Public Campaign Finance and
the Incumbency Advantage*
Timothy Werner
Assistant Professor
Department of Business, Government & Society
McCombs School of Business
University of Texas at Austin
1 University Station, B6000
Austin, Texas 78712
(512) 471-5921
[email protected]
Kenneth R. Mayer
Professor
Department of Political Science
University of Wisconsin–Madison
110 North Hall
1050 Bascom Mall
Madison, Wisconsin 53706
(608) 263-2286
[email protected]
June 2012
Abstract
Despite an increasing incumbency advantage at the state legislative level, there has yet to be an
assessment of how the advantage varies across state-level campaign finance regimes. These laws
range from near complete deregulation to full public funding. This paper estimates the advantage
for lower chamber candidates in 45 states over 28 years and, through the use of a fixed effects
panel framework, models the advantage as a function of state-specific variables and broader
conditions. We find minimal effects for campaign finance laws, with the exception of full public
funding programs, which decrease the incumbency advantage by 2 percent of the two-party vote,
cutting it roughly in half. We corroborate this finding for full public funding by applying the
synthetic control method to the incumbency advantage in Arizona, an early adopter of this
reform, and there, we find a reduction in the advantage of 1.65 percent of the two-party vote.
Word Count: 8,431
* This paper was originally prepared for the 2011 meeting of the Midwest Political Science
Association, Chicago, Ill., March 31–April 3. We would like to thank Anna Bosak, Joseph
Durheim, and Michael Horecki for their research assistance; David Primo and Jeffrey Milyo for
sharing their data; and R. Keith Gaddie, Jonathan Krasno, and Neal Malhotra for their advice and
comments. 1 Disclosure: One of the authors (Mayer) served as an expert witness for the State of
Arizona’s Department of Justice, which defended the public funding law.
How much is incumbency worth, and what factors produce this advantage? These
questions have spawned an extensive literature, as scholars have grappled with one of the most
fundamental issues in representative government. As Gelman and Huang (2008) note, the
incumbency advantage is “one of the most widely studied features in American legislative
elections” (437). Incumbents are far more likely to be reelected than to lose, an obvious point
that quickly becomes far more consequential as scholars try to identify the causes and
consequences of the increasing advantages of incumbency. The 2010 midterm election provides
one measure of incumbency’s power: In 2010, Republicans captured control of 19 legislative
chambers from Democrats, yet 85 percent of incumbent legislators who sought reelection won.
Legislative incumbents, in particular, appear to accrue significant benefits from
incumbency. First, legislative office provides a host of electoral perquisites: high name
recognition, large fundraising advantages, and the ability to engage in constituency service,
credit claiming, and blame avoidance (e.g., Ansolabehere, Snyder, and Stewart 2000; Fiorina
1977). Second, legislators benefit from selection effects in elections, in which better candidates
are more likely to become incumbents and to continue to develop relevant skills while in office
(e.g., Ashworth and Bueno de Mesquita 2008; Erikson 1971). Third, the combination of these
first two benefits produces another: the deterrence of high quality challengers (e.g., Cox and
Katz 1997; Gordon, Huber, and Landa 2007).
As this brief review suggests, scholars have devoted significant attention to where the
incumbency advantage comes from, how to measure it, how much it is worth, and what its
consequences are for democratic theory. Our goal here is not to reopen the debate over how to
measure the incumbency advantage but to explore how efforts to reform the electoral system
affect the advantage. Specifically, we focus on determining what effect, if any, the introduction
2
of full public funding campaign financing for state legislative races has on the incumbency
advantage. Through the use of a fixed effects panel regression model and of a synthetic control
analysis of Arizona, we find that full public funding cuts the incumbency advantage roughly in
half.
Full Public Funding and its Hypothesized Effects
Full public funding programs offer candidates the option to forego private fundraising
and instead receive lump sum grants intended to fund their campaigns fully. As the result of
ballot initiatives, Arizona and Maine introduced these programs in the 2000 election cycle, and
Connecticut’s legislature adopted a similar program prior to 2008. The programs were the result
of scandals in state level government (Arizona and Connecticut) and general efforts to reduce the
influence of “special interests” (Maine). The origins of full public funding are reflected in their
moniker, “Clean Elections,” highlighting that the programs’ goals focused on lessening
corruption and improving the public policy process, not on enhancing electoral competition. In
fact, one major critique of these programs is that they do the opposite and are little more than
incumbent protection rackets (Samples 2005).
