 1991). Fifth,
large swings in the ideological preferences of governments as a result of the elections are less
likely under coalition governments. Alesina, Roubini and Cohen (1997) suggest that coalition
governments (and thus proportional elections)correlate withlesspronounced”partisan” cycles
after the elections. Not all these ideas have been fleshed out with the same analytical rigor as
in the more recent theoretical literature. But they can certainly suggest interpretations for the
empirical findings we report below.
Two crucial aspects of the legislative regime concern the powers over legislation: to
make, amend, or veto policy proposals. The first concerns the separation of those powers
across different politicians and offices. The second concerns the maintenance of powers; in
particular, whether the executive needs sustained confidence by a majority in the legislative
As in the case of electoral rules, real-world regimes fall quite unambiguously into a
crude two-way classification with regard to these aspects. Presidential regimes typically have
separation of powers, between the president and Congress, but also between congressional
committees that hold important proposal (agenda-setting) powers in different spheres of policy
(as in the US). But they do not have a confidence requirement: the executive can hold on to his
powers without the support of a majority in Congress. In parliamentary regimes the proposal
powers over legislation are instead concentrated in the hands of the government. Moreover,
the government needs the continuous confidence of a majority in parliament to maintain those
powers throughout an entire election period.
Why should separation of powers matter for policy?A classical argument is that
checks and balances constrain politicians from abusing their powers. Persson, Roland, and
Tabellini (1997, 2000) formally demonstrate this old point in models where incumbents are
held accountable by retrospective voters. The upshot is that we should expect weaker political
accountability in parliamentary regimes, resulting in higher rents and higher taxes.
The confidence requirement has other effects. Parties supporting the executive hold
valuable proposal powers which they risk losing in a government crisis.Therefore, a
confidence requirement creates strong incentives to maintain a stable majority when voting
on policy proposals in the legislature. The absence of a confidence requirement instead leads
to more unstable coalitions and less discipline within the majority.
Building on this idea of “legislative cohesion”, due to Diermeier and Feddersen (1998),
Persson, Roland and Tabellini (2000) derive two additional predictions. In parliamentary
regimes, astablemajorityof legislators tends to pursuethejoint interest of its voters. Spending
in parliamentary regimes thus optimally becomes directed towards broad programs that benefit
a majority of voters, such as social security and welfare spending. In presidential regimes,
instead, the (relative) lack of such a majority tends to pit the interests of different minorities
against each other for different issues on the legislative agenda. As a result, the allocation of
spending targets powerful minorities, typically the constituency of the powerful officeholders
such as the heads of committees in Congress. In parliamentary regimes, the stable majority
of incumbent legislators, and its voters, become prospective residual claimants on additional
revenue. Both favor high taxes and high spending. In presidential regimes, on the other hand,
majorities are not residual claimants on revenue and therefore resist high spending. These
forces produce larger governments (higher taxes) and broader social transfer programs in
Let us summarize the main predictions with the help of Table 1. According to the theory,
presidential regimes have smaller governments than parliamentary regimes and less spending
on broad social security and welfare programs. Under majoritarian elections, we should
observe less spending on broad social security and welfare programs than under proportional
elections. The common-pool argument (and the model suggested by Austen-Smith, 2000)
suggests that the electoral rule could also matter for the size of government, with proportional
elections associated with bigger governments. These are all cross-sectional predictions, in that
they have been derived by comparing equilibria in static models.
Some of the theoretical ideas summarized above also have dynamic predictions. Models
stressing the greater status-quo bias and myopia of coalition governments would predict that
proportional-parliamentary systems have larger steady-state debts, and – during the transition
– larger budget deficits. The stronger incentive to perform under majoritarian elections suggest
that majoritarian-parliamentary countries might have more pronounced electoral cycles than
proportional-parliamentary countries. We have no theoretical prior about deficits and electoral
cycles in presidential regimes. Similarly, to derive specific implications about the reaction to
shocks under thesesystems, one would needa more precise dynamicmodel, including detailed
assumptions about status-quo policy.
In putting our data set together, we have relied on the theory described in Section 2
for the measurement of political institutions and fiscal policy outcomes. Data availability
also determines the sample, which comprises yearly data for 61 countries over almost four
decades (1960-98). This panel includes a large number of economic, social and political
variables. Because of missing data and our rules for sampling (described next), however, it
is an unbalanced panel. The sources for all the data used in the paper are listed in the Data
The theory suggests that we should confine our study to countries with democratic
political institutions. Here, we have relied on a well-known classification by Freedom House.
values being associated with better democratic institutions.4To assess a country’s democratic
status in a particular year, we took the average of these two indexes. The Gastil indices are
available annually, from 1972 and onwards. For the earlier period, we follow Barro (1998) and
rely on a measure compiled by Bollen (1990), available every five years (which we re-scaled
onto a scale from 1 to 7).
We use three different rules for including countries in the sample, and we report results
for all three samples. The most permissive one is to include a country from the point in time
when it first obtains a Gastil-score of 5 or lower, but not exclude it from the sample in the
wake of a temporarily higher score reflecting restricted democratic rights. This rule permits
a maximum of 61 countries in the sample. We refer to this sample of countries as the Broad
According to the index, countries scoring 1 or 2 are “free”, countries scoring from 3 to 5 “semi-free”,
while countries scoring 6 or 7 are “non-free”.
sample. Our Default sample relies on a more restrictive rule, namely to exclude a country
from the sample in any year when it has a Gastil score of 3.5 or lower. This rule cuts the
number of annual observations in the panel by about 350. As an example, the more restrictive
rule temporarily excludes countries like Turkey (intermittently) and Argentina (in the 80s)
after their first entry into the panel. A yet more restrictive rule identifies a Narrow sample as
those countries and years where the Gastil score is less than or equal to 2. Here we lose many
more observations, particularly in the early part of the sample, since we are really restricting
attention to well functioning democracies. As in the Default sample, a few countries enter
and exit from the sample at different points of time. Throughout, we treat these censored
observations as randomly missing and do not attempt to model sample selection. The three
samples are listed in Table 2, along with our classification of regime types and electoral rules
(see the next subsection). As an example, Chile enters the Broad sample for the full sample
period, exits from the Default sample between 1974 and 1988, and is only included in the
Narrow sample from 1991 and onwards.
Which political institutions?
Following the theoretical discussion in Section 2, we classify electoral rules and regime
types by means of two indicator (dummy) variables: MAJ and PRES. Majoritarian countries
(MAJ = 1) are those that relied exclusively on plurality rule in its previous most recent election
to the legislature (lower house), the others are proportional (MAJ = 0). Relying on district size
rather than the electoral formula would produce a similar but not identical classification.5In
some sensitivity analysis, not reported below, we have also allowed for a finer partition that
discriminates between three types: majority, proportional and mixed systems. But when it
comes to the effect on fiscal policy outcomes, the effects of mixed and proportional systems
appear to be similar.
With regard to regime type, we classify as presidential (PRES = 1) countries where
the executive is not accountable to the legislature through a vote of confidence, and those
where it is as parliamentary (PRES = 0). Thus, we try to capture the institutions producing
stable legislative majorities, as discussed in Section 2. (We have not tried to classify countries
on the basis of the checks and balances entailed in the separation of powers granted by their
Persson and Tabellini (1999) rely on district size, classifying all countries with an average district size
below two (seats per district) as majoritarian, others as proportional.
constitutions.) In building this index we had to assess whether or not the office of the President
has executive powers in the realm of fiscal policy. If not, and if the government is instead
accountable to Parliament through a confidence requirement, the country is classified as a
parliamentary regime. In evaluating the executive powers of the President, we mainly relied
on Shugart and Carey (1992).
