The Economic Consequences of Electoral Accountability Revisited *

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1 The Economic Consequences of Electoral Accountability Revisited * Daniel L. Millimet Assistant Professor Southern Methodist University Daniel M. Sturm Assistant Professor University of Munich John A. List Professor University of Maryland and NBER 18 June 2004 Abstract This paper revisits the impact of electoral accountability on total state expenditure and tax revenue with panel data from the 48 continental U.S. states from 1950 to Besides examining traditional tests of sensitivity, we present estimates from a difference-in-differences propensity score matching model (DD PSM) and a parametric difference-in-differences-in-differences approach (DDD) that relaxes the identification assumptions beyond those required in the matching model. We find that the estimated term limit impact is highly sensitive to modeling changes: while the effects of a binding term limit on total state expenditure and tax revenue documented in the literature are not robust to the expansion of the conditioning set, specifications requiring less stringent identification assumptions indicate that term limit effects are even stronger than previously documented, especially on tax policy. These results reinforce political reputation building models as a fruitful avenue to understanding political competition. Key words: term limits, fiscal policy, difference-in-differences-in-differences, propensity score matching JEL classifications: C23, D72, H71, H72 Correspondence: John A. List, The University of Maryland, 2200 Symons Hall, College Park, MD , Jlist@arec.umd.edu; website: * We would like to thank Craig Depken, seminar participants at several universities, and conference participants at the Western Economic Association International Annual Conference, Denver, CO, July We also thank David Kellerman from the U.S. Bureau of Census for extensive help with the local expenditure and tax data and for making a substantial part of the data available to us in electronic format. Alexander Knapp, Liesl Koch, and Alex Vialou provided excellent research and editorial assistance.

2 1. Introduction Debates over the consequences and desirability of term limits have a long tradition. Aristotle argued in favor of rotation of public office in noting that the tenure of all offices, or as many as possible, should be brief and that a man should not hold the same office twice. Term limits can be traced through the ancient Greeks to the sixteenth century renaissance of republican theory to the debates during the drafting of the U.S. Constitution. While term limits were eventually dropped from the constitutional debate, they have nevertheless become an important component of U.S. politics. 1 Grofman and Sutherland (1996) document that during the 1780s nearly half of the U.S. states imposed term limits on their governors. At the end of the twentieth century nearly 40 states had limits on the number of terms in office a governor could serve. 2 Despite the prominence of term limits in policy debates there have been relatively few empirical evaluations of the impact of term limits. 3 The main focus of the empirical literature has been to examine whether, and to what extent, politicians who face a binding term limit alter their behavior. Early contributions to this literature such as Lott (1987) and Lott and Bronars (1993) used retirements as a proxy for a binding term limit to investigate whether members of the U.S. Congress changed their voting behavior during their final term in office. This early literature generally found little evidence that term limits have significant effects. An obvious criticism of this approach is, however, that the last period that a politician spends in office 1 For a much more detailed historical sketch see Lopez (2003). 2 More broadly, the 1990s saw a wave of new term limit legislation for state lawmakers. Interestingly, term limits on U.S. Presidents were not imposed until the 22 nd Amendment was ratified in Prior to President Roosevelt, who was the only President to serve more than two terms, it was an unwritten rule in the realm of presidential politics that the President only served two terms. This precedent was seemingly set by President Washington, who could have been elected to a third term, but declined. 3 Likewise, there are few theoretical studies (for exceptions, see Dick and Lott (1993), Glaeser (1997), and Smart and Sturm (2003)). 1

3 before he voluntarily retires could be an imperfect proxy for the incentives that a lame duck politician faces. 4 In a seminal study, Besley and Case (1995a) investigated the effects of term limits on policy choices of U.S. governors. The authors use panel data for the 48 continental U.S. states from 1950 to 1986 to investigate how term limits affect total government spending and income, consumption and corporate tax receipts, and the state minimum wage. Controlling for state fixed effects and year effects, they find significant changes in these variables for years in which the incumbent governor faces a binding term limit. In particular, the authors find that both total state spending and total tax receipts increase if the governor is a lame duck, and that this effect is particularly strong for Democrats. These results lend strong support to reputation-building models of political behavior, which predict that the possibility of being re-elected to future terms in office acts as a powerful incentive instrument for politicians. In their recent survey of empirical political economy, Besley and Case (2003) revisit their earlier results and extend their original dataset to In this longer dataset, they continue to find that lame ducks significantly increase total state spending, but no longer find a statistically significant effect on the sum of state income, sales, and corporate tax revenues. More interestingly, the authors interact the lame duck dummy with time and find that the effect of a binding term limit has significantly declined over time. They speculate that this finding is likely due to omitted variable bias. Given the importance of reputation-building models of political competition, it is important to revisit the empirical effects of electoral accountability on economic policy choices. In this paper, we extend the approach of Besley and Case (1995a, 2003) along three distinct avenues. First, we assess the robustness of the term limit effect by varying the set of 4 See Besley and Case (2003), Lopez (2003), and Tabarrok (1994) for surveys of the term limits literature. 2