Nonetheless, to ensure their viability, these public funding programs originally included
“matching funds” provisions that protected participating candidates from being overwhelmed by
opposition spending by privately funded candidates or independent groups. When opposition
spending hit specified triggers, participating candidates received supplemental grants. In June
2011, however, the U.S. Supreme Court struck down these matching funds provisions on First
Amendment grounds in Arizona Free Enterprise Club’s Freedom Club PAC et al. v. Bennett et
al., 564 U.S. ___, a decision that followed a lower-court injunction that barred the use of
3
matching funds in 2010. Despite striking down the matching provisions, the Court’s decision
affirmed the constitutionality of the remaining components of public funding programs.
When public funding programs came into existence, some scholars and advocates
believed that their byproducts would include an increase electoral competition and a decrease the
incumbency advantage, even if the programs were intended to address other political ills. The
mechanisms believed to increase competition were straightforward. First, by providing
challengers with access to “free money,” incumbents would no longer have an overwhelming
fundraising advantage, reducing this perquisite. If electoral outcomes are related to spending,
such equalization should put incumbents and challengers on a more equal footing. Second, the
availability of public funds should encourage challengers to step forward who might otherwise
be deterred by fundraising. This lack of a “wealth primary” should increase the number of
contested districts and lead otherwise risk-averse quality challengers to run, lessening this benefit
of incumbency too. This leads to the hypothesis we seek to test: in state-cycle combinations in
which a full public funding program with a matching funds provision is in force, the incumbency
advantage will decrease.
The effect implied by our hypothesis squares with exiting research on the impact of
public financing programs on competitiveness. An early assessment of the public funding
programs in Maine and Arizona concluded that levels of competition – as measured by the
percentage of races contested by the major parties, incumbent victory margins, and the
incumbent reelection rates – increased slightly in the wake of their introduction (Mayer, Werner,
and Williams 2006). Self-assessments of public funding by state agencies have also been
positive (Maine Commission on Government Ethics and Election Practices 2007), and one study
4
(Malhotra 2008) found significant increases in competitiveness in state senate elections in
Arizona and Maine.
Nonetheless, as many of the authors cited above note, the magnitude of these competitive
effects were smaller than expected, and in Arizona, most indicators returned to pre-reform levels
within a few cycles. Further, other assessments have reached more mixed conclusions as to the
competitiveness effects of public funding in Arizona and Maine: Two studies by the
Government Accountability Office (2003; 2010) observed little change in Maine’s and Arizona’s
electoral environments, and early work on Connecticut found no effects on various
competitiveness measures for its program (Cavari and Mayer 2011).
These differing findings call for an analysis of the effects of full public funding that goes
beyond descriptive statistics and investigates systematically whether the introduction of full
public funding has a significant effect on electoral competition and, in particular, on the
incumbency advantage. As we articulated above, we view the decision to challenge an
incumbent and the ability to do well when doing so as related to the availability of campaign
funds, and this view informs our goal of identifying the systemic effect of full public funding on
the incumbency advantage.
Modeling the Incumbency Advantage across States and Time
Our analysis proceeds in three steps. First, we estimate the incumbency advantage using
a modified version of Gelman and King’s (1990) regression-based approach. Second, we use
these estimates as the dependent variable in a weighted time-series–cross-section (TSCS)
framework that models the incumbency advantage across state-cycles as a function of the
presence of a full public funding program and other institutional and behavioral factors. Third,
5
we corroborate the findings of our TSCS model by applying synthetic control methods to the
case of Arizona.