There are very few changes over time in these classifications (PRES does not vary at
all, whereas MAJ displays time variation in France (which had a brief period of proportional
representation in 1985-86) and in Cyprus only. This stability reflects an inertia of political
institutions sometimes called an “iron law” by political scientists. The lack of time variation is
unfortunate in that it provides us with almost no “experiments” in the form of regime changes.
But it is also an indication that it may be correct to treat institutions as given by history, and
not influenced by reverse causation going from policy outcomes to institutions.
Figure 1 illustrates the institutional variation across countries in 1995. The colored
portions of the map represent the 61 countries inthe sample. Striped areas indicate presidential
regimes (PRES = 1), solid areas parliamentary regimes (PRES = 0). Darker shade indicates
majoritarian elections (MAJ = 1), lighter shade proportional elections (MAJ = 0). The least
common system is the US-style (gray striped) combination of a presidential regime with
majoritarian elections, with only five countries. But each of the other three combinations
is well represented in the sample. In the last two columns of Table 2, we report the values of
MAJ and PRES (averaged over time) for all the countries in our samples.
As the map illustrates, using theory in the classification sometimes produces results
contrary to popular perception. According to our classification, parliamentary regimes include
France, Portugal and Finland, with a directly elected president, but where the government
is accountable to the elected assembly and the president has no or little executive powers
over fiscal policy. Conversely, the presidential regimes include Switzerland, where there is no
popularly elected president but the permanent coalition executive cannot be brought down by
the legislative assembly.6
Even a cursory look at the map reveals that our institutional classification does not
produce a random outcome. The electoral rule does not exhibit a particular pattern in terms
The Swiss constitution indeed resembles the US constitution in many respects beyond the absence of a
of development, but most Anglo-Saxon countries and countries of British colonial origin
have MAJ = 1 while most of Europe and South America has MAJ = 0. Presidential
regimes are largely confined to non-OECD countries (among the OECD-countries, only the
US and Switzerland have PRES = 1). Moreover, many presidential regimes happen to
be in Central and South America, though the sample also includes several non-presidential
Caribbean countries. Other presidential regimes are Nepal, the Philippines, and Senegal.
This non-random pattern of constitutions in our sample raises a fundamental question:
canwe really treat theconstitution as exogenous intheempirical analysis that follows?It could
very well be that countries self-select into constitutions on the basis of historical variables and
collective preferences that also influence policy decisions. To take care of this problem, in
the regressions reported below we try to control for a large set of historical and geographical
variables that might also explain the constitutional origin of a country. But in this paper we do
not seek to explain the constitutional choice itself. In a companion paper (Persson, Tabellini
and Trebbi, 2000), however, we also rely a non-parametric estimator that explicitly allows for
endogenous selection of countries into alternative electoral rules.
Which fiscal policy outcomes?
We include fiscal-policy outcomes as suggested by the theory. Thus, we measure the
size of government mainly by the ratio of central government spending (inclusive of social
security) to GDP, expressed as a percentage (CGEXP). But we have also looked at central
government revenues and at general government spending, both as a percentage of GDP. For
the composition of government spending we use two measures: social security and welfare
on goods and services (SSW/GDS). The presumption is that broad transfer programs, like
pensions and unemployment insurance, are much harder to target towards narrow geographic
constituencies compared to spending on goods and services. Finally, we look at the size of the
budget surplus of the central government, as a percent of GDP (SURPLUS).
The measures of size and deficits are available for most OECD countries for the entire
period 1960-1998. For many developing countries availability is limited to the period from
the 1970s and onward. Similarly, the measures of the composition of spending do not become
available until the early 1970s. The statistical source for all these variables is the IMF. For
the size of government, budget deficits and debts, we rely on IFS data which is available for a
longer time series. General government spending and the composition of spending are instead
extracted from the GFS database.
These policy measures vary a great deal, both across time and countries.As an
illustration consider Figure 2, which shows the size of government as measured by central
expenditures in our sample. In the figure, we see that government expenditure in a typical year
ranges from below 10 percent of GDP to above 50 percent. We also see how the distribution
drifts upwards over time, reflecting growth in the average size of government – the curve in
the graph – by about 8 percent of GDP from the 1960s to the mid 1990s. Most of this growth
takes place in the 1970s and 80s.
Our measures of the composition of spending also show a wide distribution where
spending on social security and welfare drifts upwards at least until the mid 1980s. The
deficits are also widely distributed across countries, with average deficits having their peak
in the period from the mid 70s to the mid 80s.
Given that we mainly rely on central government spending in our analysis, a natural
question is whether this matters. Suppose, for instance, that presidential regimes were more
decentralized than parliamentary regimes. By looking at central government spending only,
we might than mistakenly interpret a lower size of central government in presidential countries
as due to the regime type, while it could simply reflect their lower degree of centralization.
Fortunately, however, centralization of spending is not systematically correlated with the
political constitution, at least in the 41 countries and in the years were data on both levels
of government are available - see the last subsection below.
Which socio-economic controls?
The theory we have surveyed in Section 2 should clearly be understood as providing
ceteris paribus predictions about fiscal policy. Therefore, we control for other variables likely
to shape government outlays and revenues. Specifically, we always include in our regressions
the level of development, measured by the log of real per capita income (LYH), a measure of
openness (TRADE), defined as exports plus imports over GDP, and two variables measuring
the demographic composition, defined as the percentages of the population between 15 and 64
years of age (PROP1564), and above 65 years of age (PROP65), respectively. These variables
(1978), Rodrik (1998), and Persson and Tabellini (1999). We will refer to this basic set of
controls by X1.
Depending on the specification, the dependent variable and the frequency of sampling,
we have also included several other variables, such as the price of oil in US dollars (OIL),
income shocks, measuredeitherasthegrowthrateofrealGDP orasthelogdifferencebetween
real GDP and its trend computed with the Hodrick-Prescott filter (YSHOCK), and levels of
government debt, as a percentage of GDP (DEBT).
To cope with the non-random pattern of constitutions noted above, we also use several
indicator variables, measuring geographic locations, legal origin, colonial origins, federal or
unitary structure, and election dates. All these variables are defined more precisely in the Data
Tables 3a and 3b display the correlation matrix between our main variables of interest.
Table 3a shows cross-country correlations, with data averaged over the full period for which
we have observations for each variable-country pair.Table 3b instead pools the yearly
observations for all countries. Both tables display a similar pattern. While the electoral
rule appears uncorrelated with the socio-economic controls, the regime type is much more
correlated with the level of development and the demographic structure, in line with our
previous observation that most presidential regimes are outside the OECD countries. We
also see that presidential regimes are associated with smaller governments and smaller social
security and welfare spending, whereas majoritarian electoral rules are correlated with larger
surpluses and smaller social security and welfare spending.These correlations are not
inconsistent with the theoretical predictions summarized in Table 1.
As Table 3a shows the variable CENTRAL – defined as the ratio of central to general
government expenditure – is neither systematically related to our measures of institutions, nor
to the overall size of government. (This variable can be constructed for 41 countries between
the early 1970s and the late 1980s.) The lack of correlation with political institutions reassures
us that focusing on central government spending will not systematically bias our results.