4 conditioning variables. Second, we alter the identification assumptions, as well as relax the parametric assumptions, via the use of a difference-in-differences propensity score matching estimator that also makes use of data on local fiscal policy. Finally, we employ a parametric difference-in-differences-in-differences approach that relaxes the identification assumptions beyond those required in Besley and Case (1995a) and the matching approach. Via our battery of empirical approaches, we directly tackle the potential endogeneity problem inherent in any empirical study of the consequences of term limits. We report several interesting findings. Our analysis suggests that the conditioning set matters greatly: simply relaxing the assumption of linearity in the control variables eliminates and even reverses the findings in Besley and Case (1995a, 2003). Yet, by relaxing the identification assumptions employed in Besley and Case (1995a, 2003), we find new evidence of the effects of political accountability on the determination of fiscal policy, robust to changes in the conditioning set. Assuming complementarity between state and local fiscal policy, we find term limit effects that are substantially larger than previously reported. Moreover, in a number of specifications we find that Republican lame duck governors increase per capita taxes and spending significantly more than their Democrat counterparts. The remainder of our study proceeds as follows. Section 2 discusses the empirical techniques employed. Section 3 describes the data and summarizes our empirical findings. Section 4 discusses our findings and concludes. 2. Empirical Models 2.1 Parametric Difference-in-Differences The initial parametric models used to assess the impact of electoral accountability on fiscal policy choices are nested in the following estimating equation: Y it = X it β + τt it + η it, (1) 3

5 where Y it is a measure of either per capita taxes or government expenditure in state i at time t, X it is a vector of state and governor attributes, T it is a binary variable (equal to one if the governor cannot seek re-election, zero otherwise), τ is the parameter of interest, and η it = λ t + α i + ε it, where λ t and α i are fixed time and state effects, and ε it captures all idiosyncratic shocks. τ represents the difference-in-differences (DD) average treatment effect for states with a lame duck governor (see, e.g., Athey and Imbens, 2002). τ is a DD estimate since it is identified from the excess temporal variation in fiscal policy in treatment states (those with lame duck governors) relative to control states (those whose governors are eligible for re-election). In addition to estimating (1) on the Besley and Case (1995a) sample ( ), we estimate three versions of (1) using the full data sample (known hereafter as the baseline model), where the differences lie in the control variables included in X. The most parsimonious case identical to that in Besley and Case (1995a) includes per capita state income, population, the proportion of the population aged 5 17, and the proportion of the population aged 65 and over as covariates. For robustness, we re-estimate this model, first by adding squared terms of each covariate and controls for the governor s age and age squared, and second by retaining the squared terms and adding a complete set of interactions between all five covariates. 5 The next set of regression models allows for specific forms of heterogeneous treatment effects. First, we test for differences in the behavior of lame duck Democrat and Republican governors by estimating Y it = X it β + τ d TD it + τ r TR it +η it, (2) 5 This results in ten interaction terms. 4

6 where TD it and TR it are dummy variables equal to one if state i at time t has a Democrat or Republican lame duck governor, respectively, τ d and τ r are the associated average treatment effects on states with lame duck governors, and all other notation has been previously defined. 6 Second, following Besley and Case (1995a), we allow the average treatment effect to vary over the election cycle. Specifically, we estimate Y it = τ 0 T0 it + τ 1 T1 it + τ 2 T2 it + τ 3 T3 it + τ 0n TN0 it + τ 1n TN1 it + τ 2n TN2 it + τ 3n TN3 it + X it β +η it, (3) where T0 it (TN0 it ) is a dummy variable equal to one if state i at time t has a lame duck (non-lame duck) governor and is currently in an election year, zero otherwise; and T1 it, T2 it, and T3 it (TN1 it, TN2 it, and TN3 it ) are dummy variables equal to one if state i at time t has a lame duck (non-lame duck) governor and is one, two, and three years, respectively, from its next gubernatorial election. 7 As with the baseline model, we estimate four versions of (2) and (3), varying the data sample and the set of controls in X. Identification of the DD treatment effect in the previous models requires that there be no state-specific shocks to fiscal policy that are correlated with, but not a result of, lame duck status. As stated and documented in Besley and Case (1995a, 1995b), however, lame duck status may be non-random, influenced by unobservables affecting fiscal policy. For example, a recession may lower an incumbent s probability of re-election and may also be correlated with lower per capita tax revenue (possibly due to lower sales tax collection as a result of less consumer 6 During the actual estimation of (2), the vector of controls, X, is expanded to also include a dummy variable for political party. 7 Note, although some states have gubernatorial elections every two years and others every four years, all observations are used in the estimation of (3). The difference in term length simply implies that states with only two-year terms can never be two or three years from the next election. 5