Measuring the Incumbency Advantage
We first need a measure of the incumbency advantage that we can then use as the
dependent variable in an analysis to estimate the effects of public funding. We focus on lower
chambers of state legislatures, because they have more observations and are less likely to have
staggered terms. To estimate the incumbency advantage, we use Gelman and King’s (1990)
regression-based approach, which has seen wide use in the incumbency advantage literature.1 As
1
Although there are several different estimators of the incumbency advantage that we could have
employed, we believe that our choice performs best for a study of this temporal and
geographic scale. First, this estimator produces results similar to Levitt and Wolfram’s
(1997) model at the congressional level, which takes into account candidate quality, and
Ansolbehere and Snyder’s (2002) model at the state-legislative level, which offers an
alternative, more informed measure of the normal vote in a district. Second, Gelman and
King’s regression results correlate highly with Gelman and Huang’s (2008) Baysian
estimates of the advantage: They find the same trends across time, but Gelman and Huang’s
estimates are not quite as high as Gelman and King’s (there is roughly a 2-point gap between
them). Third, although much recent work has employed regression discontinuity designs to
estimate the incumbency advantage (see, Caughey and Sekhon 2011 for a summary and
critique of this technique or Uppal 2010 for an application of it to state legislatures), these
designs, while powerful from an identification standpoint, do not suit our purposes, as they
rely on an exceedingly small subset of races (bare winners/losers) to estimate the advantage;
6
this equation reveals, we deviated slightly from the original Gelman and King formula, however,
by using the lagged winning party rather than the current winning party to avoid endogeneity:2
𝐄 𝑣! = 𝛼 + 𝛽! 𝑣!!! + 𝛽! 𝑃!!! + 𝜓(𝑃!!! × 𝑅! ) where vt equals the Democratic share of the two-party vote in election cycle t, vt-1 equals the
Democratic share of the two-party vote in election cycle t-1, Pt-1 is coded 1 if the winning
candidate in election cycle t-1 was a Democrat and -1 if the candidate was a Republican, and Rt
is coded 1 if an incumbent seeks reelection in election cycle t, and 0 if the incumbent does not.3
in many individual state-cycle combinations, this number is far too low for us to have
confidence in the approach’s results. Further, we have no theoretical reason to suspect that
the effects of full public campaign financing on the incumbency advantage will only occur in
or will be strongest in marginals. Finally, the Gelman and King estimator requires a
parsimonious set of variables. Although we recognize that, were we to live in a world with
better records of candidate quality, election returns, and campaign finance or with more
competitive elections, we may have employed an alternative measure, our choice to use
Gelman and King’s measure best serves our effort to model variation in the incumbency
advantage across states and time.
2
Our results are robust to using the lagged or current winning party, but we prefer the lagged
term since it is clearly exogenous to the dependent variable in this regression (and, as
Engstrom and Monroe 2006 observe, the literature is unsettled on which to prefer).
3
Gelman and King’s model is designed to handle districts in single-member district electoral
systems. Since several states currently use or have used multi-member districts for lower
chamber elections, for the purposes of calculating this indicator of the incumbency
7
In the results of this model, the coefficient 𝜓 can be interpreted as an unbiased measure of the
average incumbency advantage in state n during election cycle t.
We ran this regression using district-level data for the lower chamber of 45 state
legislatures in each non-post redistricting election cycle from 1980 through 2008, using electoral
data from Klarner et al. (2011).4 Following Gelman and King (1990), we included only seats
contested in both elections (t and t-1) in calculating these regressions. As documented in the
Appendix, due to data availability and quality, differences in term length across states, and
differences in redistricting cycles, we were left with differing numbers of cycles across the states
– i.e., unbalanced panels. Additionally, as we will discuss below, we included a lagged term in
our TSCS model, leading us to drop the first two post-redistricting cycles in each state.
Ultimately, this left us with 360 state-cycle observations to analyze. Figure 1 illustrates the
distribution of these estimations of the advantage across cycles by state using box plots and
advantage, we converted all of the non-single member district elections in our data set to
pseudo-districts using Niemi, Jackman, and Winsky’s (1991) method.