Our empirical analysis is certainly motivated by theory. We aim as much at establishing
empirical regularities, however, as at testing hypotheses derived from specific models. That
is, we would like to succinctly describe systematic relations in the data, establishing some
stylized facts about the effect of institutions on policy outcomes. For this reason, we follow an
A general formulation
The regressions we estimate in the paper are all derived from the following general
yit= αi+ γisit+ βiqt+ δxit+ ηzi+ uit. (1)
In (1), yitdenotes a specific policy outcome in country i in year t and Greek boldface letters
denote vectors of unknown parameters to be estimated, possibly varying across countries or
groups of countries. We allow for a country-specific average, αi. Policy can be influenced
directly by the institutions zit, concretely the two dummy variables MAJ and PRES. It can
also be affected by vectors of socio-economic control variables: sitand qtdenote country-
specific and common variables the slope coefficients of which are allowed to vary, whereas the
variables in xitare instead constrained to have the same impact on all countries. Finally, uit
is an unobserved error term.
We want to test two sets of hypotheses. The first is whether institutions have a direct
impact on policy outcomes, which is really what most of the theory discussed in Section 2 was
about. The nul hypothesis corresponding to this question can be formulated as:
0: η = 0 .
To see how we may test the first hypothesis, HD
0, we take time averages of (1) within
each country, and rewrite it as (a bar over a variable denotes a time average):
¯ yi= (αi+ γi¯ si+ βi¯ q) + ηzi+ δ¯ xi+ ¯ ui. (2)
Equation (2) can be estimated on cross-sectional data with standard methods, with the
estimated intercept capturing the effect of all variables within brackets. The t-statistic on
PRES and MAJ is then a test of the nul hypothesis HD
Time variation in the data
Such cross-sectional estimates have the advantage of being closely related to some
existing theories. But they do not exploit the time variation in the data.Moreover, they
might be subject to simultaneity problems in the form of omitted-variable bias: as discussed
above some forces selecting political institutions in historical times may also drive economic
policy outcomes. The institutional variation over time is too small to circumvent this problem
of “historical omitted variables” by conventional fixed-effects, panel-data estimation. For
practical purposes, zitis given by a constant, zi, equal to the time average zi. Thus, we cannot
separately estimatetheeffectsonpolicy ofacountry’s institutions,zi,andothertime-invariant,
country-specific features, αi.
For this reason we also ask a slightly different question, namely whether political
institutions have an indirect, or non-linear, effect on policy. In particular, we ask whether
different electoral rules and political regimes induce different policy responses to economic
and political events. Even if the cross-section results might be plagued by simultaneity, it is
much less plausible that the forces selecting the observed political institutions in historical
times would be systematically correlated with the response to economic and political events
during our recent sample period.
The nul hypothesis corresponding to this second question is whether countries with
different values of zinevertheless have the same coefficients γ and β in (1):
0: γi= γj and/or
Recall, however, that the specific theoretical contributions discussed in Section 2, are either
static, or have rather loose predictions concerning the link between institutions and policies.
Most of our tests for indirect effects (non-linearities) should thus be seen as a search for
empirical regularities rather than tests of specific predictions.
Non-observable common events
There are various ways of testing HI
0, that is, the absence of an indirect effect of
institutions. It is plausible that a set of common economic and political events have affected
fiscal policy in all countries. We need only think about the worldwide turn to the left in the late
1960s and 70s, or the productivity slowdown and oil shocks in the 1970s and 80s. But suppose
we do not want to commit to, or cannot observe, all such events. Blanchard and Wolfers
(2000) suggest a simple statistical method for estimating how labor-market institutions might
influence the adjustment of unemployment to unobservable shocks. Milesi-Ferretti, Perotti
and Rostagno (2000) indeed apply this method to study how the proportionality of electoral
systems affects policy in the OECD countries.
Assume that the response to observable country-specific variables is the same in all
countries, γi= γjin (1). Then we can lump all the variables in sittogether with those in
xitand rewrite (1) as:
yit= (αi+ ηzi) + (1 + λ(zi− z))βqt+ δxit+ uit. (3)
We can use a set of time dummies (one per time period) to estimate, βqt, the common effect of
the common events in (3). The institution-specific effect of common events qtis proportional
to the term λ(zi− z) on the right-hand side, where z is the cross-country average of zi. The
form of (3) tells us to estimate the crucial parameter λ by NLS and include fixed effects to
pick up the country-specific intercept given by the first term. We use both annual data and
five-year averages. The latter may be more robust to measurement error and allow better for
discretionary adjustments of policy than yearly data.
Observable economic events
Yet another way of testing whether institutions induce different policy responses to
shocks and other variables is to focus on specific observable events. These may be economic
events, such as changes in the price of oil, country income, or changes in population structure.
To assess whether the impact of such common or country-specific events on policy outcomes
depends on institutions, we can re-write (1) as:
yit= (αi+ ηzi) + (β + λzi)qt+ (γ + µzi)sit+ δxit+ uit. (4)
Finding coefficients µ or λ different from zero thus implies an indirect effect of institutions
through these observable events. We use two basic estimation methods: (i) fixed effects
estimation, to control for the first country-specific term on the right-hand side of (4);
sometimes we jointly estimate spending, revenues and deficit equation by seemingly unrelated
variables. In (i ) and (ii) we always include the lagged dependent variable yit−1either in xit
or in sit.7We also report some GLS estimates of the difference specification (with no lagged
dependent variable), to allow for heteroskedasticity and panel-specific autocorrelation in uit.
Finally, we test for an institution-dependent response to observable political events, in
the form of elections. As we saw in Section 2, theory indicates that we should expect at least
the electoral rule to affect the strength of the electoral cycle. For this purpose, we construct
an indicator variable, ELt, taking a value of 1 if there was an election in country i in year t,
and 0 otherwise (sometimes, as noted below, ELtequals 1 if there was an election in either
year t or year t + 1). For presidential regimes, the election date is that of the president, for
parliamentary regimes it is that of the legislative assembly’s lower house. We then expand sit,
the vector of country-specific events, to include indicator variables for election years, ELt,
and post-election years, ELt−1. Otherwise, the specification is identical to that in our tests
for institution-dependent responses to economic events. The estimation methods are also the
same as those described above, except that the specification includes a set of common time
dummies, to allow a more precise estimation of the electoral cycle.
In this section, we report the results obtained by applying the methodology discussed
in the previous section to our three policy outcomes: the size of government, the government
surplus and the composition of government spending.
5.1 Size and surplus of government
As is well known, the presence of a lagged dependent variable can bias the fixed-effects estimator even if
the error term is not correlated over time. But in panels where the time series dimension is as long as ours, the
bias is rather small. Transforming the data to first differences removes the fixed effect part of the error term, but
may aggravate the correlation between the error termand the lagged dependent variable (see, for instance Baltagi,
1995, Ch 8). This is why when differencing we rely on instrumental variable estimation, where the instruments
are the lagged explanatory variables (in differences) and the lagged dependent variable in level lagged twice, as
suggested by Anderson and Hsiao (1981) and Arrellano and Bond (1991).
Cross-country variation in the size of government
We begin with the cross-sectional regressions testing HD
0for the presence of a direct
effect of institutions on the size of government. The results are displayed in Table 4. The
major dependent variable is expenditures by central government (Columns 1-3 and 7), but we
also include results for central government revenue (Columns 4-5) and general government
expenditure (Column 6). Every specification includes our basic set of controls X1and all
but one also include dummies for continents and colonial origin. Every regression except
the last one relies on data from the full length of the panel. Most regressions refer to our
Default sample of countries (a Gastil index less than or equal to 3.5, applied year by year), but
two (Columns 3 and 5) refer to the Broad sample. All variables are measured in levels. The
estimation method is Weighted Least Squares, where each country’s weight is proportional
to the length of its panel (the results for unweighted OLS regressions are similar). The table
displays the estimated η parameters for the PRES and MAJ dummies. Bracketed expressions
are p-values for false rejection of η = 0. Boldface font denotes a coefficient significantly
different from zero at the 10 percent level.