7 spending) and with higher per capita government spending (perhaps due to an increase in welfare recipients). To circumvent this potential problem, we use two alternative estimators that rely on different identification assumptions: (i) a semi-nonparametric difference-in-differences propensity score matching (DD PSM) estimator, and (ii) a parametric difference-in-differencesin-differences (DDD) estimator. As discussed more fully below, both methods control for certain state-specific unobservables that may be correlated with lame duck status by using data on local fiscal policy. Specifically, the DD PSM estimator uses variation in state, relative to local, fiscal policy in states with lame duck governors relative to control states without lame duck governors to identify the treatment effect. DD PSM estimation therefore requires (i) that there are no state-specific time-invariant (or time-varying) unobservables that differentially affect state versus local fiscal policy and are correlated with lame duck status, and (ii) that lame duck status does not directly or indirectly affect local fiscal policy. Alternatively, the DDD estimator examines changes in state, relative to local, fiscal policy in states with lame duck governors relative to control states without lame duck governors. DDD estimation therefore requires (i) that there be no state-specific, time-varying shocks that differentially affect state versus local fiscal policy and are correlated with lame duck status, and (ii) that lame duck status does not directly or indirectly affect local fiscal policy. 8 To compare the various estimators, along with the identification assumptions maintained by each, it is useful to consider the following two-state example, where for simplicity both states governors are reelected, but the lame duck governor (by definition) does not have the option of seeking a third term: 8 DDD estimates of the treatment effect are, however, consistent in the presence of state-specific, time-invariant unobservables that differentially affect state versus local fiscal policy. 6

8 Figure 1. State Level Local Level 1 st Term 2 nd Term Lame Duck Y 1,1,S y 1,2,S Non-Lame Duck Y 0,1,S y 0,2,S Lame Duck Y 1,1,L y 1,2,L Non-Lame Duck Y 0,1,L y 0,2,L where y s,t,k is (the conditional expected value of) a measure of fiscal policy in state s (s = 1 implies state has a term limit, 0 otherwise) at time t (t = 1,2 indexes the term in office) at level k (k = S,L indexes state and local level). The parametric DD estimator considered thus far is τ DD = (y 1,2,S - y 1,1,S ) (y 0,2,S y 0,1,S ). As stated above, if unobservable shocks are correlated with changes in state fiscal policy and the presence of a lame duck governor, then τ DD will not consistently identify the treatment effect. 2.2 Propensity Score Matching An alternative to the parametric DD estimator is the semi-nonparametric difference-indifferences propensity score matching (DD PSM) estimator. For clarity, we first discuss the general (non-dd) PSM estimator, and then extend the method to allow for a difference-indifferences estimator in the current context General Approach PSM was originally developed in Rosenbaum and Rubin (1983) and is an increasingly popular method for evaluating the effects of a particular treatment on an outcome of interest. While extensively used in other disciplines, economic applications have proliferated only recently. A few notable examples include Heckman et al. (1997, 1998), Dehejia and Wahba (1999, 2002), Smith and Todd (2000), Bratberg et al. (2002), List et al. (2003), and Persson and 7

9 Tabellini (2002). 9 Blundell and Costa-Dias (2002) provide an excellent introduction to the matching method, concluding that matching methods have been extensively refined in the recent evaluation literature and are now a valuable part of the evaluation toolbox (p. 4). The goal of PSM is to identify treatment effects despite the availability of only nonexperimental data, where treatment assignment is not likely to be random. To overcome the lack of experimental data, Rosenbaum and Rubin (1983) advocate finding a vector of covariates, Z, such that y y T, pr ( T = 1 Z) (0,1), (4) 1, 0 Z where denotes independence. If condition (4) holds, then treatment assignment is said to be strongly ignorable (Rosenbaum and Rubin, 1983, p. 43). To estimate the average treatment effect (on the treated), only the weaker condition E[y 0 T=1,Z] = E[y 0 T=0,Z] = E[y 0 Z] pr ( T = 1 Z) (0,1) (4') is required. Thus, the treatment effect is given by τ = E y y ], implying that conditional [ 1 0 Z on Z assignment of lame duck governors mimics a randomized experiment. Several details of this estimation procedure require further explanation. First, for condition (4) or (4') to hold, the appropriate conditioning set, Z, should be multi-dimensional. Consequently, finding observations with identical values for all covariates in Z may be untenable. However, Rosenbaum and Rubin (1983, 1985) prove that conditioning on p(z) is equivalent to conditioning on Z, where p ( Z) = pr( T = 1 Z) is the propensity score. In the next section, p(z) is estimated using a probit model, where Z includes population, per capita personal income, proportion of the population aged 5 17, proportion of the population aged 65 and over, 9 We point the interested reader to the Symposium on the Econometrics of Matching published in this Review (2004). 8