4
We excluded the four states (Louisiana, Mississippi, New Jersey, and Virginia) that have offyear state-legislative elections, and Nebraska since it has a non-partisan unicameral
legislature. Our time-series began in 1980 since our preferred measure of legislative
professionalism (the Squire Index) was not available prior to that cycle, and it ended in 2008,
as litigation in Arizona Free Enterprise resulted in matching funds not being available to
candidates in Arizona in 2010. We view the absence of matching funds as a separate
institutional change that requires a different and more tailored analysis than this examination
of full public funding programs as a whole.
8
Incumbency Advantage Estimate
15
10
5
0
AK
AL
AR
AZ
CA
CO
CT
DE
FL
GA
HI
IA
ID
IL
IN
KS
KY
MA
MD
ME
MI
MN
MO
MT
NC
ND
NH
NM
NV
NY
OH
OK
OR
PA
RI
SC
SD
TN
TX
UT
VT
WA
WI
WV
WY
5
State
Figure 1: Distribution of Lower Chamber Incumbency Advantage Estimates by State,
1980–2008, excluding post-redistricting cycles
demonstrates that there is significant variation to be explained across and within the states over
these 28 years.
Constructing a TSCS Analysis
These state-cycle estimates of the incumbency advantage (𝜓!" ) served as the dependent
variable in our TSCS analysis. As mentioned previously, our goal is to explain the variation in
these estimates of the incumbency advantage across and within states and election cycles. Due
to the highly sensitive nature of TSCS models (Wilson and Butler 2007), we detail the modeling
choices, specification tests, and robustness checks that we performed to arrive at our model.
9
First, following Beck and Katz (1995), we employed panel-corrected standard errors
since our sample of cases is roughly our population (the U.S. states), as opposed to more
traditional panel data in which sampled cases are roughly interchangeable. As Beck (2001)
notes, in TSCS, “all inferences of interest are conditional on the observed units” (273) and not an
underlying population, as we cannot resample “new” states.
Second, we included unit effects for states, as well as period effects for election cycles.
In the case of the former, both Hausman and F tests reject the null that these state unit effects are
not needed, and in the case of the latter, an F test comes close to rejecting this same null for the
cycle period effects.5 Including both sets of these effects using a dummy variable approach
lessens the chance that omitted variable bias affects our results.
Third, we used of a lagged dependent variable to address the dynamic nature of the data.
By including this lagged measure, we can interpret the regression coefficients for the remaining
independent variables as capturing the variables’ short-term effects, with their long-term effects
cumulating into the lagged dependent variable, which then allows these long-term effects to
decay exponentially. Theoretically, we believe that this approach best captures the nature of
5
The test results presented in this endnote and footnotes 5–12 are for our first specification, but
the statistical and substantive results of these tests are highly similar across all three
specifications. The Hausman test (run using generalized least squares models with fixed and
!
random effects) results were: 𝜒(!")
= 76.22, p < 0.01; the F test results (run using the reported
!
ordinary least squares model with panel corrected standard errors) were 𝜒(!!)
= 153.01, p <
!
0.01 for the unit (state) effects and 𝜒(!")
= 21.14, p = 0.07 for the period (cycle) effects.
Although we technically could have dropped our period effects given this p-value (and their
inclusion or exclusion does not affect our results), we opted to retain them.
10
dynamic electoral effects (a two-year election-to-election gap in all but a handful of cases), but
nonetheless, we checked the robustness of our findings using three alternative approaches to
modeling dynamics – fixed effects vector decomposition, first differences, and error correction –
and in all three approaches, our central finding for full public funding holds.6
Finally, we addressed for panel-level heteroskedasticity by correcting our standard errors
for it and serial autocorrelation by including an AR(1) correction in the model.7
6
As many of our independent variables are time-invariant or near time-invariant, we first tested
the robustness of our panel results using fixed effects vector decomposition. Although our
finding on our key variable of full public funding held, it had a lower p-value (significant at
𝛼 = 0.10 but not 0.05). We chose not to go forward with this approach, however, because of
continuing debates in the literature about its validity (see, e.g., the contributions to the
Political Analysis symposium on this approach in Spring 2011). Our findings for public
funding also held and were more robust in both a first differences model and an error
correction model (significant at 𝛼 < 0.01 in both). These results are unsurprising, for as Beck
and Katz (2011) note, when a dynamic process has a relatively quick speed of adjustment,
the findings of most TSCS models will be hard to differentiate from one another. The full
results for all three of these alternative models are included in our Supporting Information.