Our two institutional measures always enter with a negative sign. The effect for MAJ
is statistically insignificant in half the cases. The finding that majoritarian countries have
significantly smaller governments in terms of revenue but not in terms of spending turns
out to reflect systematically smaller deficits.
8Evidence of a large and statistically robust
negative effect of majoritarian elections is limited to general government expenditures. Note,
however, that – due to data availability – the panel in this case is both shorter and restricted
to a much smaller number of countries. Our result that majoritarian countries have smaller
general governments is consistent with the findings by Milesi-Ferretti et al. (2000) for the
The presidential dummy variable is instead consistently significant, except in the case of
general government where the sample includes considerably fewer presidential regimes, and
in the broad sample that includes the more dubious democracies. The finding that presidential
Similar cross-sectional estimates for the government surplus indicate that average deficits are smaller
in countries with either presidential regimes or majoritarian elections. The effect of the electoral system is
considerably more robust to inclusion of regional and colonial dummies, however. Consistent with our findings
on spending and revenue in Table 4, the estimates imply a smaller average deficit by 1.5 to 2 percent of GDP
under plurality rule.
regimes have smaller governments is clearly in line with the theoretical predictioninSection 2.
According to the point estimates, the effect is substantial: about 5 percent of GDP. It appears
to be slightly smaller in the larger sample, which corresponds to the broader definition of
In some specifications, not reported, we also included a dummy variable taking a value
of 1 for federal countries, and 0 otherwise. The coefficients of interest, of PRES and MAJ,
were never affected. The federalism variable had a negative estimated coefficient that was
statistically significant in some regressions but not in others.9
As the last column shows, the negative effect of PRES is much stronger – above 10
percent of GDP – for cross sections based on data from the 1990s, rather than the whole
sample. It is also statistically much more robust. These findings are consistent with the
empirical results in Persson and Tabellini (1999), who considered data from around 1990.
Together, the findings suggest that the negative sign of the PRES dummy might largely reflect
a faster growth of government in parliamentary regimes in the last four decades. As Figure 3
illustrates, this time pattern is clearly visible already in the raw data. The graph is identical
to Figure 2, except that the data is partitioned into presidential regimes, marked with black
diamonds and a thick curve for the average, and parliamentary regimes, marked with circles
and a thin curve.10
Unobservable common events and the size of government
Next, we turn to the time variation in the data, testing HI
0for (the absence of) an
institution-dependent reaction of the size of government to economic and political events.
We begin with the effect of unobservable common events variables, using the specification in
Table 5 displays selected results for expenditures and revenue as the dependent variable,
for yearly data and five-year averages, and for the broad and default sample of countries.
We relied on threee very closely related classifications of countries into federal or unitary states, provided
by Boix (2000), Scartascini and Crain (2000) and Treisman (2000), that mainly look at the political structure and
the authonomy of states and local governments. Scartsascini and Crain (2000) find a robust and significant effect
of federalism on the size of government in a similar sample of countries. These measures of federalism, like the
centralization of spending discussed in the previous section, are uncorrelated with both MAJ and PRES.
The result that the estimated coefficient on PRES is larger in absolute value in the more recent cross
sectional estimates is not due to a different sample of countries beeing included in later years compared to the
early period, since it holds even if we hold the sample of countries fixed.
All variables are measured in levels and each specification includes country fixed effects
on top of the basic controls in X1. The first two rows in the table report the coefficients
on the institutional variables: our estimates of λ in (3). The results remain similar if we
extend the vector of observable controls to include the lagged dependent variable or income
shocks, as in Table 6 below. Both PRES and MAJ are negative and highly significant across
One way of interpreting the results is to consider a common event in some period t
that raises government spending by 1 percent of GDP in an average country: i.e., an event
corresponding to β(qt− qt−1) = 1. Then, a coefficient of about -1 on PRES means that the
regimes (recall that ziin (3) is adjusted by the sample mean, which is about 0.4 for PRES).
Similarly, the effect is
3of a percent smaller under majoritarian rather than proportional
elections. Identical specifications for the government surplus (not shown) produce similar
The estimated effects of the common events on the size of government, the sequence
of βqtin (3), generally reflect the time pattern suggested by Figures 2 and 3: the estimated
coefficients on the time dummies grow from the beginning of the sample until the mid 1980s,
thenthey remainconstant ordropslightly. Theirsigndependontheprecisespecification(since
we include fixed effects, data are measured in deviations from country means), but their time
profile is stable. Figure 4 illustrates the estimated coefficients of the time dummies pertaining
to column 1 in Table 5. The effects of the common events are shown by the dashed line for
an average country, by the thick solid line for a presidential regime (PRES = 1), and by a thin
solid line for a parliamentary regime (PRES = 0). The negative parameter estimates reported
in Table 5 thus suggest that whatever unobservable events caused the growth in government
in the sample as a whole, their effect was significantly smaller in countries with presidential
regimes and majoritarian elections.
Another way of gauging the results is thus to consider the cumulative effect of the
common events over the course of the sample, as measured by β(qT−q1) – in terms of Figure
NLS estimation of the adjustment of the government surplus suggest that unobservable common events
have smaller effects in presidential regimes and under majoritarian elections. An unobservable event that raises
theaverage country’s surplusby 1 percent of GDP thus has an effect about 0.5 percent smaller both in presidential
(vs. parliamentary) regimes and under majoritarian (vs. proportional) elections.
4 this measure corresponds to the vertical distance between the first and the last observation.
The cumulative effect is positive on average (i.e., for the sample as a whole). The last two
rows in Table 5 show how much this cumulative effect differs across institutions, according
to our point estimates. For government spending, the difference between presidential and
parliamentary regimes is just above 10 percent of GDP, which well matches our estimate in the
last columnofTable4ofa cross-sectional differenceinthe1990s ofjustabove 10percent. The
influence of the electoral rule is also statistically significant but quantitatively less important,
between 3 and 6 percentage points of GDP, again about the same order of magnitude as in the
Altogether, the results in Tables 4 and 5 convey a similar message. The size
of government is strongly influenced by the political constitution. Proportional and
parliamentary systems spend the most, while presidential regimes and countries electing their
legislatures by plurality rules spend the least. The regime type has a larger and more robust
effect than the electoral rule.
Observable economic events and the size of government
We now ask whether the impact of observable determinants of the size of government
depends on institutions. We mainly focus on income shocks, since they are one of the main
sources of time variation in government outlays and receipts. Our goal is to find out whether
the cyclical response of fiscal policy is affected by the political constitution. We measure
income shocks (YSHOCK) as the log-deviation of real income from its (Hodrick-Prescott)
trend. We then interact this variable with our two measures of institutions, so as to estimate
the coefficients µ and λ in equation (4). As institutions might also influence the persistence
of spending or taxation after an income shock, we also interact the lagged dependent variable
with PRES and MAJ. Throughout, we treat income shocks as exogenous in the regression.
Their amplitude is about the same on average in countries ruled by different institutions.
There are several reasons to expect that the cyclical response of fiscal policy might
be influenced by the constitution. First, cyclical fluctuations induce an automatic response
of entitlement spending: welfare spending as a fraction of GDP is likely to increase more
than other government outlays during cyclical downturns. But the constitution is likely to
influence the relative importance of entitlement spending. According to the theories reviewed
in section 2, proportional and parliamentary systems should have bigger welfare states. This
prior is also born out in the data: as further discussed below, parliamentary countries with
proportional elections devote almost 12 percent of GDP on average (across countries and
years) to social security and welfare spending. In the remaining groups (presidential or
parliamentary-majoritarian), this average is about 4-5 percent of GDP. Hence, we should
expect spending to be more counter-cyclical and more elastic to cyclical fluctuations in
proportional-parliamentary systems .
