Do Fiscal Rules Dampen the Political Business Cycle?

Do Fiscal Rules Dampen the Political Business Cycle?Author(s): Shanna RoseSource: Public Choice, Vol. 128, No. 3/4 (Sep., 2006), pp. 407-431Published by: SpringerStable URL: http://www.jstor.org/stable/25487566 .

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Public Choice (2006) 128: 407-431 DOI: 10.1007/sl 1127-005-9007-7 ? Springer 2006

Do fiscal rules dampen the political business cycle?

SHANNA ROSE Robert E Wagner School of Public Service, New York University, New York, NY 10012-9604, U.S.A.;

E-mail: [email protected]

Accepted 1 November 2005

Abstract. This paper develops and tests the theory that fiscal rules limit politicians' ability to manipulate the budget for electoral gain. Using panel data from the American states, I

find evidence suggesting that stringent balanced budget rules dampen the political business

cycle. That is, while spending rises before and falls after elections in states that can carry

deficits into the next fiscal year, this pattern does not exist in states with strict "no-carry" rules.

Neither binding gubernatorial term limits nor the partisan composition of government appear

to significantly affect the magnitude of the political business cycle.

1. Introduction

Political business cycle theory suggests that reelection-minded incumbents

temporarily increase spending in election years and defer the tax increases

needed to pay for new spending to non-election years. It follows that deficits

should rise before elections and fall after elections. A large empirical literature

finds such cycles in virtually every region of the world, from Northern America

to sub-Saharan Africa to the transition economies of Eastern Europe.1 This theory assumes that politicians can run deficits. However, many gov

ernments have fiscal rules that limit or prohibit deficits. To the extent that such

rules are effective, they should curb politicians' ability to manipulate fiscal

policy for electoral gain. The existing literature on fiscal rules focuses on their

average effectiveness in enforcing discipline; it has not explored their impact on fluctuations in spending, taxes, or deficits over the electoral cycle.

The American states constitute an excellent laboratory in which to test

the hypothesis that fiscal rules dampen the political business cycle. Approx

imately half of the states have stringent balanced budget rules that prohibit

"carry-over" of deficits into the next fiscal year. These rules are largely a

product of historical accident - nearly all were included in the original state

constitutions, or were adopted shortly after statehood - reducing concerns

about institutional endogeneity. And unlike cross-sections of countries, the states are characterized by a broadly common political and constitutional

setting.

Using panel data from the American states between 1974 and 1999,1 find

evidence of political business cycles in deficits and spending, but not taxes.



408

When I control for the stringency of balanced budget rules, I find that, as

predicted, political business cycles are negligible in states with prohibitions on deficit carry-over. However, this result only holds for states that restrict

the government's ability to close budget gaps with borrowed funds. No-carry rules unaccompanied by borrowing restrictions do not appear to diminish

the political business cycle. Finally, I find that neither binding gubernatorial term limits nor the partisan composition of government significantly affect

the magnitude of the political business cycle.

2. The Political Business Cycle2

The political business cycle theory was first developed by Nordhaus (1975), who showed that if reelection-minded politicians can exploit the trade-off

between inflation and unemployment known as the Phillips curve, and if

voters base their decisions on recent economic performance, incumbents will

find it optimal to expand the economy prior to elections. This result depends

critically on the assumption that voters reward this behavior despite the fact

that, after each election, output and employment return to their natural rates

but inflation is higher.

Shortly after Nordhaus's article was published, Robert Lucas (1976) fa

mously argued that economic actors form rational expectations by optimally

using all available information-including knowledge of the effects of past economic policies-to forecast the future. In response to the Lucas critique, several authors (most notably Rogoff & Sibert, 1988; Rogoff, 1990) modified

Nordhaus's model in two ways.

First, these newer models substitute an assumption of asymmetric infor

mation for voter irrationality. Specifically, they assume that voters do not have

full information about incumbents' competence. Thus, incumbents engage in

pre-election manipulations not to take advantage of voters' irrationality, but

to try to appear as competent as possible.

Second, these newer models focus on "political budget cycles" rather than

cycles in real variables such as inflation, output, or unemployment. Rogoff

(1990) points out that if voters form rational expectations, pre-election policy

manipulations should not have any real macroeconomic effects since elections

are perfectly anticipated events.3 For this reason, the recent literature has

focused on electoral cycles in public spending, taxes, and deficits.

2.1. Empirical evidence of political business cycles

The earliest empirical studies of political budget cycles look at U.S. federal

spending, and particularly transfers - arguably one of the most visible ways

to increase voters' disposable income (Alesina, 1988). Keech and Pak (1989) find that, between 1961 and 1978, veteran's benefits were higher in election



409

years than in non-election years. Alesina, Roubini and Cohen (1992) find

an electoral cycle in the ratio of net transfers to GNP between 1961 and

1985.

There is also a sizeable literature on political business cycles among cross

sections of countries. Schuknecht (1996) finds that, in a sample of 35 develop

ing countries between 1970 and 1992, budget deficits were larger in election

years. Alesina, Roubini and Cohen (1997) arrive at similar results for a sam

ple of 13 OECD countries between 1960 and 1993. Block (2002) studies a cross-section of 44 sub-Saharan African countries, and finds electoral cycles in both expenditures and budget deficits.

More recently, the literature has begun to investigate how these cycles vary in different institutional contexts (see Franzese, 2002, for a review). Brender

and Drazen (2004) argue that fiscal manipulation should be more effective - and thus electoral cycles should be stronger

- in new democracies, where

voters are relatively inexperienced with electoral politics, than in advanced

democracies. In a sample of 68 democratic countries between 1960 and 2001, the authors find political budget cycles in the deficits of new but not established

democracies. Persson and Tabellini (2002) and Shi and Svensson (2002) find

similar results.