7
To test for panel-level heteroskedasticity, we used a likelihood ratio test and rejected the null
!
hypothesis of homoskedasticity (𝜒(!!)
= 130.39, p < 0.01). To test for serial autocorrelation,
we used Wooldridge’s (2003) test for panel data and rejected the null hypothesis of no serial
autocorrelation (F(1,40) = 19.84, p < 0.01). Repeating these tests on the corrected model
confirmed that these efforts addressed both violations.
11
Having addressed these modeling concerns, we estimated the following Prais-Winsten
regression model, with heteroskedastic panel-corrected standard errors:
𝑦!" = 𝜆𝑦!"!! + 𝛽𝑿!" + 𝛼! + 𝛾! + 𝑢!" ; 𝑢!" = 𝜌𝑢!"!! + 𝑒!"
where, 𝑦!" equals the incumbency advantage in election cycle t, 𝑦!"!! equals the incumbency
advantage in election cycle t-1, Xit represents a vector of independent variables described below,
𝛼! captures our unit (state) effects, 𝛾! captures our period (cycle) effects, and 𝑢!" our error term,
as shaped by its autoregressive component (𝜌). Finally, because our dependent variable (𝑦!" ) is
only an estimate (𝜓) of the incumbency advantage, to deal with underlying uncertainty in its
value, we weighted our observations in our TSCS framework by the number of observations
used to generate each estimate in the Gelman and King regression, which effectively weights the
estimates inversely to the size of their standard errors.
Our independent variable of interest is a binary indicator (Full Public Funding or Full)
that captures whether (1) or not (0) the state had a full public funding program in place during
the electoral cycle. This variable is coded as 1 for Maine and Arizona from 2000 onward and for
Connecticut in 2008. Since public funding was introduced to address corruption and improve
policy, not specifically to increase election competitiveness, we can regard our variable for full
public funding as exogenous to the incumbency advantage and can formally identify the
treatment effect (𝛽!"## !"#$%& !"#$%#& ) – that is, the average effect of a full public funding program
on a state-cycle’s incumbency advantage – as:
𝛽!"## = 𝐄 𝑦!" 𝑦!"!! , 𝛼! , 𝛾! , 𝑿!" , 𝐹𝑢𝑙𝑙!" = 1 − 𝐄 𝑦!" 𝑦!!!! , 𝛼! , 𝛾! , 𝑿!" , 𝐹𝑢𝑙𝑙!" = 0
Testing whether or not this coefficient for full public funding equals 0 provides a direct test of
our hypothesis that full public funding decreases the incumbency advantage; a negative and
statistically significant 𝛽!"## would support our hypothesis.
12
Full public funding programs may not be the only campaign finance reform that affects
the incumbency advantage, however.8 To take into account other potential campaign finance
effects, we used binary indicators to control for: the presence/absence of a partial public funding
program for state legislative candidates, the presence/absence of restrictions on donations from
individuals and organizations to individual candidates, the presence/absence of a disclosure law,
the presence/absence of a ban on soft money donations to political parties, and whether or not
bans existed on independent expenditures by corporations and labor unions. Partial public
funding programs were in place in the following states during the following cycles under
analysis: Hawaii (1986-present), Minnesota (1982-present), and Wisconsin (1980-present). The
data on individual and organizational limits and disclosure laws were provided by Jeffrey Milyo
and David Primo and were coded following the rules in Primo and Milyo (2006); the data on soft
money and independent spending bans came from the National Council of State Legislatures.
Although our naïve expectation is that these reforms would all depress the incumbency
advantage, we recognize that arguments can be made for the opposite expectation. In our first
TSCS specification, we included only these variables. In our second and third specifications,
based upon the existing literature, we controlled for the additional indicators listed below that
might also affect the incumbency advantage at the state-legislative level.