10 governor s age, the percentage of the total vote obtained by the incumbent during the previous election, squared and cubed terms for each variable, and a full set of interactions between all six covariates. 10 Second, after estimating the propensity score (i.e., the predicted probability of observing a lame duck governor), a matching algorithm is used to estimate the missing counterfactual, y 0, for each treated observation. The simplest algorithm is (single) nearest-neighbor matching, whereby each treated observation is paired with the control observation whose propensity score is closest in absolute value (Dehejia and Wahba, 2002; see Smith and Todd (2000) for a review of other methods). 11 Unmatched controls are then discarded. 12 The average treatment effect on the treated obtained via the matching method is given by τ M = E[E[y 1 T=1, p(z)] - E[y 0 T=0, p(z)]] = E[E[y 1 - y 0 p(z)]], (5) where the outer expectation is over the distribution of Z T = 1. The third issue one confronts under the matching technique is that although the propensity score is uni-dimensional, it is rare for two observations to have identical scores. The validity of the resulting matching estimate, however, requires that matched pairs have identical propensity scores. As a result, when using the matching method in practice, one may wish to exclude pairs with scores deemed to be too different. Known as caliper matching, the choice of 10 Dehejia and Wahba (2002) and others indicate that the inclusion of higher order and interaction terms in the firststage estimation of the propensity score is advisable as it facilitates balancing (discussed below). Note that since we are not concerned with the first-stage estimates per se, the loss of efficiency due to the inclusion of multiple covariates is not an issue. 11 Typically, nearest-neighbor matching is performed with replacement, implying that a given control observation may be matched with multiple treatment observations. Dehejia and Wahba (2002) verify that matching with replacement fares at least as well as matching without replacement, and possibly better. 12 The fact that unmatched control observations are discarded is one of the main distinctions between the method of matching and standard regression analysis. The matching method identifies a sub-sample of the full set of controls that better approximates the treatment group in terms of potentially confounding influences. As a result, using data from an actual randomized job training experiment (where the treatment effect is known), Dehejia and Wahba (2002) verify that matching provides a significantly closer estimate of the treatment effect than standard regression techniques. Bratberg et al. (2002) use data from an actual randomized experiment as well a rehabilitation project in Norway and obtain similar findings. 9

11 the caliper or maximum allowable difference in propensity scores across matched pairs is ad hoc. As noted in Dehejia and Wahba (2002), there is a trade-off: as the difference in propensity scores between matched observations increases, the greater the bias introduced, but there is also an efficiency gain as more pairs are retained. In our empirical analysis, we present results for a range of calipers. Fourth, the method of matching requires imposition of a common support (Blundell and Costa-Dias, 2002). Specifically, the matching estimator is defined over only the range of propensity scores common to both the treatment and control groups. As such, prior to implementing any matching algorithm, the common support of the propensity score is determined, and observations outside the common support are excluded. 13 Finally, upon completing the matching, a balancing test is conducted. Balancing refers to the fact that after conditioning on the propensity score, the distribution of the conditioning variables, Z, should not differ across the treatment and control group in the matched sub-sample. If the first moment of any of the conditioning variables differs across the matched treatment and control groups, the estimated treatment effect, τ M, will be biased if differences in such attributes also impact the outcome of interest. The various difference-in-differences matching estimators, however, will be biased only if such unbalanced attributes differentially affect state versus local fiscal policy. If not, they are implicitly controlled in the adjustment based on differences in local fiscal policy, discussed next. 13 In practice, this typically implies that control observations with a propensity score below the lowest propensity score in the treatment group, and treatment observations with a propensity score above the highest propensity score in the control group, are excluded. Even with our relatively large sample size, such trimming does not exclude a significant number of observations. 10

12 2.2.2 Difference-in-Differences Propensity Score Matching The matching estimator discussed thus far is applicable to situations of selection on observables, as the estimator given in (5) is equivalent to y 1,2,S y 0,2,S in the example in Figure 1. If state-specific attributes (either time-varying or time-invariant) affect both lame duck status and fiscal policy and are not captured by the propensity score, inferences based on the estimator in (5) may be incorrect. To relax this identification assumption, we take advantage of the richness of our data by employing a DD PSM estimator. Unlike the parametric DD estimator considered in Section 2.1, the DD PSM estimator does not use the difference in the outcome of interest prior to the treatment to control for omitted factors; rather, it uses the difference in local values of the outcome of interest (at the same point in time) across treatment and control states to proxy for omitted unobservables. As a result, identification in the DD PSM estimator requires that any omitted state-specific unobservables (time-invariant or time-varying) that are correlated with state fiscal policy and lame duck status do not differentially affect state and local fiscal policy. An interesting issue therefore is what type of unobservables are permitted under the DD PSM estimator that are not allowed under the parametric DD estimator in Section 2.1. Returning to the hypothetical in Figure 1, assume that prior to the elections being held at the end of each governor s first term, for example, one state suffers an economic crisis, while the other state enjoys an economic boom. If the state of the economy is not properly controlled, is correlated with the probability that each incumbent wins re-election (or, alternatively, is correlated with the presence of term limit laws), and affects fiscal policy in the second term, then the parametric DD estimator in the previous section will be biased. Yet, provided that (i) economic conditions do not differentially affect state versus local fiscal policy and (ii) local fiscal policy is unaffected by lame duck status, the DD PSM estimator will yield a consistent estimate of the treatment effect. 11