According to Alt and Lassen (2004), one reason political budget cycles

might be more pronounced in new democracies is that they tend to be char

acterized by less fiscal transparency. As fiscal transparency increases, the

information asymmetry arguably declines and voters are better able to dis

tinguish manipulation from competence. Indeed, Alt and Lassen find that,

among OECD countries during the 1990s, electoral cycles in budget deficits

were stronger in countries characterized by less fiscal transparency.

Despite this growing interest in how political business cycles vary in differ

ent contexts, the literature has inexplicably overlooked the American states, which are characterized by a wealth of institutional heterogeneity and yet are

otherwise more similar than cross-sections of countries.4 Of the few studies of

political business cycles in the American states, only one, to my knowledge, considers the institutional context in which they take place. Besley and Case

(1995b) investigate whether cycles are weaker under term-limited governors, who arguably have less incentive to manipulate fiscal policy; however, the

authors find little evidence of political business cycles, regardless of whether

the governor is a lame duck.5

One potentially relevant source of institutional variation in the American states relates to fiscal rules. To the extent that balanced budget require

ments are effective, they should constrain politicians' ability to manipulate

intertemporal patterns of spending and taxes for electoral gain. Before fully developing this hypothesis in Section 4, I first provide an overview of bal

anced budget rules in the American states and review the related empirical literature.



410

3. Fiscal Rules in the American States

Forty-nine of the 50 states have some type of balanced budget requirement; Vermont is the exception. These rules are largely a product of historical acci

dent; most were included in the original state constitutions, or were adopted

shortly thereafter as state laws.6

Fiscal rules in the American states can be grouped into two broad cate

gories. The first type of rule, which currently applies in twenty-two states,

imposes "prospective" restrictions on the budget at the beginning of the fiscal

period rather than "retrospective" restrictions on actual balances at the end

of the period.7 In some of these states, the governor must submit a balanced

budget to the legislature, while in others the legislature must pass a balanced

budget. Either way, these states are permitted to run unanticipated deficits that

materialize during the fiscal period. The second type of rule is more stringent; it combines a prospective rule

with a retrospective rule prohibiting the government from "carrying over"

a deficit into the next fiscal year. Twenty-seven states currently have such

rules. In these states, any deficits that emerge during the fiscal period must

be eliminated through real adjustments (spending cuts or revenue increases),

accounting adjustments, or (in some states) borrowing. The use of accounting

adjustments or "gimmicks"-such as temporarily transferring money from spe cial earmarked funds into the general fund-is quite common, but appears to ac

count for only a small portion of deficit elimination (U.S. General Accounting Office, 1993). The ability to close revenue shortfalls with borrowed funds

varies from state to state. In some states, the governor, the legislature, or a

state official such as the treasurer is authorized to issue debt. Other states

prohibit the government from issuing debt or require a public referendum for

debt authorization (National Association of State Treasurers, 2001).

3.1. Empirical evidence of the effects of fiscal rules

The empirical literature on fiscal rules in the American states focuses primarily on the question of their average effectiveness in enforcing discipline.8 The first

such study was conducted by the Advisory Commission on Intergovernmental Relations (1987). The authors compile an index of the stringency of balanced

budget requirements, with no-carry rules receiving the maximum score. Using cross-section data from 1984, they find that states with more stringent rules had

lower deficits in that year. However, Von Hagen (1991) repeats this exercise

using panel data between 1975 and 1985, and finds no relationship between

balanced budget rule stringency and the size of deficits.

Rather than using an index, Bohn and Inman (1996) regress separate

dummy variables for each type of balanced budget rule on the general fund

surplus. They find that, controlling for state economic and political conditions,



411

no-carry rules are associated with significantly larger surpluses than are other

types of rules.

Several authors consider how balanced budget rules affect government

responses to revenue shortfalls. Poterba (1994) finds that, between 1988 and

1992 in states with annual budget cycles, stringent balanced budget rules

(as measured by the ACIR index) were associated with more rapid fiscal

adjustment to unexpected deficits. In particular, a $100 deficit overrun led to a

$44 spending cut in states with no-carry rules, compared to a $17 cut in states

without rules. Alt and Lowry (1994) find that no-carry rules are associated with

more rapid adjustment to deficits when Republicans control both branches of

government, but do not appear to have an effect under Democratic control.

Taken together, the empirical literature on fiscal rules suggests that no-carry rules are substantially more effective in enforcing fiscal balance, on average, than other types of rules. However, tests of the average impact of balanced

budget rules on fiscal discipline do not reveal how they affect volatility in

spending, taxes, and deficits over the electoral cycle. The remainder of this

paper addresses this question.

4. Model

The following is an extension of the model developed by Rogoff and Sib

ert (1988) and adapted by Alesina, Roubini and Cohen (1997). Suppose the

government faces the following budget constraint:

Yt = rt+dt+st (4.1)

where ~g~t is an exogenously-given level of government spending, rt is a lump sum, non-distortionary tax, dt is the budget deficit, and et is the incumbent

politician's competence.9 Competence is defined as the ability to limit waste

in the budget process, so that a more competent politician is able to finance

the given level of spending with a smaller amount of revenue. Competence is

assumed to follow a moving average:

et = lit + /Jit-i (4.2)

where /x, [0, /x]. That is, competence is comprised of a contemporary com

ponent and the realization of competence in the preceding period. Intuitively,

competence could be said to vary over time because abilities well-suited to

dealing with one type of circumstance might become outdated as the problems

facing the government change (Rogoff, 1990). Elections are held at the end of period t. In period t, voters observe ~g~t and

rt but not dt or et. Voters observe the deficit with a one-period delay, that is,



412

in period t + 1. Thus, voters can also "back out" the incumbent's competence with a one-period delay.

Voters want to elect the politician who maximizes their expected utility:

U = E X>'M< <43>

where

ut = Tt -

xt -

dt -

A(dt) (4.4)

where Yt is an exogenously given level of income and A(dt) are the distor

tionary costs of deficits, which crowd out capital formation and thus reduce

consumption. The social optimum is to finance spending with taxes rather

than deficits.10

Rogoff and Sibert show that if politicians care about both reelection and

social welfare, then prior to the election, the incumbent chooses a positive amount of deficit spending for every realization of competence except /x, = 0.