A first set of control variables that we included relates to non-campaign finance
institutional factors, and a second set relates to cycle-specific features. In the institutional
category, we first accounted for the professionalization of the state legislature using Squire’s
(2007) index of professionalism, which is based upon legislator salary, legislature staffing levels,
8
Ideally, we would have included actual campaign spending in our regression model, but these
data are not available for all 45 states over the last 30 years.
13
and time-in-session, and was calculated for 1979, 1986, 1996, and 2003. As is fairly well
established in the existing literature (see, e.g., Carey, Niemi, and Powell 2000 or Berry,
Berkman, and Schneiderman 2000), we expect that as professionalism increases, so too will the
perquisites and electoral advantages of holding office to legislators and, as a result, the
incumbency advantage.
A second institutional factor that we expect to affect the advantage is term length.
Longer term lengths of four years exist for lower chamber members in Alabama, Maryland, and
North Dakota. These terms are double the length of those in the other 41 states analyzed, and
they may allow members more time to establish themselves as incumbents, increasing any
advantages they gain from their position. Others, however, have argued the opposite, stating that
shorter terms ought to increase the incumbency advantage because they increase the frequency of
campaigns and the visibility of incumbents and decrease the likelihood of a quality challenger
emerging in any one election, since the opportunity to run for office comes along more often
(Carey, Niemi, and Powell 2000).
Two factors that we expect to reduce the incumbency advantage are the percentage of
seats elected from true multi-member districts, and whether or not the state was located in the
South. First, in multi-member districts, incumbents are competing with each other for credit
claiming opportunities; the individual incumbency advantage is likely to decrease, as
constituents may experience difficulties in tracing policy/case work outcomes back to the efforts
of a single legislator among the several that may represent them (Cox and Morgenstern 1995;
Carey, Niemi, and Powell 2000). Second, given the electoral shift toward Republicans that
occurred down to the state-legislative level in the South (defined here as the 11 state former
Confederacy) during this time period (Woodard 2006), we suspect that the incumbents in this
14
region, who up to and through the 1990s were largely Democrats, found themselves facing a
more difficult electoral environment over the course of the 28 years under study.
Our second set of control variables relates to economic and political forces that vary from
cycle-to-cycle. These include economic and turnout effects. To control for economic effects,
following Kramer (1983), we included an indicator that captured the national percentage change
in real disposable income between the third quarter of the election year (t) and the prior year (t1), using data from Federal Reserve Bank of St. Louis.9 As has often been observed by those
who explore the link between macro-economic performance and electoral outcomes, we would
expect that as real disposable income increases, so too will the electoral performance of
incumbents. However, it should be noted that past research either has not found this effect at the
state-legislative level (see, e.g., Lowry, Alt, and Ferree 1999 or Chubb 1988) or found it to be
conditional both on membership in the president’s party and the interactive effect of president’s
party and whether or not the candidate was an incumbent (Berry, Berkman, and Schneiderman
2000). Since our estimate of the incumbency advantage is constrained to be equal across the two
parties, this later concern does not factor into our model.
Lastly, we control for changes in voter turnout to capture broader trends in terms of the
composition of the electorate that might affect the overall, and not a party-specific, incumbency
advantage. We included the percentage of the voting age population that turned out to vote in
9
The results presented below for this economic measure are robust to using the percentage
change in national real gross domestic product from third quarter-to-third quarter, to linearly
scaling either of these variables so that 0 represents the worst performance and 1 represents
the best performance, as Berry, Berkman, and Schneiderman (2000) do, and to measuring the
change in income at the state level, as our third specification shows.
15
each election. Specific expectations for turnout are hard to pin down, however: Although we
would expect that increased turnout would reflect an electorate that is not as aware of challengers
for lower-level offices and that this might aid incumbents, a larger electorate might also reflect
the mobilization of new voters who are less familiar with incumbents and thus, less likely to vote
for them due to simple familiarity; such counteractive dynamics are often in play in
congressional elections (e.g., Jacobson 2009).