13 Thus, using measures of local fiscal policy, we can adjust the observed difference in state fiscal policy across matched pairs by the difference in local fiscal policy, analogous to the method used in Heckman et al. (1997), Eichler and Lechner (2002), and List et al. (2003). 14 Indeed, Blundell and Costa-Dias (2002, p. 12) endorse this approach, concluding that a joint [difference-indifferences] and matching approach may significantly improve the quality of non-experimental evaluation results. Formally, the matching estimator in (5) is τ M = E[E[y 1,S T=1, p(z)] E[y 0,S T=0, p(z)]], where the outer expectation is over the distribution of Z T=1. If the identification assumption in (4') does not hold, the bias is given by B = E[y 0,S T=1] E[E[y 0,S T=0, p(z)]]. The DD PSM estimator assumes that B can be estimated by E[E[y 1,L T=1, p(z)] E[y 0,L T=0, p(z)]], or the difference in local fiscal policy across matched pairs. Intuitively, this assumes that if local taxes/spending differs by $X across a matched pair, then state taxes/spending should also differ by $X, ceteris paribus. Thus, the DD matching estimator is given by τ M,DD,C = E[E[y 1,S - y 0,S p(z)] - E[y 1,L - y 0,L p(z)]], (6) where S (L) indexes fiscal policy outcomes at the state (local) level, C denotes complements (discussed below), and the outer expectation is over the distribution of Z T=1. Returning to Figure 1, the estimator in (6) is equivalent to (y 1,2,S y 0,2,S ) (y 1,2,L y 0,2,L ). An important issue arises with regard to the proposed correction in (6). Typically, DD PSM estimators use differences in the outcome of interest prior to the treatment to proxy for the bias term. For example, Eichler and Lechner (2002) and Heckman et al. (1997) subtract pre- 14 This assumption is referred to as the bias stability (BS) assumption in a different context in Eichler and Lechner (2002) and Heckman et al. (1997), where the authors assume that wage differentials between participants and nonparticipants prior to the availability of a job training program proxy for unobservable differences between the treatment and control group after the intervention. List et al. (2003) assume that differences in the location of nonpollution-intensive manufacturing plants proxy for unobservable differences between counties with and without stringent environmental regulations that affect the location decisions of pollution-intensive plants. 12

14 treatment wage differentials from post-treatment differentials in order to obtain the DD estimate of various interventions on wages. In such cases, it is reasonable to subtract pre-treatment differences since pre- and post-treatment wages are positively correlated through unobserved factors such as ability and motivation. In the current context, this means that the bias correction in (6) supposes that higher local taxes/spending should imply higher state taxes/spending ceteris paribus. It is not clear, however, if state and local fiscal policies are indeed positively correlated. When maintaining the assumption of positive correlation, we will refer to state and local fiscal policy as complements (hence the subscript C in (6)). On the other hand, if unobservable state-specific shocks that may be correlated with the presence of term limits (and, hence, lame ducks) affect state and local fiscal policies in the opposite direction, we will say they are substitutes. For example, if a shock results in lower state taxes, state-provided public goods may suffer as a consequence. As a result, localities may decide to increase taxes under their discretion to compensate for the lack of state-level funds. On the other hand, a recession may result in lower tax revenue at all levels of government. If state and local taxes move in the opposite direction as a result of various unobservable shocks, then the correction utilized in (6) is incorrect; instead, we need to employ an additionin-differences estimator. In other words, returning to the hypothetical example in Figure 1, the correct estimate should be (y 1,2,S y 0,2,S ) + (y 1,2,L y 0,2,L ), and the corresponding matching estimator is given by τ M,DD,S = E[E[y 1,S - y 0,S p(z)] + E[y 1,L - y 0,L p(z)]] (6') where S denotes the assumption of state and local substitutability For consistency, we continue to refer to the estimator in (6') as a DD estimator. Note that in traditional program evaluation studies the treatment group experiences the intervention and the control group does not. Thus, the second term in equation (6) typically does not depend directly on treatment. 13

15 The critical issue necessarily turns to whether state and local policies are complements or substitutes. Unfortunately, vertical interaction between governments in the setting of fiscal policy in federal systems has been largely neglected until only recently (Keen and Kotsogiannis, 2002, p. 363). Given a finite tax base within each state and a fixed number of public goods that voters might consider necessities (e.g., police protection, public education, etc.), one might conclude that state and local taxes are substitutes, because as long as one level of government satisfies the needs of the public, it is not necessary for the other level to do the same. Alternatively, if some states are more tax-friendly, while people in other states are more likely to backlash against taxes from any level of government, one might expect state and local taxes to be positively correlated, and thus be complements. The few empirical studies on fiscal federalism in the U.S., as well as within other countries, yield contradictory findings. For example, using a panel of 13 OECD countries from 1975 to 1984, Goodspeed (2000) documents a negative relationship between federal and local income tax rates. Hayashi and Boadway (2001), likewise, document lower levels of business taxation at the local (provincial) level in Canada during periods of higher federal taxation over the period Besley and Rosen (1998) present evidence that U.S. states follow the lead of the U.S. federal government, however, when setting cigarette and gasoline taxes. And Esteller-Moré and Solé-Ollé (2001) generalize the Besley and Rosen (1998) results to personal income and general sales tax rates. The literature is mute on the question to which we seek an answer in this case, as it does not analyze local versus state taxation only state or provincial taxes relative to federal taxation and it does not assess the relationship between government spending at various levels. However, given the results from Esteller-Moré and Solé-Ollé (2001) and Besley and Rosen (1998), which use evidence solely from the U.S., and assuming that the local-state relationships 14