That is, in an effort to appear as competent as possible, every type of politician runs a deficit before elections except the least competent type, who, given the

behavior of other types, finds it impossible to manipulate the budget enough to hide his incompetence. Note that incumbents engage in manipulations

immediately prior to the election because voters can observe the incumbent's

competence with a lag. Therefore incumbents do not find it optimal to run

deficits in non-election years.

Thus, the model predicts that the fiscal position will temporarily deteriorate

in election years. Since the deficit grows and spending is assumed to be

exogenous, it follows that taxes will temporarily decline in election years.

If, on the other hand, rt is treated as exogenous instead of gt, and voters'

welfare is assumed to increase in the level of government services provided, then the model predicts that spending will temporarily rise in election years.

Intuitively, a politician can appear more competent by reducing taxes for a

given level of spending or increasing spending for a given level of taxes (or some combination of the two).

Now consider how the equilibrium changes when we introduce a balanced

budget rule. A balanced budget rule, if binding, prevents the incumbent from

running a deficit, such that dt = 0. Thus, the budget constraint becomes:

gi = rt + et. (4.5)

Because voters can observe both ~g~t an(i Tt in period t, they can immediately back out the incumbent's competence et. Since the balanced budget rule re

quires that spending be financed entirely with taxes, the incumbent is unable



413

to signal his competence and thus no longer derives any electoral advantage from manipulating fiscal policy.

Thus, to the extent that a balanced budget rule is truly binding, in the sense

that spending must equal taxes, it should eliminate the political business cycle,

enabling voters to identify and reelect competent leaders without relying on

costly signals in the form of budget deficits. However, if the incumbent is able

to circumvent the balanced budget rule, for example by resorting to borrowing, then dt ^ 0 and the political business cycle persists.

Applying this model to the American states, three testable hypotheses

emerge:

Hypothesis 1: The American states are characterized by political business

cycles, whereby fiscal balance deteriorates in election years as a result of

tax cuts, spending increases, or both.

Hypothesis 2: States that are prohibited from carrying deficits into the next

fiscal year have weaker political business cycles than do states without such

rules.

Hypothesis 3: Among states with no-carry rules, political business cycles are

weaker where those rules are more difficult to circumvent by borrowing.

In the next section, I devise an empirical strategy to test these hypotheses.

5. Methodology

Consider the following regression model:

yit = ft Eit + yn Eit + kXit + af + S, + fiit (5.1)

where yit is a fiscal aggregate (surplus, tax revenues, or spending), Eit is a

vector of dummy variables representing the years in the election cycle, r, is a dummy variable for states with "no-carry" rules, Xit is a vector of control

variables representing state political and economic conditions, at are state

fixed effects, <$, are year effects, and /jiit is a disturbance term. I describe each

of these variables in greater detail below.

The dependent variable alternately measures the real per capita general fund surplus, real per capita general revenue from taxes, or real per capita

general expenditure. I follow Bohn and Inman (1996) in focusing on the

general fund - which is the principal source of state appropriations and, as a

rule, the fund directly constrained by balanced budget requirements- rather

than total fiscal aggregates. The general fund differs from the total budget in

that it excludes insurance trust funds, public employee retirement funds, and other special funds.11



414

The key explanatory variables relate to the electoral cycle. I focus on

gubernatorial rather than legislative elections for two reasons. First, guberna torial elections occur at four-rather than two-year intervals, offering greater

scope for studying political business cycles.12 Second, since governors and

legislators must agree on spending and tax legislation, cycles are likely to

be more detectible in gubernatorial election years, when both branches are

up for reelection, than in legislative election years, when only one branch is

on the ballot; indeed, this assertion turns out to be consistent with my re

sults. Thus, I include dummy variables for the gubernatorial election year, one year after, and two years after the election year; the omitted base cate

gory to which these coefficients are compared is the year prior to the election n

year.

To determine whether political business cycles differ in states with and

without stringent balanced budget requirements, I interact the electoral cycle variables with a dummy variable for states with no-carry rules.14 In some

specifications, I distinguish between states with "strict" and "weak" no-carry rules. I define strict no-carry rules as those that are difficult to circumvent

by borrowing, due to either a popular referendum requirement or prohibition on the issue of public debt. In states with weak no-carry rules, on the other

hand, the governor, the legislature, or a public official such as the treasurer is

authorized to issue public debt.15

I control for several state-level variables that are likely to affect state fiscal

policy. First, I control for government resources: the tax base (measured by real per capita state income) and real per capita grants from the federal govern

ment. Second, because economic downturns reduce tax revenues and increase

demand for need-based programs, I control for the unemployment rate. Fi

nally, I control for demographic variables-population size and the fraction

of the population that is school-aged (5-17) or elderly (over 65)-to capture demand for government services. Finally, I control for the partisan compo sition of government by including variables for unified Democratic control

and unified Republican control of both branches of government (the omitted

category is divided government).

5.1. Dynamic panel estimation16

The regression model in Equation (5.1) does not address the problem of per

sistence in the dependent variable. That is, fiscal aggregates within a state

tend to be highly correlated from one period to the next. One approach would

be to simply include a lagged dependent variable on the right-hand side to

capture persistence:

yit = 4>Xit + yytj-i + at +St + /iit (5.2)



415

where Xit is a vector consisting of the key independent variables and control

variables in Equation (5.1) (Eit, rt Eit , and Xit). However, it is well known

that panel data models with individual effects-whether fixed or random

generate biased estimates in the presence of a lagged dependent variable

(Nickell, 1981). I use the standard approach to dealing with this problem: the general

method of moments (GMM) estimator developed by Arellano and Bond

(1991). This method removes the individual effect by taking first-differences

of both sides of Equation (5.2):

yu -

yi,t-\ =

4>(Xu -

Xij-i) + viyu-x -

yu-i)

+ (St -

&t-\) + (M/7 ~

r^u-i)- (5.3)

Although the individual effect drops out, this method generates a new problem: correlation between ytj-i and /jlu-i. To remove this correlation, the lagged levels of the dependent variable from period t?2 and earlier (ytj _2, j/,/-3,...) are used as instrumental variables for the difference (ytj-i

? yi,t-i)- Arellano

and Bond show that these lagged levels are suitable instruments if the distur

bance term /j,it has mean zero and is not serially correlated, in which case the

first difference of the disturbance term (/iit ?

fitj-i) has zero covariance with

the levels of the dependent variables from period t ? 2 and earlier.17

5.2. Data

I use panel data from forty-three American states between 1974 and 1999.