Regression Results
The results of our regression model are presented in Table 1. Using the estimates
produced by Specification 1, which includes only campaign finance variables, or Specification 2,
which includes all of our independent variables and economic performance measured at the
national level, if we were to set all of our independent variables to their means, our regression
model would predict a mean incumbency advantage for candidates of approximately 3.6
percentage points for incumbents in state lower chambers, which is roughly consistent with but
slightly lower than what previous scholars have found (see, Ansolabehere and Snyder 2002), as
well as about half of the incumbency advantage enjoyed by members of the U.S. House. This
result suggests that the limitations of our data identified above are not biasing our results.
Table 1 also shows that full public funding programs significantly reduce the incumbency
advantage. Across all three specifications in the table, the coefficient for the presence of a full
public funding system (our treatment effect 𝛽!"## ) is negative and statistically significant. That
is, those state-cycle combinations with full public funding systems are associated with a
substantially reduced incumbency advantage. In our first two specifications the incumbency
advantage is just over two points lower, which represents a 56% reduction in the advantage
16
Table 1: Modeling the Incumbency Advantage in State Lower Chamber Elections, 1980–2008
Lagged Incumbency Advantage
Full Public Funding
Partial Public Funding
Individual Donation Limits
Organizational Donation Limits
Disclosure Law
Soft Money Ban
Corporate Spending Ban
Union Spending Ban
(1)
-0.03
(0.06)
-2.04
(0.60)
0.51
(1.20)
1.06
(0.67)
-1.06
(0.80)
-0.26
(1.27)
1.20
(1.09)
-0.96
(0.74)
0.64
(0.89)
Legislative Professionalism
Term Length
Percentage Multi-member
Economic Conditions
(N/A, National, State)
Turnout
South
ρ
State Unit Effects?
Cycle Period Effects?
r2
n
-0.09
Yes
Yes
0.31
360
Specifications
(2)
-0.03
(0.06)
-2.03
(0.59)
0.55
(1.24)
0.97
(0.67)
-1.03
(0.80)
-0.34
(1.25)
1.36
(1.13)
-1.04
(0.78)
0.71
(0.91)
1.67
(3.10)
0.19
(0.59)
-0.01
(0.01)
0.38
(0.23)
0.03
(0.03)
-0.53
(1.12)
-0.09
Yes
Yes
0.31
360
(3)
-0.02
(0.07)
-1.96
(0.59)
0.58
(1.24)
1.05
(0.68)
-1.05
(0.80)
-1.37
(1.55)
1.37
(1.10)
-1.06
(0.75)
0.73
(0.89)
1.34
(3.07)
0.23
(0.62)
-0.01
(0.01)
0.07
(0.05)
0.03
(0.03)
-0.66
(1.38)
-0.09
Yes
Yes
0.31
360
Unbalanced panel model with heteroskedastic panel corrected standard errors and a common
AR(1) process. Dependent variable is the by state-cycle incumbency advantage for state
house/assembly candidates, estimated using Gelman and King’s (1990) approach. Observations
are weighted by the number of cases used in the estimation of the dependent variable. Postredistricting cycles are excluded; see the Appendix for election cycles excluded by state.
17
from the mean predicted value. This finding also holds in our third specification, when we
measure economic performance at the state level: The incumbency advantage drops just under
two-points when we take into account each state’s economic performance, which represents a
54% reduction in the advantage from its mean predicted value. We discuss the likely
mechanisms behind this finding, as well as its implications, further in our general discussion,
which follows our corroboration of this finding via synthetic control methods in the next section.
None of our other campaign finance variables (capturing donation limits, disclosure, and
soft money and spending bans) are statistically significant, although the presence of limits on
individual donations comes close to conventional levels of significance. Additionally, with
exception of economic conditions, none of our other control variables are significant either. For
variables such as legislative professionalism, term length, percentage of multi-member seats, and
the South, the lack of a finding is not terribly surprising, given that they are or are near timeinvariant and that the model includes unit and period effects.10
The significant (p < 0.10) and positive finding for economic conditions further increases
our confidence in our model’s overall performance, given the prominence of economic
performance in models of electoral outcomes. In substantive terms, the effect for changes in
national real disposable income per capita is quite large. A one standard deviation shift (2.09) in
the variable is associated with approximately an 18 percent increase in the incumbency
10
In the fixed effects vector decomposition model mentioned above and included in our
Supporting Information, we retain our central finding for full public funding, and of the timeinvariant or slowly moving variables, only legislative professionalism and percentage multimember are statistically significant.