Second, the constitution might also have a direct effect on the discretionary reaction of
policy to exogenous events. Coalition governments are often said to have a greater status quo
bias than single party majorities, because of the difficulties of bargaining within the governing
coalitions. The number of veto players is generally thought to be higher in presidential
regimes, because of their stronger separation of powers. More generally, the different rules
for legislative bargaining in presidential and parliamentary democracies suggest that shocks to
the status quo might induce different policy reactions in these regimes. Here, however, it is
more difficult topredict theobservedresponseofgovernment spendingorrevenue toaggregate
Yet another possibility is that some types of democracies are more likely to face
borrowing constraints in financial markets. As already noted, many presidential regimes are
in Latin America, where sovereign debt crisis or exchange rate crisis have been more frequent
than in other democracies. Borrowing constraints would impart a procyclical bias to fiscal
policy: governments are forced to cut spending or raise revenues when hit by a recession or by
a financial crisis, since they cannot let the deficit absorb the shock. Indeed, other studies have
shown that fiscal policy in Latin America tends to be much more pro-cyclical than elsewhere
– see in particular Gavin and Perotti (1997).
Table 6 displays our estimates, for government spending and revenues (of central
government only). We rely on the three estimation methods discussed in Section 4, namely in
levels with country fixed effects, and in differences with instrumental variables and with GLS.
When estimating in levels, the spending and revenues equation are often jointly estimated by
SUR as indicated. The vector of other controls X2, not reported in the table, includes the
same basic variable as in the previous tables, plus the oil price and the trend of aggregate
real income from which the shock is computed. Time-dummy variables, colonial origin
and continental dummy variables are not included in the regression. A P* in front of a
variable denotes that the variable is interacted with the PRES dummy variable, while a M*
denotes interaction with the MAJ dummy. The results we report here are robust to estimation
methods, samples and measurements (we also measured income shocks as the yearly growth
rate in income, and obtained similar findings). We also tried to interact institutions with other
common and country-specific socio-economic variables, such as the oil price or the proportion
of population above 65 years of age. Some of these interaction terms were occasionally
significantly different from zero; although not robust to specification or estimation method,
these results reinforce the general message below.
The central message of Table 6 is that institutions matter a great deal. Consider the first
three columns of the table. In proportional and parliamentary countries, income shocks affect
central government spending as a proportion of GDP. The estimated coefficient of YSHOCK is
consistently negative with a value around - 0.2, meaning that a 10 percent drop in real income
induces a rise in the spending ratio of 2 percentage points. When the size of government is
measured by revenues, rather than by spending, the estimated coefficient drops in absolute
value, but remains negative and statically significant. Because spending and revenue are
highly serially correlated, this effect persists over time. By contrast, policy in presidential
and majoritarian countries is not affected by the income shock; in presidential countries
spending even appears to be pro-cyclical. Moreover, persistence in the size of government is
significantly smaller, particularly in presidential regimes. This pattern of reactions to income
shocks is consistent with the observation that welfare state tends to be larger in proportional
cum parliamentary systems: the outlays of such entitlement programs are fixed in cash terms,
or perhaps even inversely related to income. But, as argued above, there are other plausible
reasons why government outlays might move more than in proportion to aggregate income in
proportional-parliamentary democracies but not elsewhere.
To gain a better understanding, column 4 disaggregates income shocks into positive
(YSH_POS) and negative (YSH_NEG). An asymmetry is apparent. Only negative income
shocks have a statistically significant effect on the spending ratio, and their estimated
coefficient is much larger in absolute value. This asymmetric effect suggests that a ratchet
effect might be in place. A negative income shock induces a lasting expansion in the size of
government, which is not undone when income grows above potential. But this effect is not
present in presidential or majoritarian countries, where a ratchet effect instead appears to be
associatedwith positiveincome shocks. This different ratchet effectacrossconstitutional types
is hard to explain just on the basis of the different size of entitlement programs. It is instead
in line with the idea that presidential countries are more likely to face borrowing constraints:
when positive income shock occurs, they are able to expand aggregate spending more than in
proportion to income; but when hit by a recession, they are forcedtoenact sharpspending cuts.
If correct, this interpretation would lead to the further question of why presidential regimes
would be more likely to be credit rationed, or more generally why they would be more risky
borrowers. Whatever the interpretation of this ratchet effect, it could contribute to account for
the differential growth of government in different political systems that we uncovered in the
previous subsections. Thus, the possibility and precise explanation of an institution-dependent
ratchet effects certainly deserve more attention in future research.
Finally, in columns 5 and 6 we turn to other estimation methods. The results on the
income shocks stand, but the coefficient on lagged spending drops and differences across
institutions disappear. This last finding is important, as this coefficient could be biased in the
level-specification due to the panel structure of the data. Note also that these results are robust
across samples of countries. In particular, the same pattern of reactions to income shocks are
observed in our broad and narrow samples of democracies.12
Observable economic events and the budget surplus
As the budget surplus is defined as the difference between revenues and spending, it is
natural to ask how the same observable events manifest themselves in the budget surplus. To
do that, we use a specification consistent with the earlier regressions for central government
revenues and spending. As those include lagged revenues and spending, respectively, we
include the same variables in the surplus regression (but do not constrain their respective
coefficients to sum to zero). Since the surplus is also closely related to changes in government
debt, stationarityofthedebttoGDPratiorequires thatthesurplus alsoreacts totheoutstanding
stock of debt. We thus include lagged debt in the regression (including it in the spending and
We have assumed that the coefficients on LAG_SIZE and YSHOCK are the same within country groups,
but different across groups with different political institutions. A more general approach would be to allow
coefficients to differ across all countries, while looking for differences across countries belonging to different
groups. We have also tried the latter approach, by estimating the regressions in Table 6 by the method of random
coeffcients. The (mean) coefficients on LAG_SIZE in the group of presidential regimes is about 0.2 higher than
in the group of parliamentary regimes in consistency with the pooled regressions (both coefficients are precisely
estimated, although lower than in the pooled regressions). Similarly, the estimated coefficient on YSHOCK is
negative in the parliamentary group, wheras it is positive in the presidential group (although both have a high
revenues regressions above does not change the previous results). We allow the coefficients
on lagged debt, as well as on lagged spending and revenues, to differ for countries ruled by
different institutions, but for the rest, the specification is the same as in Table 6.
As in the previous subsections, we estimate the regressions in levels and in differences.
In the first case, we always include country fixed effects and estimate by SUR, jointly with the
spending and revenues regressions (the results are similar if we estimate the surplus regression
in isolation). When estimating in differences, we rely on IV estimation, as in the previous
subsection. But here, we exploit the fact that the surplus is approximately equal to the change
in debt (with reverse sign). We thus run a regression of the surplus (in levels) on the lagged
surplus and on all the other right hand side variables in first differences, omitting lagged debt.
The instruments are the levels of spending, revenues and surplus, all lagged twice, as well as
the other right hand side variables in differences lagged once.13
Table 7 shows the results. Consider the first three columns, estimated in levels. As
expected, we find that surpluses (as a percent of GDP) are procyclical – they go up with
positive income shocks – in the average country. But presidential regimes are different, with
acyclical or even countercyclical surpluses. Majoritarian elections seem to have a similar
effect, albeitnotstatisticallysignificant. Theorderofmagnitudeoftheseestimatedcoefficients
is in line with those estimated in Table 6 with regard to revenues and spending. These results
are also stable across the samples of democracies, except that the presidential effect becomes
even stronger in the narrow sample. The fourth column disaggregates the income shocks into
positive and negative shocks. As in the case of spending, there is some evidence of a ratchet
effect: negative income shocks reduce the surplus while positive shocks have no effect. But
now the differences across institutions are not statistically significant.