Arkansas, New Hampshire, Rhode Island, and Vermont are omitted from the

sample because they had two-year gubernatorial election cycles during most

or all of the sample period.18 Tennessee is omitted because it adopted a no

carry rule during the sample period, Nebraska is omitted because it has a

nonpartisan legislature, and Alaska is omitted because it is a "fiscal outlier"

due to heavy reliance on severance taxes. Of the states in the sample, 23 have

no-carry rules and 20 do not.

Data on state finances, income, population, and unemployment come from

the Census Bureau. Where necessary, these data have been converted from

fiscal to calendar years. Data on the partisan composition of government were

provided by Jim Alt, and data on no-carry rules and borrowing requirements are from the Advisory Commission on Intergovernmental Relations and the

National Association of State Treasurers.

Figure 1 shows the geographical distribution of no-carry rules, and Table 1

provides summary statistics for states with and without no-carry rules. States with no-carry rules are located somewhat disproportionately in the Midwest

and South, have somewhat smaller populations and governments, and are more



416

Ca \ i ^ *?$?* \a No rule

rs. Weak rule

C\ Hi Strict rule

Figure 1. Geographical distribution of no-carry rules.

frequently governed by Republicans than are states without such rules. Among states with strict and weak no-carry rules, the most notable differences appear to be geographic and political; states with weak no-carry rules are located

in the south and west and tend to be more Democratic than states with strict

no-carry rules.

These dissimilarities are partly ameliorated by the Arellano-Bond proce

dure, which removes state effects from the regression by taking first differ

ences. Moreover, the key independent variables capture variation over the

electoral cycle-which is itself clearly exogenous-as opposed to average dif

ferences among states. Thus, dissimilarities will only bias my estimates if they cause states to be "differently different" over the electoral cycle. Nonetheless, it is important to rule out this possibility. I return to this issue in the next

section.

6. Results

Tables 2, 3, and 4 report the results of regressions in which the dependent variable is the per capita general fund surplus, per capita tax revenue, and

per capita expenditure, respectively. All three tables report the coefficients

on the key independent variables: the years in the electoral cycle and, in

some cases, their interactions with no-carry rules. The control variables in all

regressions are the lagged dependent variable, real per capita state income, real per capita federal grants, the unemployment rate, population size, percent



I Table 1. Summary statistics

i

I States with

All states States without rules States with rules States with strict rules weak rules Standard Standard Standard Standard Standard Mean deviation Mean deviation Mean deviation Mean deviation Mean deviation

Surplus (per capita) 142 216 172 274 117 144 126 153 89 109

Taxes (per capita) 2,367 585 2,630 610 2,139 452 2,215 458 1,925 357

Expenditure (per capita) 4,057 913 4,442 955 3,722 724 3,789 731 3,531 671

| State income (per capita) 23,040 4,143 24,610 4,149 21,676 3,625 22,228 3,592 20,112 3,249

i Federal grants (per capita) 828 227 897 263 769 168 772 174 760 151

\ Unemployment rate 6.3 2.1 6.2 1.9 6.4 2.2 6.4 2.4 6.4 1.8

] Population (millions) 5.4 5.4 6.1 6.9 4.7 3.5 4.8 3.3 4.5 3.9

I Percent aged 5-17 20.2 2.5 20.0 2.3 20.5 2.6 20.0 2.3 21.6 3.0 j; Percent aged 65+ 11.8 2.0 11.4 1.6 12.2 2.2 12.4 1.7 11.5 3.2

Unified Democrat 0.29 0.48 0.41 0.49 0.30 0.46 0.25 0.43 0.45 0.50

Unified Republican 0.13 0.32 0.05 0.22 0.17 0.38 0.18 0.39 0.13 0.34 Divided government 0.58 0.50 0.54 0.50 0.53 0.50 0.57 0.50 0.42 0.49

Number of states 43 20 23 17 6

Years 26 26 26 26 26

Observations 1,118 520 598 442 156



418

Table 2. Political business cycles in the general fund surplus

No rule vs. strict rule

All states No rule vs. rule vs. weak rule

Election year -17.01** -31.78** -31.54** -41.52**

(6.75) (12.08) (12.06) (20.71) Election year + 1 -5.13 -22.29 -22.48 -45.53

(8.39) (17.29) (17.30) (31.41) Election year + 2 14.41** 14.46 14.42 -5.89

(7.34) (11.91) (11.90) (16.36) Election year

* rule 27.63**

(14.07) Election year + 1* rule 31.87

(20.06) Election year + 2* rule -0.72

(11.48) Election year

* strict 32.86** 25.42*

(14.50) (13.19) Election year + 1* strict 37.71* 29.96*

(20.80) (17.57) Election year + 2* strict 1.73 0.28

(12.58) (11.04) Election year

* weak 13.61 13.65

(15.77) (16.32) Election year + 1* weak 15.39 13.95

(20.44) (23.54) Election year + 2* weak -7.26 -9.35

(11.73) (10.08)

Regional Controls No No No Yes

Observations 1,118 1,118 1,118 1,118

Dependent variable = real per capita general fund surplus. Control variables = lagged depen

dent variable, real per capita state income, real per capita federal grants, unemployment rate,

population, percent aged 5-17 and 65+, unified Democratic government, unified Republican

government, year dummies. Robust standard errors in parentheses. * Significant at 10% level.