16 (for taxes and spending) operate in the same manner as the state-federal tax relationship, the assumption of complementarity appears to be most reasonable. Furthermore, two other pieces of evidence point in this direction as well. First, in our dataset the sample correlation coefficient between total per capita state and local taxes (per capita state and local government expenditures) is 0.43 (0.75). Second, to explore correlations within states, we regressed state-level taxes (expenditures) on state and time indicators, as well as local tax (expenditure) levels. All coefficient estimates are positive and significant at the p < 0.06 level using a two-sided alternative; thus we focus on estimates based on the assumption of complementarity, but for completeness we present estimates of both (6) and (6'). 16 Finally, as in Section 2.1, we allow for heterogeneous treatment effects by political party and stage in the electoral cycle. For separate effects by political party, this entails restricting matched pairs to be from the same political party, and then estimating (5), (6), and (6') once for matched pairs of Democrat governors, and once for matched pairs of Republican governors. Similarly, to allow the lame duck effects to vary over the election cycle, we restrict matched pairs to be at the same stage of the electoral cycle, and then we estimate (5), (6), and (6') separately for each stage. 2.3 Parametric Difference-in-Differences-in-Differences An alternative estimation technique that relaxes the identification assumption needed by the parametric DD estimator in Section 2.1 and returns to a parametric framework is the 16 Besides suggesting a positive correlation between state and local fiscal policy, the empirical studies on vertical interaction suggest that local fiscal policy may be affected by state fiscal policy in a causal manner. If state fiscal policy directly affects local fiscal policy, then governors may indirectly affect local fiscal policy through their impact on state fiscal policy, thereby invalidating one of the identifying assumptions of the DD PSM estimator: local fiscal policy must be unaffected by lame duck status. However, under such a scenario, one can show that the DD PSM estimator is attenuated toward zero, and therefore represents a lower bound (in absolute value) on the actual term limit effect. 15

17 difference-in-differences-in-differences (DDD) estimator. In the example in Figure 1, the DDD estimator is τ DDD = [(y 1,2,S - y 1,1,S ) - (y 0,2,S y 0,1,S )] - [(y 1,2,L - y 1,1,L ) - (y 0,2,L y 0,1,L )]. (7) As argued elsewhere, DDD estimates entail fewer restrictions than DD estimates (e.g., Gruber, 1994; Moehling, 1999; Zavodny, 2000). 17 In the current application, DDD requires (i) that there are no state-specific, time-varying unobservables correlated with lame duck status that differentially affect state versus local fiscal policy in lame duck states and (ii) that local fiscal policy is not affected by lame duck status. 18 While the intuition is similar to the DD PSM estimator, the identifying assumptions are less restrictive since time-invariant, state-specific unobservables that differentially affect state versus local fiscal policy will bias only the DD PSM estimator. In a regression context, the DDD estimator in (7) is given by Y itk = X it β + γ 0 TWO t + γ 1 L i + γ 2 LEVEL k + γ 3 L i *TWO t + γ 4 LEVEL k *TWO t + γ 5 L i *LEVEL k + γ 6 L i *TWO t *LEVEL k + η it, (8) where Y itk is a fiscal policy measure in state i in year t at level k (k = S,L), TWO t is a dummy variable equal to one if the governor is in his or her second term, zero otherwise, L i is a dummy variable equal to one if the governor belongs to the treatment group (i.e., is, or will be, a lame duck), zero otherwise, and LEVEL k is a dummy variable equal to one if Y is measured at the state level. It is straightforward to verify that γ 6 = τ DDD is the DDD estimate of the treatment effect See Gruber and Poterba (1994) and Kaestner (2000) for other applications of the DDD methodology. 18 If local fiscal policy is affected by lame duck status, the DDD estimator will be attenuated toward zero, thus representing a lower bound in absolute value. See footnote While other differences arise as well, the parametric DD estimator in Section 2.1 imposes the restriction that γ3 = 0, while the DD PSM estimator in Section imposes the restriction that γ 5 = 0. 16

18 Prior to continuing, a few comments are in order. First, during the actual estimation, equation (8) has to be slightly altered because not all lame duck governors are lame ducks in the second term; a few governors in the sample do not become lame ducks until their third or fourth term. 20 Second, unlike many DD or DDD applications, the treatment occurs repeatedly and not at the same time for all states. Thus, we estimate the following equation: Y itk = X it β + γ 0 TERM it + γ 1 L it + γ 2 LEVEL k + γ 3 L it *TERM it *T it + γ 4 LEVEL k *TERM it + γ 5 L it *LEVEL k + γ 6 L it *TERM it *LEVEL k *T it + η it, (9) where TERM it is a dummy variable equal to one if the governor in state i at time t is in his or her (at least) second term in office, zero if it is the governor s first term, and T it, as before, equals one if the governor in state i at time t cannot seek re-election during the next gubernatorial election. Third, some states allow governors to serve only one term. Consequently, in the notation in equation (9), some first-term governors (TERM it = 0) will be lame ducks (L it = T it = 1). Inclusion of states with only a one-term term limit still adds to the identification of γ 3 and γ 6 in (9) since even in single-term states some governors do not become lame ducks until their second term in office if they took over for the previously elected governor partway through his or her term. Thus, technically, one-term limit states still may have incumbents seeking reelection. 21 Nonetheless, we estimate (9) using all available observations, as well as on the subsample excluding state-year observations for which a one-term limit is in place, given Johnson and Carin s (2001) critique that Besley and Case s (1995a) term limit effect was driven solely by one-term limit states. The results from the two samples will differ if states with one-term limits are not a random sub-sample, thereby introducing sample selection bias through their exclusion. 20 Five governors are lame ducks in their third term, while one governor is a lame duck in his fourth term. 21 There are five instances of this occurring in the data. 17