Write the level specification for the surplus as:
zit= αi+ γiτit−1− βigit−1+ λibit−1+ δxit+ uit,
where z denotes the surplus, τ revenue, g spending and b public debt, all in percentage of GDP, while x denotes
the vector of observable shocks. Taking differences (∆) and noting that zit−1≈ −∆bit−1, we can rewrite the
surplus regression as:
zit= γi∆τit−1− βi∆git−1+ (1 − λi)zit−1+ δ∆xit+ ∆uit.
The first three rows of the table show the reaction of the surplus to lagged debt. As
expected, the surplus is higher when the debt is larger. But this does not happen in the
presidential regimes (except in the narrow sample, where all regimes appear similar). Though
not reported in the Table, we also find that the surplus reacts to lagged spending and revenues.
As already found in Table 6, the coefficients on lagged spending and revenues is smaller (in
absolute value) in the PRES countries. Thus, the regime type appears to influence not only the
reaction of the surplus to income shocks, but also its dynamics.
Finally, the last two columns of Table 7 report the IV estimates of the specification
in differences. This estimation method leads to very unstable estimates, except for the
estimated coefficient on lagged deficit which has most of the explanatory power (the estimated
coefficient on lagged deficit is much larger than that on lagged debt, as it ought to be, because
of the variable transformation – see the expressions in Footnote 10). Deficits in presidential
regimes appear to have much less inertia (more mean reversion) than inparliamentaryregimes.
Majoritarian elections modify the dynamics in a similar way, but, again, not as strongly.
These results are consistent with the different dynamic response of deficits to debt in the
levels regressions. Although evidence remains of a different reaction to income shocks in
presidential regimes, the coefficient for the reference countries is almost zero. Moreover, the
estimated coefficients on the income shocks are now quite unstable across specification and
lists of instruments, a sign that these IV estimates are less reliable.
We next ask whether there is an electoral cycle in spending or revenue, whether it occurs
before or after the elections, and whether its magnitude depends on institutions. As explained
in Section 4, we essentially rely on the same specification as that underlying Table 6, except
that we expand sitwith indicator variables for current and lagged elections. We also drop the
price of oil from the specification, and include instead a set of year dummies, so as to identify
the effect of elections more precisely. PRES and MAJ are still interacted with the lagged
dependent variable and with YSHOCK, as in Table 6. In the levels specifications, we estimate
the spending and revenues equations jointly by SUR.
Table 8 reports the results for different samples and different estimation methods. The
first six columns rely on the basic specification where ELtincludes only the election year. As
this measure does not distinguish between elections held early and late in the year, we have
also used an alternative measure where ELtis redefined as taking a value of 1 if there was an
election in either year t or in year t+1. That is, a pre-election cycle is defined by fiscal policy
in the year before the election as well as in the year of the election. Our estimates in the last
two columns of the table rely on this alternative definition.
We find a strong electoral cycle in spending and taxation, but it takes a very different
form in presidential and parliamentary democracies.14Consider presidential regimes first.
There is strong evidence that they postpone fiscal adjustments until after the election. Once the
election is over, spending is cut by almost 1 percent of GDP and revenues hiked by at least 0.5
percent of GDP. Whether presidential regimes have a pre-election cycle is more ambiguous
and sensitive to our definition of the election dummy. According to columns 1-6, nothing
of statistical significance happens during the election year. But estimates based on the more
comprehensive definition of ELtin the last two columns suggest a tax break of about 0.7
percent of GDP before the election.
In parliamentary regimes, on the other hand, we only find a pre-election cycle, and only
on the revenue side. Revenues are cut by about 0.3 percent before elections, while government
spending does not seem affected by the election date.
We also investigated the specific prediction of the theory in Section 2, that majoritarian
electoral rules are associated with stronger electoral cycles (results not reported). While
the coefficient on ELttypically turns out to be larger (in absolute value) in parliamentary
countries with plurality elections than in those with proportional elections, the difference is
only statistically significant in a few specifications.
Finally, we look for evidence of electoral cycles in the budget surplus. As Table 9 shows,
we find a post-election cycle: improvements in the surplus on the order of 0.5-1 percent
points of GDP are postponed until the year after the election. Again, this electoral cycle is
present onlyinpresidential regimes, consistently withour results for government spending and
revenue. This cycle is statistically significant only in the estimation in differences, however,
and appears more pronounced in the broad sample of democracies. There is no evidence of a
Earlier studiesoninternationaldataconductedwith differentmethodologies hadtypicallynotfound robust
evidence of an electoral cycle (see Alesina, Roubini and Cohen, 1997 for a summary). An exception is the recent
study by Shi and Svensson (2000), who use panel data for over 100 countries and find significant electoral cycles
in spending, revenues and government deficits. But they only search for pre-election cycles and do not explore
institutional differences across countries.
pre-election deficit cycle in parliamentary regimes. Neither is there any systematic influence
of the electoral rule in these regimes (results not shown in the Table). As a final check on
the robustness we also used the more comprehensive definition of the pre-election cycle. The
results (not reported) do not change much, except that the evidence of a post-election cycle in
the budget surplus for presidential regimes becomes even stronger.
To understand why presidential regimes display systematic cycles in all fiscal aggregates
before and after elections, while parliamentary regimes mainly have a pre-election revenue
cycle, is an interesting issue for further theoretical research. Future research ought to pay more
attention to one issue in particular. While in presidential regimes elections of the president
tend to be exogenous, in many parliamentary regimes they are endogenous; in our sample,
elections are also somewhat more frequent in parliamentary than in presidential regimes. In
our estimates we ignore this potentially important difference across groups of countries.
5.2 Composition of spending
We now turn to the composition of government. Recall that our two measures of
composition include central government spending on social security and welfare, either as
a percent of GDP (SSW/GDP), or as a ratio to central government spending on goods and
services (SSW/GDS). We have already noted that different groups of countries have very
different welfare states: the large welfare states are a feature of proportionalcum parliamentary
systems. But do these differences remain after controlling for other social and economic
features of these countries? And does social security and welfare spending react to income
shocks and to election dates? As the methodological considerations closely follow those in the
previous subsection, we keep the discussion of our results more brief.
We start with cross-sectional tests for a direct effect of institutions. Estimation results
are shown in Table 10 for both our measures of composition. Note that data availability
restricts the full sample to the period from 1972. The results indicate that broad, non-targeted
programs are indeed systematically smaller under majoritarian elections, as predicted by the
theory discussed in Section 2. Ceteris paribus, social security and welfare spending is smaller
by 1-2 percentage points, when measured as a percentage of GDP, and about 0.20-0.40 points
lower, when measured as a ratio to spending on goods and services (in this latter case, the
dependent variable takes values close to 1 on average). Statistically, these results are more
fragile to the sample and the inclusion of socio-economic controls than were the results for
overall spending. Qualitatively, they are in line with the findings of Milesi-Ferretti et al (2000)
for the OECD countries.
Unlike for the size of government, however, we find no discernible effect of the regime
type on our measures of composition after controlling for our usual observable variables. On
average, presidential regimes have much smaller welfare states than parliamentary countries.