**Significant at 5% level.

of the population aged 5-17 or 65 and over, unified Democratic government, unified Republican government, and year dummies.19 Because the Arellano

Bond procedure takes first differences of all variables, I am controlling for

annual changes in each of these variables rather than levels; the levels are

differenced out.



419

Table 3. Political business cycles in general tax revenue



Election year -5.75* -8.12 -7.83 -4.88

(3.47) (5.70) (5.66) (9.12) Election year + 1 -6.12 -12.39 -12.15 -13.17

(5.14) (10.69) (10.66) (18.79) Election year + 2 -1.10 -5.21 -5.03 -11.79

(5.30) (9.77) (9.75) (16.85) Election year

* rule 4.54

(7.10) Election year + 1

* rule 11.83


* rule 7.68


* strict 4.21 1.55

(7.92) (7.35) Election year + 1

* strict 14.30 11.64

(12.70) (12.21) Election year + 2

* strict 12.10 10.88


* weak 5.70 4.62

(7.13) (7.15) Election year + 1

* weak 4.87 4.14

(13.11) (15.24) Election year + 2

* week ?4.76 ?7.77

(9.38) (11.36)


8.19e+ 3.55e+

Observations 1,118 1,118 1,118 1,118

Dependent variable = real per capita general tax revenue. Control variables = lagged depen



government, year dummies. Robust standard errors in parentheses.

*Significant at 10% level.

^Significant at 5% level.

The regression reported in the first column of Table 2 constrains political business cycles to be the same in all states; that is, it includes the election year dummy variables Eit but not the no-carry interaction terms rt Eit. Recall that the omitted category is the year prior to the election year; therefore, coefficients should be interpreted as relative to that base year. Thus, the coefficient on



420

Table 4. Political business cycles in general expenditure



Election year 10.11** 17.78** 18.03** 23.54**

(5.15) (8.35) (8.33) (8.63) Election year + 1 -4.01 0.42 0.94 5.85

(6.51) (11.22) (11.25) (10.21) Election year + 2 -20.62** -26.71** -26.59** -19.54**

(5.88) (9.17) (9.21) (9.89) Election year

* rule ?14.05


* rule ?8.04


* rule 12.02


* strict -19.49** -20.13**

(8.46) (7.79) Election year + 1

* strict ?6.37 ?6.53

(11.72) (10.76)

Election year + 2 *

strict 18.14* 18.15**


* weak 1.24 1.35

(10.16) (11.27) Election year + 1

* weak -12.57 -15.76

(15.15) (14.11) Election year + 2

* weak -5.28 -9.07

(12.93) (9.72)


6.02e+ 1.64e+

Observations 1,118 1,118 1,118 1,118

Dependent variable = real per capita general expenditure. Control variables = lagged depen



government, year dummies. Robust standard errors in parentheses. * Significant at 10% level.


"election year" in column one suggests that the real per capita general fund

surplus declines by $17.01 in election years. The coefficient on "election

year + 2" suggests that the fiscal position recovers two years after elections;

specifically, the per capita surplus is $14.41 larger than in the base year. This

finding that the surplus shrinks in election years and grows two years later



421

provides support for Hypothesis 1 that the American states exhibit political business cycles in fiscal balance.

The regression reported in the second column is identical to that in the

first column except that it relaxes the aforementioned constraint by includ

ing interactions between the electoral cycle and no-carry rules. The coeffi

cient on "election year" indicates that, in states without rules, the per capita

general fund surplus declines by $31.78 in election years; this deteriora

tion is greater than that reported in the first column for all states (however, the coefficient on "election year +-2" now falls short of statistical signifi

cance). The coefficient on "election year *

rule" suggests that in states with

rules, the election-year deterioration in the per capita surplus is only $27.63

$31.78 = ?$4.15. The coefficient on this interaction term is significant at the

five percent level, suggesting that political business cycles in the two sets of

states are statistically different. This is consistent with Hypothesis 2, which

predicted that no-carry rules are associated with a dampened political business

cycle. The regression reported in the third column of Table 2 distinguishes be

tween strict and weak rules. The election-year deterioration in fiscal balance

among states without rules is almost identical to that reported in the previ ous column. In states with strict rules, the election-year change in surplus is

now even closer to zero ($32.86-31.54 = $1.32). However, in states with weak

rules, the election-year deterioration is only about half the size of that in states

without rules ($13.61-31.54 =

?$17.93)-and moreover, this difference is not

statistically significant. This supports Hypothesis 3, which predicted that rules

that are difficult for politicians to circumvent by borrowing are more effective

than weaker rules in dampening the political business cycle. Indeed, no-carry rules unaccompanied by borrowing restrictions do not appear to diminish the

political business cycle at all.20

Balanced budget rules are not distributed evenly throughout the United

States, as shown in Figure 1. In particular, states with strict no-carry rules are

located disproportionately in the Midwest. To test whether there is something

special about Midwestern states-or states in any other region, for that matter

I add to the regression in column three interactions between the electoral

cycle and dummy variables for Midwestern, Southern, and Eastern states

(the omitted category is Western states).21 As shown in column four, the

inclusion of these controls slightly reduces the magnitude and significance of the coefficient on "election year

* strict," suggesting that only part of

the dampening effect in column three is attributable to strict no-carry rules.

Nonetheless, strict rules are still associated with a significantly diminished

political business cycle. Thus, regional differences appear to matter but cannot

account for my results.