19 Fourth, as in the previous section, the usual DDD set-up assumes that the outcomes of the treatment group in treatment states are positively correlated with the outcomes of the control group in the treatment group states. For example, Gruber (1994) uses DDD to assess the impact of mandated maternity benefits on the wages of those likely to be covered by the policy in the states that enacted such a policy. The author defines the treatment group as women aged 20 40, and the control group (within the treatment states) includes all individuals over age 40 and single men aged The control group also includes women aged in states that did not enact the law, as well as all individuals over age 40 and single men aged in states that did not enact the maternity mandates. The use of individuals over age 40 and single men aged from treatment states allows the author to control for unobservable state-specific shocks likely to affect the wages of all individuals that are correlated with the enactment of the maternity statute. Since such shocks are assumed to affect the wages of all individuals in the same manner (i.e., positively or negatively), differential trends in the wages of the control groups across treatment and control states are differenced out. In the current application, this corresponds to assuming that state and local fiscal policy are complements. As articulated in the previous section, this is the assumption we feel is most realistic given available evidence. Nonetheless, we also obtain DDD estimates assuming state and local fiscal policy are substitutes. In the regression equation (9), it is straightforward to verify that τ DDD,S, = γ 6 + 2γ 3. Finally, as with the previous estimators, we allow the treatment effect to vary across political parties and the electoral cycle. In both cases, this entails re-estimating (9), allowing the appropriate interactions. Furthermore, we estimate four versions of each model, as in Section 2.1, varying the data sample and the set of control variables. 18

20 3 Data and Empirical Results 3.1 Data To estimate the effects of electoral accountability on economic policy choices, we utilize state-level panel data from 1950 to We obtained access to the Besley and Case (2003) data, for which we are grateful. We then updated and extended their data through The primary explanatory variable in the Besley and Case (2003) dataset is a dummy variable that indicates whether the incumbent governor faces a binding term limit at the end of his or her current term. This variable was originally constructed from information available in the Book of the States. Table A1 summarizes the term limit legislation for governors in the U.S. states between 1950 and Additional explanatory variables contained in the Besley and Case (2003) dataset include per capita state income and state demographic variables, such as total state population and the proportion of the population between 5 and 17 and over 65. The policy variables in the Besley and Case (2003) data include state sales, income, and corporate tax receipts, as well as the total general expenditures of each state. These data were originally taken from the Statistical Abstract of the United States and the State Government Finances publications of the U.S. Bureau of Census. We have expanded the dataset in several directions. First, we supplemented the dataset with local tax revenue and expenditure data. On the expenditure side, we added total general expenditures by all local governments in each state. On the tax side, we added total local tax revenue collected by all localities in each state. These data are available from 1958 onwards, and 22 We corrected a few minor errors in the dataset. These corrections do not substantially affect the results. A list of all changes that were made to the Besley and Case (2003) dataset is available from the authors on request. 19

21 were obtained from the U.S. Bureau of Census publication Governmental Finances for the early years and provided in electronic format by the U.S. Bureau of Census from 1977 onwards. Second, we added a new variable measuring total tax revenue by state governments, obtained from the same sources as above. This variable differs substantially from the variable total taxes in Besley and Case (1995a, 2003). The latter variable is simply the sum of the state income, sales, and corporate tax revenues. Our variable truly reflects total tax receipts by state governments, which differs from the sum of income, sales, and corporate tax revenues due to other state taxes such as, for example, motor fuel and motor license taxes. Finally, we added additional control information on the governors in the sample. In particular, we measure how many terms a governor served. Table 1 presents means and standard deviations of all variables and also contains the source of each variable. We also include results of t-tests associated with the null of equal means across states with and without lame duck governors at the p < 0.05 level. 3.2 Parametric Difference-in-Differences Baseline Specification Table 2 presents the most relevant empirical results from the parametric DD baseline model in (1). Four models are estimated, varying the sample and set of covariates. Model I replicates the baseline model in Besley and Case (1995a) using their sample period, , with the only difference being that we updated the data along the lines discussed in Section 3.1. Empirical results are virtually identical to their original findings: lame duck governors have a statistically significant, positive effect on per capita sales (τ = 5.92, t = 1.89) and income taxes (τ = 7.20, t = 2.01), as well as per capita government spending (τ = 13.30, t = 1.86). Model II re-estimates the baseline model from Besley and Case (1995a), extending the sample through 1999 (referred to as the Full Sample hereafter). Empirical results are fairly 20