But this appears to be due to a different demographic composition and to other economic
features, not to the political institution per se, at least when we neglect the time variation in
Unobservable common events
What about the indirect effects of institutions?Results from our estimates of the
adjustment to common unobservable events are collected in Table 11. As in the case of
overall spending, we find a strong and significant influence of political institutions. Now both
the electoral rule and the regime type matter. Unobservable common events have a smaller
effect on the spending ratio (SSW/GDS) under majoritarian elections and under presidential
regimes. When social security and welfare is measured as a share of GDP, the estimated effect
of presidential regimes is particularly relevant, with a cumulative difference of about 5 percent
of GDP. As the estimated effects of the common events (the time sequence of βqt) grow
throughout the entire course of the sample, the last result can be interpreted as evidence of
more rapid growth of welfare-state spending in parliamentary than in presidential regimes.
Finally, note that the influence of political institutions appears weaker in the broader sample
of democracies. A likely reason is that this broad sample includes a number of developing
countries, where the welfare state is too small to be meaningfully compared to the larger
welfare states in the OECD.
Observable economic events
Table 12 summarizes our results regarding the adjustment to income shocks. Here
we only report results on social security and welfare as a share of GDP, as the results for
SSW/GDS are less robust. The estimated coefficients resemble the pattern we obtained in
Table 6 for the overall size of government. Presidential and majoritarian systems have a
dampened reaction to income shocks, and less persistence, compared to parliamentary and
proportional systems. The result on persistence is less robust across estimation methods,
however, as already found in Table 6. Moreover, comparing these estimates with those in
Table 6, income shocks have a smaller impact on this component of the budget than on the
overall budget size. This suggests that automatic stabilizers due to the larger welfare states of
proportional-parliamentary countries cannot fully explain the different cyclical reaction of the
size of government and the budget surplus, noted in the previous subsection.
Do we find a systematic effect of elections on the composition of spending? The answer
is positive, but with some important differences relative to our findings on the overall size
15As Table 13 shows, the post-election cycle in presidential regimes can be
detectedinonlysomespecifications andestimationmethods. Ontheotherhand, parliamentary
regimes now display a statistically significant pre-election cycle in this component of spending
(about 0.2 percent of GDP), which continues in the post-election year.But this hike in
social security spending is present only under proportional elections. Although the estimates
are not entirely stable across samples and estimation methods, our results suggest quite a
subtle pattern. In presidential regimes, spending on social security falls after the elections,
as painful adjustments seem to be delayed. In parliamentary regimes, on the other hand,
program expansions seem to take place during election years, although only in countries
with proportional elections. In proportional parliamentary regimes favors granted during the
electoral campaign are sustained after the elections.
We find these results intriguing: without taking explicit account of electoral rules and
reliance on social-security spending around election time in parliamentary and proportional
systems is perhaps plausible if – as in the theory discussed in Section 2 – politicians indeed
have greater overall incentives to use broad programs for seeking electoral support in those
systems. But it remains to work out the details – and auxiliary predictions – of such a theory.
Do political institutions shape economic policy? Our empirical results, summarized
in Table 14, strongly suggest that the answer is yes. Several of these empirical regularities
When estimating by SUR, the SSW/GDP equation is jointly estimated with the corresponding equation
on the size of government.
are in line with the first wave of theory discussed in Section 2. In particular, as predicted,
presidential regimes have smaller governments, while majoritarian elections lead to smaller
But other findings still await a satisfactory theoretical explanation. A puzzling but
robust feature of the data is that the cyclical response of aggregate spending and budget
deficits is much smaller in presidential regimes and under majoritarian elections, compared to
proportional-parliamentary systems. Larger welfare programs in proportional-parliamentary
systems inducing a larger automatic reaction of government outlays to cyclical fluctuations
could partly account for this finding. But this is unlikely to be the whole story.In
particular, different political constitutions seem to be associated with different ratchet effects
in government spending.
Another puzzling but robust finding concerns electoral cycles. Fiscal adjustment is
delayed until after the election, but only in presidential regimes. And social transfers tend
to grow around the election date, but only in proportional cum parliamentary systems. Why do
we observe these different patterns in countries ruled by different institutions?
These are promising first steps in a research program, but much work remains to be
done. One direction is to refine the theory of policy. To understand the cyclical reaction of
fiscal policy, or why fiscal adjustments are delayed, we need dynamic models. This theory
does not yet exist, as the existing predictions of comparative politics and economic policy
are generally drawn from static models, in which there is no role for state variables such as
government debt, or no link between current policy decisions and the future status quo.
On the policy side, we have concentrated on government spending. It would be
interesting, and certainly feasible, to study other policy instruments — such as the structure of
taxation, including trade policy — with similar methods. On the institutional side, one should
study the effect on policy of more detailed constitutional features; for instance, different types
of checks and balances, or different types of confidence requirements.
This suggests another direction of research, namely refined measurement of political
institutions. In some cases, such measurement will involve a mere, but time-consuming,
compilation of data from existing sources. One example would be to collect panel data for
continuous measures ofthetwo aspects of the electoral rulediscussed in Section 2: district size
and the electoral formula. In other cases, better measures will require the collection of new
primary data. An example would be to try and find continuous or multidimensional measures
of checks and balances in different political regimes.16As this may be a labor-intensive and
open-ended task, it is important to use theory as a guide.
Some econometric issues certainly need to be explored in more detail. Even with refined
measurement, considerable measurement error will remain in our data. Sharper theory would
help trade off the prospective biases due to measurement and specification errors. Sharper
hypotheses, derived from dynamic models, would also help avoid the pitfalls of estimation in
All in all, a close interplay of theory, measurement and statistical work appears essential
for making progress on the broad questions dealt with in this paper. The empirical findings
described in this paper suggest that it is worth trying.
Attempts to construct such measures have been made by Beck et al (1999) and Shugart and Carey (1992).
CENTRAL: Degree of centralization of spending, measured as the ratio between central and
general government expenditure. Source: GFS and IFS, International Monetary Fund.
CGEXP: Central Government Expenditure (as a percentage of GDP) Source: IFS, International
CGREV: Central Government Revenue (as a percentage of GDP) Source: IFS, International
COLONIAL ORIGIN: Three dummy variables, COLO_UK, COLO_ES, and COLO_OTH,
for countries with colonial origins in the UK, Spain or Portugal, and other colonizers,
respectively. Source: CIA World Factbook 1998.
CONTINENTS: Four dummy variables, ASIA, AFRICA, LAAM, OECD, for different
continents or levels of development. Source: Persson and Tabellini (1999).
DEBT: Total government debt (both domestic and foreign) as a percentage of GDP. Source: IFS,
International Monetary Fund.
ELECTION: Takes value of 1 when the parliamentary/presidential election is held, 0
otherwise. When the country is considered as parliamentary we use legislative elections,
otherwise presidential elections. For elections of the legislature, only elections for the lower
or single house are considered. Partial elections that cover at least 1/3 of the total seats
available are recorded as 1. For presidential regimes, only first round elections for president
are considered. Sources: International Institute for Democracy and Electoral Assistance
(2000) and Inter Parliamentary Union (Chronicle of Parliamentary Elections, various issues).
Political Handbook of the World, different volumes (from 1960 to 1996) Banks (Ed.) and
Muller (Ed.); Mackie and Rose “The International Almanac of Electoral History” Mc Millan.
GASTIL: Average of Gastil index for civil liberties and political rights. Source: Freedom
House, various years.
GGEXP: General Government Expenditure (as a percentage of GDP) Source: GFS,
International Monetary Fund.
LYH: Real GDP Per Capita in constant dollars (international prices, base year 1985),
expressed in logs. Source: Penn World Table 5.6. Missing data calculated from 1985 GDP
per capita and GDP per capita growth rates (Global Development Finance & World
MAJ: Dummy variable taking value 1 if the country's electoral system in that year utilizes a
majority or plurality rule for legislative elections, 0 otherwise. Source: Inter Parliamentary
Union, various years.