As discussed in Section 4, political business cycles in fiscal balance could

be the result of cycles in taxes or spending (or both). I investigate each of



422

these possibilities in turn. Table 3 reports the results of regressions identical

to those in Table 2 except that the dependent variable is per capita tax revenue

instead of the per capita surplus. The coefficient on "election year" in column

one suggests that, as expected, taxes decline in election years. However, this

coefficient is small (?$5.75) relative to the magnitude of the cycle in the

surplus, and is barely statistically significant. When no-carry rules are added

to the model, this coefficient loses significance. These results suggest that the

political business cycle in taxes is negligible. Since the American states appear to exhibit a significant political business

cycle in fiscal balance but not in taxes, one would expect to find a cycle in

expenditures. The first column of Table 4 confirms this. Not only does per

capita spending rise by $10.11 in election years, it also falls by $20.62 two

years after elections.

Also as predicted, this cycle in spending appears to be smaller in magnitude in states with no-carry rules than in states without such rules, as shown in

column two. In states with rules, per capita spending rises by only $3.73 in

election years, compared to $17.78 in states without such rules, and falls two

years later by $14.69, compared to $26.71 in states without no-carry rules-but

these differences fall short of statistical significance.

However, column three reveals that, as before, the distinction between strict

and weak rules is critical. The political business cycle in states without rules is

virtually identical to that reported in the previous column: per capita spending rises by $18.03 in election years and falls by $26.59 two years later. In states

with weak rules, the political business cycle is not statistically significantly different from this. In states with strict rules, by contrast, per capita spending remains virtually unchanged in election years and falls by only $8.45 two

years later; these differences are significant at the five and ten percent levels,

respectively.

Finally, as shown in column four, when regional controls are added to

the regression, the coefficients on the election year dummies and strict rule

interactions increase in magnitude, statistical significance, or both, while the

coefficients on the weak rule interactions remain statistically insignificant.22

Thus, my results do not appear to be driven by regional patterns. Figure 2 illus

trates this dampening effect of strict no-carry rules relative to the impotence

of weaker rules, controlling for regional differences.

6.1. Discussion

Taken together, the regression results in Tables 2, 3, and 4 suggest that states

with strict no-carry rules do not exhibit political business cycles, while states

without these rules-as well as those with weak rules that can be easily circum

vented by borrowing-do exhibit cycles in fiscal balance. These cycles appear

to be driven by the expenditure side rather than the tax side of the budget.



423

30 -j?-1

g 20 \-^^^^^^^

| -10

]-^-^--?^

f ,20 J-^->^ x 3 ^. /

I I ?30-^

-40 -I-1

Election Year -1 Election Year Election Year + 1 Election Year + 2 Election Year - 1

I Without Rules-Weak Rules - - Strict Rules

|

Figure 2. Political business cycles in general expenditure.

This is perhaps not surprising, as it is probably easier for politicians to adjust

outlays than to modify the tax code. It is also consistent with the existing

empirical literature on political business cycles, which finds more evidence

of cycles in spending than in taxes.

Back-of-the-envelope calculations suggest that these cycles in fiscal bal

ance and spending are fairly large in magnitude. Based on the summary statistics in Table 1, the general fund surplus in states without strict rules

is approximately $150; the election-year deterioration of $41.52 represents

approximately one-fourth of this amount. Similarly, average per capita gen eral expenditure is approximately $4,000 in these states. State governments

typically have discretion over about 10-20 percent of general expenditure in a

given year, with the remainder locked in by mandates, initiatives, prior obliga tions, etc. (Rosenthal, 1990: 132). Thus, the spending cycle of $23.54+19.54

= $43.08 represents approximately five to ten percent of discretionary per

capita spending. An important caveat is that, while I have controlled for the relative ease with

which governments can circumvent no-carry rules by borrowing, I have not

controlled for their ability to use gimmicks. It is probably easier for politicians in some states than in others to make accounting adjustments to avoid closing

budget gaps with unpopular tax increases or spending cuts. For example, states

with large tobacco settlement funds often respond to budget shortfalls by

including in the revenue forecast "securitization proceeds" from the proposed sale of the state's stream of future tobacco settlement receipts-even if those

sales have not actually occurred (see McNichol, 2004) Similarly, states with

large reserve accounts earmarked for education, welfare, or other programs often temporarily transfer monies from those accounts into the general fund.



424

Finally, some states have "rainy day" funds set aside for precisely this purpose.

Thus, an extension of this paper might attempt to measure and control for

states' access to these and other special funds.

6.2. Partisanship and term limits

There are several reasons to believe that these results are not spurious. First, as discussed in Section 3, balanced budget rules are largely a product of his

torical accident, and therefore are relatively unlikely to be endogenous to the

preferences of current voters or politicians. Second, unlike previous studies

that have looked at the average impact of balanced budget rules on fiscal dis

cipline, I have focused on their interaction with the electoral cycle. Therefore,

the identification comes not from overall differences among states with and

without stringent balanced budget rules-indeed, anything that remains fixed

within a state over the sample period has been differenced out-but rather dif

ferences among these states over the electoral cycle, which is itself clearly

exogenous.

Nonetheless, it is important to test the robustness of these results. In par

ticular, it is possible that states with strict no-carry rules share some other

characteristic that explains why they are "differently different" over the elec

toral cycle. I have already tested for regional differences. The remainder of this

section investigates whether my results are robust to the inclusion of interac

tions between the electoral cycle and other state characteristics-in particular, the partisan composition of government and the presence of gubernatorial term limits.23 Because political business cycles appear to be driven by spend

ing, I focus on the regression model in which the dependent variable is per

capita general expenditure. For comparison, the first column of Table 5 repeats the results reported in the last column of Table 4.

States with strict rules experienced unified Republican government more

often than did other states during the sample period, as shown in Table 1.