22 similar to those from Model I, with lame duck governors having a statistically significant, positive impact on per capita income (τ = 9.06, t = 2.73), corporate (τ = 1.82, t = 1.82), and total (τ = 10.67, t = 2.44) taxes, as well as on per capita government expenditures (τ = 28.28, t = 3.79). Inclusion of the more recent data does increase the magnitude of the lame duck effects, however, as the point estimates for per capita total taxes and government spending more than double (from 3.93 to and to 28.28, respectively). Models III and IV assess the robustness of these findings by expanding the set of covariates to include governor s age, as well as higher order terms (Model III) and the full set of interactions between the controls (Model IV). In both cases empirical results are drastically altered as now all of the lame duck effects are statistically insignificant at conventional levels except for per capita aggregate taxes (sales + income + corporate taxes), where the point estimate is negative, suggesting in Models II and IV that lame ducks reduce per capita aggregate taxes by $11.08 (t = 2.63) and $7.08 (t = 1.70) per annum, respectively. 23 Robustness of the Baseline Results Before moving to the models allowing for possible heterogeneous impacts of lame ducks, we further assess the robustness of the baseline specification through the employment of Leamer s (1983, 1985) extreme bound analysis (EBA). EBA, as applied in, for example, Levine and Renelt (1992) and Fölster and Menrekson (2001), involves estimation of regressions of the form Y it = Z jit β j + τ j T it + η it, (10) 23 Re-estimating Models III and IV on the original Besley and Case (1995a) sample, , does not dramatically change the results. In both models lame ducks have a statistically significant effect only on corporate tax receipts, and the effect is negative (Model III: τ = -1.78, t = 1.75; Model IV: τ = -1.58, t = 2.04). Furthermore, if we exclude governor s age and only utilize the original variables in Besley and Case in Models III and IV, our results remain robust. 21

23 where Z j X is a vector of up to four variables taken from the full vector X. After estimation of (10) for all possible combinations of Z j X, the lower (upper) extreme bound for the lame duck effect is defined as the lowest (highest) value of τ j - 2σ j (τ j + 2σ j ), where σ j is the standard error of τ from specification j. If the lower and upper bounds are of the same sign, then the lame duck effect is said to be robust; if not, the effect is said to be fragile. EBA has been criticized, however, for being too stringent: if the parameter of interest, τ, is insignificant (at the 95% significance level) in even one specification, the effect of the variable of interest, T, is concluded to be fragile (Sala-i-Martin, 1997). In light of this criticism, Fölster and Menrekson (2001) also report the percentage of specifications for which the parameter of interest is statistically significant. To proceed, we estimate (10) where X initially includes per capita income, population, percentage aged 5 17, percentage aged 65 and over, and governor s age. Thus, we estimate 30 versions of (10), including all combinations of one, two, three, or four variables from this set as controls. 24 Using the full sample, the bounds exclude zero for three of the six fiscal policy measures, indicating a robust lame duck effect for income tax, total tax, and government spending; for sales tax, corporate tax, and aggregate tax, the lame duck effect is fragile. 25 Analyzing the distribution of the estimates and using a 90% significance level, the lame duck effect is positive and statistically significant in 100% of the specifications for income tax, total tax, and government spending, 97% of the specifications for corporate tax, and 0% of the specifications for the remaining policy measures. 24 All specifications include time and state fixed effects, and we maintain the use of Huber standard errors. 25 Bounds are [2.15, 22.01] for income tax, [0.78, 22.75] for total tax, [10.69, 47.96] for government spending, [- 6.03, 10.19] for sales tax, [-0.36, 4.81] for corporate tax, and [-7.02, 16.63] for aggregate tax. 22

24 Inclusion of higher order terms (control set B) in Table 2 is sufficient to eliminate and even reverse the positive lame duck effects found in the Besley and Case (1995a) baseline specification. To assess the robustness of these findings, we re-perform the EBA analysis, expanding the vector of potential controls to include the five previous variables (per capita income, population, percentage aged 5 17, percentage aged 65 and over, and governor s age), plus the quadratic of each. In this case we conduct the EBA slightly differently, however. Specifically, we still draw one, two, three, or four variables from the five linear variables (per capita income, population, percentage aged 5 17, percentage aged 65 and over, and governor s age), but we include the squared term for each chosen variable in the regression as well. 26 Thus, the EBA still involves 30 regressions. Using the full sample, the bounds now encompass zero for all six fiscal policy measures, indicating a fragile lame duck effect for each outcome. 27 Using a 90% significance level, we do, however, find modest evidence of a lame duck effect, although much less so than in the EBA, excluding the quadratics. Specifically, the lame duck effect is positive and statistically significant in 50% of the specifications for income tax and government spending, 40% of the specifications for corporate tax, and 37% of the specifications for total tax, and the lame duck effect is negative and statistically significant in 50% of the specifications for aggregate tax. Lastly, the lame duck effect is never statistically significant for sales tax. Thus, the EBA confirms the results in Table 2. Specifically, inclusion of higher order terms significantly weakens the estimated relationship between lame duck governors and the six fiscal policy measures. 26 For example, if specification j includes, say, population and per capita income as the two controls, then population squared and per capita income squared are also included in specification j. 27 Bounds are [-8.55, 11.18] for sales tax, [-1.94, 4.62] for corporate tax, [-6.84, 22.47] for income tax, [-20.23, 16.93] for aggregate tax, [-13.17, 22.64] for total tax, and [-10.68, 46.73] for government spending. 23

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