OIL: Oil Price (Market Price-Petroleum, Spot US $/Barrel) avg. crude price not seasonally
adjusted. Source: IMF, International Financial Statistics.
PRES: Dummy variable taking a value of 1 for presidential regimes. Sources: Shugart., M.
and J. Carey (1992), “Presidents and Assemblies”, Cambridge University Press (in particular
fig 8.2); Cox, G., (1997) “Making Votes Count”, Cambridge University Press (appendix C);
Delury, G. (Ed.) (1983), World Encyclopedia of Political Systems.
PROP1564: Share of total population between 15 and 64 years of age. Source: World Saving
Database, World Bank.
PROP65: Share of population older than 65. Source: World Saving Database, World Bank.
SSW/GDP: Central Government Expenditures on social security and welfare (as a percentage of
GDP) Source: GFS, International Monetary Fund.
SSW/GDS: Central Government Expenditures on social security and welfare (as a percentage of
GDP) divided by Central Government Current Expenditure on goods and services (as a percentage
of GDP) Source GFS, International Monetary Fund.
SURPLUS: Overall surplus (as a percentage of GDP) Source: IFS, International Monetary Fund.
TRADE: Total trade (imports +exports) (as a percentage of GDP). Source: Global
Development Finance & World Development Indicators.
YSHOCK: Log deviation of real GDP from its HP filtered trend. Real GDP is measured in
constant dollars (international prices, base year 1985). Source: Penn World Tables.
YTREND: HP-filtered trend value of real GDP (see YSHOCK).
Summary of Theory
PRES (vs. PARL)MAJ (vs. PR)
− − − −
− − − − /?
− − − −− − − −
Reaction to shock
Sample of Countries
(Table 2 segue)
PAPUA N.GUIN1960-86 1960-9810
Narrow refers to countries with a Gastil index of political right less than 2. Default refers to countries with a Gastil
index of political right less than 4. Broad refers to countries with a Gastil index of political right less than 5.
SURPLUSSSW/GDSLYHTRADE PROP1564 PROP65CENTRALPRES
0.04- 0.56- 0.73
0.27- 0.13 0.07- 0.07
- 0.020.720.76 - 0.61 0.17
- 0.110.820.80 - 0.71 - 0.040.82
0.09- 0.28 - 0.480.58 - 0.36 - 0.56- 0.50 0.12
0.23 - 0.27- 0.12- 0.02 0.23- 0.06- 0.22 0.04 -0.24
Pooled Yearly Data
CGEXPSURPLUSSSW_GDS GROWTHLYH GASTILTRADEPROP1564PROP65
SSW/GDS0.47 - 0.08
GROWTH- 0.15 0.15- 0.18
LYH 0.49 0.010.65 - 0.11
GASTIL- 0.460.08 - 0.470.14 - 0.59
TRADE0.320.13- 0.130.10 0.13- 0.03
PROP1564 0.44- 0.010.60 - 0.12 0.76- 0.480.19
PROP65 0.56- 0.08 0.79 - 0.160.79- 0.590.020.78
PRES - 0.490.07 - 0.21- 0.05 - 0.450.46- 0.35 - 0.47- 0.47
MAJ- 0.05 0.12- 0.28 0.05- 0.040 0.16 - 0.02- 0.17- 0.26
Size of Government
Broad refers to the less restrictive definition of a democracy (see text). p-values in brackets. Boldface fonts denote significance at the 10% level. X1 includes the variables TRADE, LYH,
PROP1564, PROP65 (see the text and Data Appendix). Cont. and Col. refer to two sets of dummies for continents and colonial origin, respectively (see the Data Appendix).
Size of Government
Unobservable Common Events 1960-1998
Yearly Yearly Yearly Yearly
β ∗(qT - q1)∗
- 12.73 - 13.46 - 11.09- 9.05 - 7.17- 6.60
β ∗(qT - q1)∗
- 2.99 - 5.84- 6.24 - 2.90- 2.37 - 3.09
Broad refers to the less restrictive definition of a democracy (see text). p-values in brackets. Boldface fonts denote significance at the 10% level. X1 includes the variables TRADE, LYH, PROP156
(see the text and Data Appendix). All the equations include a set of country dummies.
Size of Central Government
Observable Economic Events 1960-1998
p-values in brackets. Boldface fonts denote significance at the 10% level. P and M denote interaction with the PRES and
MAJ dummies, respectively. X2 includes the variables in X1 (namely TRADE, LYH, PROP1564, PROP65), plus OIL and
the trend corresponding to YSHOCK (see text and Data Appendix). R2 in the fixed-effects regressions refers to the within
Surplus of Government
Observable Economic Events 1960-1998
Estimation FE, SUR
Broad and Narrow refer to less and more restrictive definitions of a democracy (see text). p-values in brackets.
Boldface fonts denote significance at the 10% level. SUR estimated jointly with CGEXP and CGREV. P and M denote
interaction with the PRES and MAJ dummies, respectively . X3 includes the variables in X2 (namely TRADE, LYH,
PROP1564, PROP65, OIL, the trend corresponding to YSHOCK) plus lagged size of spending and revenues by central
government. These two variables are interacted with PRES and MAJ in columns 1-4, but not in the last two columns.
R2 in the fixed-effects regressions refers to the within estimator.
* In the last two columns, the variable (change in) lagged DEBT is replaced by the lagged deficit (in levels) – see the
footnote in subsection 5.1.
Size of Government
Electoral Cycles 1960-1995
Dep. VariableCentral SpendingCentral Revenue
Broad refers to the less restrictive definition of a democracy (see Table 2). p-values in brackets. Boldface fonts denote significance at the 10% level. ELt and ELt-1
are dummy variables for the election and post-election years, respectively. X4 includes the variables in X2 minus OIL and all the variables (including the
interaction terms) in column 1 of Table 6, plus a set of year dummies; X5 is constructed as X4 but with lagged central revenue taking the place of lagged central
spending (see the text and Appendix). Note that ELt in the last two columns is defined as to take a value of 1 not only in the election year but also in the year before.
Surplus of Government
Electoral Cycles 1960-1995
Broad and Narrow refer to the less and more restrictive definitions of a democracy (see text). p-values in brackets. Boldface fonts denote significance at the 10% level.
ELt and ELt-1 are dummy variables for the election and post-election years, respectively. SUR estimated together with CGEXP and CGREV. X6 includes the variables
in X2 except OIL plus all the variables (including the interaction terms) in Column 1 of Table 7 plus a set of yearly dummies; X7 is identical to X6 except that the
lagged surplus is not included (see the text). R2 in the fixed-effects regressions refers to the within estimator.
Composition of Government
Cross Sections 1972-1998
Dep. VariableSSW/GDP SSW/GDS
PRES - 0.70
Broad refers to the less restrictive definition of a democracy (see text). p-values in brackets. Boldface fonts denote significance at the 10% level. X1 includes
the variables TRADE, LYH, PROP1564, PROP 65 (see the text and Data Appendix). Cont. and Col. refer to two sets of dummies for continents and colonial
origin, respectively (see the Data Appendix).
Table 11 Download full-text
Composition of Government
Unobservable Common Events 1972-1998
Dep. variable SSW/GDPSSW/GDS
SamplingYearly Yearly Yearly
- 4.70- 4.92 - 4.04 - 0.13- 0.07
- 1.04 - 0.70 - 0.14- 0.20- 0.08
Broad refers to the less restrictive definition of a democracy (see text). p-values in brackets. Boldface fonts denote significance at the 10% level. X1 includes the
variables TRADE, LYH, PROP1564, PROP 65 (see the text and Appendix). All the equations include a set of country dummies.