Although the model in Section 4 does not make any predictions about the

impact of partisanship on political business cycles, one might expect cycles to be stronger under unified partisan control than under divided government

because a governor and legislature of the same party might have greater ability or incentive to coordinate reelection efforts. It is also possible that Republican and Democratic politicians have different preferences for political business

cycles, although the nature of this difference is not obvious, a priori. Thus, I

add interactions between the electoral cycle and dummy variables for unified

Republican and unified Democratic control to the regression (the omitted

category is divided government). The results are reported in the second column of Table 5. When Republi

cans control both branches, the election-year increase in spending is twice as

large as when the government is under divided partisan control; however, this



425

Table 5. Political business cycles in general expenditure: effects of partisanship and term limits

Basic model Partisanship Term limits Both

Election year 23.54** 22.13** 26.58** 24.88**

(8.63) (8.57) (9.10) (9.14) Election year + 1 5.85 -0.68 3.81 -2.51

(10.21) (11.47) (10.66) (11.53) Election year + 2 -19.54** -25.53** -14.97 -21.24*

(9.89) (10.47) (11.02) (11.23) Election year

* strict -20.13** -23.57** -19.19** -22.43**

(7.79) (7.95) (7.65) (7.87) Election year + 1

* strict -6.53 -11.26 -8.32 -13.07

(10.76) (11.10) (10.34) (10.72) Election year + 2

* strict 18.15** 16.72* 20.35** 19.38**

(9.18) (9.16) (9.36) (9.41) Election year

* weak 1.35 -2.61 2.38 -1.45

(11.27) (11.98) (11.18) (11.91) Election year + 1

* weak -15.76 -22.22 -15.82 -22.45

(14.11) (15.02) (14.02) (14.67) Election year + 2

* weak -9.07 -11.38 -7.55 -9.50

(9.72) (9.95) (9.23) (9.69) Election year

* unified Republican 20.61 19.70

(13.67) (13.30) Election year + 1


(29.34) (29.33) Election year + 2



* unified democrat ?7.77 ?6.51

(9.86) (10.14) Election year + 1

* unified democrat 1.06 0.35

(13.54) (13.75) Election year + 2

* unified democrat 10.53 12.62


* lame duck ?5.76 ?4.79

(8.18) (8.26) Election year + 1 * lame duck 13.80 13.53

(12.07) (12.30) Election year + 2

* lame duck -17.58 -18.73

(13.26) (13.51)

(Continued on next page)



426

Table 5. (Continued)

Regional controls Yes Yes Yes Yes

1.64e+ 6.05e+ 1.78e+ 6.86e+

Observations 1,118 1,118 1,118 1,118

Dependent variable = real per capita general expenditure. Control variables = lagged depen



government, year dummies. Robust standard errors in parentheses.

*Significant at 10% level.


and all other partisan interaction terms fall short of statistical significance.

Moreover, the coefficients on the election-year and no-carry-rule variables

remain largely unchanged. Thus, the partisan composition of government does not appear to significantly affect the magnitude of the political business

cycle. Second, I consider the possibility that my results are driven by the pres

ence of an institution other than fiscal rules. One likely culprit is term limits.

Governors who cannot run for reelection arguably have less incentive to gen erate political business cycles.24 Thus, if gubernatorial term limits are more

common among states with strict balanced budget rules, my results may be

partially or wholly attributable to this "lame duck" effect.

Data on term limits from the Book of the States indicate that there is

indeed a positive correlation between these two institutions. Of the 17 states

with strict no-carry rules in the sample, 16 (or 94 percent) have gubernatorial term limits, whereas among the 26 states without strict rules, only 19 (or 73

percent) have term limits. Therefore, I add to the model interactions between

the electoral cycle and a dummy variable for governors facing binding term

limits.25

The results, reported in column three of Table 5, suggest that political busi

ness cycles are not significantly different when the governor faces a binding term limit. Although the coefficient on "election year

* lame duck" suggests

that spending rises by 20 % less in election years ($20.82 compared to $26.58) when the governor is a lame duck, this coefficient is not statistically significant.

Moreover, the coefficients on the election-year and no-carry-rule variables re

main largely unchanged. Similar results are attained in column four, which

includes interactions between the electoral cycle and both partisanship and

binding term limits.

The finding that term limits do not affect the magnitude of the political business cycle suggests that governors care about their reputations even when

they cannot run for reelection. This might be because they have aspirations



427

for higher office, or because they want to help a member of their party (such as the lieutenant governor) take their place. This puzzle presents a potentially

interesting area for future research.

7. Conclusions

Using panel data from the American states, I have found evidence suggesting that fiscal rules dampen the political business cycle in public spending. While

spending rises before and falls after elections in states that can carry deficits

into the next fiscal year, this pattern does not exist in states with no-carry rules

if those rules are accompanied by borrowing constraints. Thus, the extent of

political manipulation of government finances appears to be shaped in an

important way by the institutional context in which the budget process takes

place. The American states are not alone in imposing limits on deficit spending. A

number of governments have recently adopted or considered adopting deficit

controls. In the 1990s alone, several Canadian provinces adopted balanced

budget requirements, the European Monetary Union approved the "Excessive

Deficit Procedure" as part of the Maastricht Treaty, and the United States

came close to adopting a balanced budget amendment to the Constitution. The

findings of this paper suggest that governments that restrict politicians' ability to run deficits will experience less politically-motivated fiscal volatility-but

only if politicians cannot easily circumvent those restrictions by resorting to borrowing. This implication should be weighed against other documented

lessons from the American states' experience with fiscal rules-namely, that

rules are associated with more rapid adjustment to revenue shortfalls but a

reduced ability to use countercyclical policy.

Finally, my finding that the magnitude of the political business cycle varies

in different contexts suggests several interesting directions for future research.

For instance, how do these cycles vary with the competitiveness of elections, the degree of fiscal transparency, or the balance of budgetary power between

governors and legislatures? The American states constitute an excellent lab

oratory in which to study "conditional" political business cycles.

Acknowledgements

I thank Jim Alt, Ilyana Kuziemko, David Dreyer Lassen, Lou Rose, Ken

Shepsle, Greg Wawro, Eric Werker, Gerald Wright, participants in the Work

in Progress Seminar at the Kennedy School of Government and the Political

Economy and Government Lunch at Harvard University, and Ron Snell at

the National Conference of State Legislatures for helpful suggestions. Finan

cial support from the Center for Basic Research in the Social Sciences and

the Center for American Political Studies at Harvard University is gratefully



428

acknowledged. An earlier version of this paper was prepared for delivery at

the 2004 Annual Meeting of the American Political Science Association.

Notes

1. See Alesina, Roubini, and Cohen (1992), Block (2002), Brender and Drazen (2004). The next section provides a detailed review of this literature.

2. Drazen (2000) provides an excellent review of this literature.

3. Indeed, the empirical literature on political cycles in macroeconomic activity provides little support for the Nordhaus model; see Drazen (2000).

4. However, there is a large literature suggesting that voters in the American states are quite

responsive to changes in fiscal policy, which is consistent with the political business cycle model (see for example Besley & Case, 1995a, & Lowry, Alt; Ferree, 1998).

5. The remainder of the relatively small literature on political business cycles in the Amer

ican states ignores the potential effects of institutions. Mikesell (1978) finds that states

are more likely to increase taxes immediately after elections than in election years.

Poterba (1994) finds that spending cuts and tax increases in response to unanticipated deficits are smaller in election years than in non-election years. And Clingermayer and

Wood (1995) find a positive correlation between state debt and "electoral competition," as measured by an election-year dummy variable interacted with the majority party's

margin in the state legislature. However, since the authors only include the interaction

term, omitting the two variables themselves from the regression, this result is difficult to

interpret.

6. Exceptions include Tennessee and California, which adopted their rules in 1977 and 2004,

respectively. See Savage (1988) for a history of balanced budget rules in the states.

7. These terms are suggested by Bohn and Inman (1996). 8. See Besley and Case (2003) and Bohn and Inman (1996) for a review of this literature.

A small related literature looks at whether balanced budget rules impede governments'

ability to pursue countercyclical policies; Bayoumi and Eichengreen (1995) and Levinson

(1998) find evidence suggesting that states with strict balanced budget rules are indeed

characterized by greater cyclical variability.

9. In the original model dt represented seignorage, but the authors note that it can also reflect

the budget deficit.

10. This model abstracts away from spending and revenue shocks, which-in the presence of

distortionary taxation-make it optimal for the government to run deficits or surpluses for

the sake of "tax smoothing" (see Barro, 1979).

11. The definition of the general fund varies somewhat across states. As discussed below, I

use data from the Census Bureau, which applies its own definition of the general fund to

all states.

12. As discussed below, I omit from the sample the handful of states with two-year cycles.

13. The states are not all on the same gubernatorial election schedule. For example, between

1996 and 1999, two-thirds of the states in the sample had gubernatorial elections in

1998, while 20 percent had elections in 1996 and the remainder had elections in 1997 or

1999.

14. Because this variable does not change over the sample period, it cannot be included by

itself in a fixed-effects regression. 15. All results reported in this paper are robust to the separation of strict no-carry rules into

those with referendum requirements and those with prohibitions on borrowing. I do not

control for states' ability to use gimmicks. I return to this issue in the next section.

16. See Wawro (2002) for a more detailed discussion of this topic.



429

17. Arellano and Bond recommend several diagnostic tests of the assumptions underlying

this model. The first is the Sargan test of overidentifying restrictions; the null hypothesis

is that the instruments are valid in the sense that they are not correlated with the errors

in the first-differenced equation. The authors also recommend tests of first- and second

order autocorrelation. If there is no first-order autocorrelation in the residuals of the levels

Equation (4.2), then there should be negative first-order autocorrelation but no second-order

autocorrelation in the residuals of the differences Equation (4.3) (see Arellano and Bond,

1991, for a discussion).'7 The null hypothesis in each case is that there is no autocorrelation.

In addition to these three tests, I also report the results of the Wald test of the hypothesis

that all coefficients in the model are jointly equal to zero. Conventional goodness-of-fit

measures such as the R-squared are not available for the Arellano-Bond estimator.

18. Many other states switched from two- to four-year gubernatorial election cycles in the

early 1970s, which is why I chose to extend my sample back only to 1974.

19. For the sake of parsimony, the coefficients on control variables are not reported; they are

available upon request.

20. The Wald statistics for these and all regressions reported in this paper indicate that the full

set of coefficients is jointly significantly different from zero at the one percent level. The

Sargan test statistics for all regressions indicate that there is not sufficient evidence to reject

the null hypothesis that the instruments are valid. Most of the first-order autocorrelation

tests indicate that, as expected, there is evidence to reject the null hypothesis of zero

first-order autocorrelation. However, in a few regressions the significance level for rejection

is between 20 and 30 percent; this may be due to the relatively small number of cross

section units (see Arellano and Bond, 1991). The second-order autocorrelation tests for

all regressions indicate that, as expected, there is not sufficient evidence to reject the null

hypothesis of zero second-order autocorrelation. Therefore the instruments appear to be

valid.

21. For the sake of parsimony, the coefficients on the regional interaction terms are not reported.

None of these coefficients are statistically different from the election year dummies, with

the exceptions of "election year +2* southern states" (coefficient = $32.76, t =

2.43) and

"election year +2* eastern states" (coefficient = $41.08, t =

2.27), suggesting that the

political business cycle is more pronounced in these regions.

22. None of the coefficients on the regional interaction terms are statistically different

from the election year dummies, with the exceptions of "election year +1* eastern

states" (coefficient = -

$28.88, t = ?1.76) and "election year +2* eastern states"

(coefficient = ?$34.45, t =

?2.05), suggesting that the spending cycle is more pro

nounced in the east.

23. I do not look at legislative term limits because these rules are a relatively recent phenomenon and therefore bind in only a handful of cases during my sample period.

24. As mentioned in the literature review, Besley and Case (1995b) test this hypothesis

using a fixed-effects regression on panel data from 1950 to 1986 but find little evi

dence of political business cycles, regardless of whether or not the governor is a lame

duck.

25. These data were generously provided by Tim Besley.

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Do Fiscal Rules Dampen the Political Business Cycle?

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