18
advantage. The effect is smaller (0.39 percent of the two-party vote) but still significant when
income when we measure income at the state level.
As a falsification test of these panel results, we ran a cross-sectional probit regression model
in which we reversed our causal effect, using the lagged value of Incumbency Advantage to predict
whether a state had full public funding program in the current period. This test assessed whether a
state’s imposition of a full public funding was exogenous to the level of its incumbency advantage.
The result of this probit regression revealed that the lagged incumbency advantage was a poor
predictor of a state’s adoption of a full public funding program: it was not only incorrectly signed
but was far from statistically significant (p > 0.89). This test lends credence to our argument that the
adoption and implementation of a full public funding program causes the incumbency advantage to
decrease for elections to the lower chamber of state legislatures.
Taken together, these findings provide strong support for our hypothesis. The model, as a
whole, also explains a fair amount of the variation in the incumbency advantage, with an r2 of
0.31 across all three specifications. Nevertheless, although we believe we successfully isolated
the treatment effect of a full public funding program on the incumbency advantage, in our next
section, we cross-check this specific finding through the use of synthetic control methods.
Applying the Synthetic Control Method to Arizona’s Incumbency Advantage
Synthetic control methods use a data-driven approach to build a counterfactual for a
treated unit. That is, instead of researchers selecting control units to serve as counterfactuals,
this approach uses preintervention data to create a “synthetic” version of the treated unit. As
Abadie, Diamond, and Hainmueller (2010) note, “a combination of units often provides a better
comparison for the unit exposed to the intervention” (494). To construct the synthetic unit, the
approach requires researchers to a) identify predictors for the dependent variable and b) identify
19
a relevant donor pool of units. Using these two sets of information, the approach minimizes the
mean square error in the dependent variable between the synthetic unit and the observed unit in
the preintervention period. After doing so, researchers can compare, postintervention, the
counterfactual trend of the synthetic to the observed (and now treated) unit’s trend to identify
and measure the intervention effect. Abadie, Diamond, and Hainmueller praise the openness of
this approach to counterfactual analysis: “Because a synthetic control is a weighted average of
the available control units, the synthetic control method makes explicit: (1) the relative
contribution of each control unit to the counterfactual of interest; and (2) the similarities (or lack
thereof) between the unit affected by the event… and the synthetic control, in terms of
preintervention outcomes and other predictors of postintervention outcomes” (494).
We employ this technique to analyze the trend in the incumbency advantage for one of
our treated states, Arizona. We chose Arizona, as Connecticut would only provide one postintervention cycle to analyze (2008) and Maine redistricts in cycles ending in four, severely
limiting the amount of data we could use in a synthetic analysis, since the approach requires
balanced panels. Our predictor variables are the same as those in our regression analysis, with
two exceptions. First, we did not include the absence/presence of a soft-money ban since this
applied solely to Connecticut, which, as we discuss below, we eliminated from our donor pool.
Second, we also did not include term length, as the need to balance our panels forced us to
remove states from our donor pool that did not have elections at the same intervals as Arizona.
We did, however, keep North Dakota in our donor pool, as although it has four-year terms, its
elections are staggered.
Our final donor pool consisted of the 22 states listed in column one of Table 2. In
addition to dropping Nebraska, the four states with odd-year elections, and states with non-
20
Table 2: State Weights in the Synthetic Arizona
State
Weight
Alaska
California
Colorado
Delaware
Georgia
Illinois
Indiana
Iowa
Michigan
Minnesota
Missouri
New York
North Dakota
Ohio
Oklahoma
Oregon
Pennsylvania
Rhode Island
Utah
Washington
West Virginia
Wyoming
0.126
0.116
0
0.453
0
0
0
0
0
0
0
0
0
0
0
0
0.067
0
0
0
0.238
0
Note: States not listed were excluded from the donor
pool.
staggered four-year terms, we dropped Maine and Connecticut since they too experienced the
intervention, Kentucky since it entered the time-series late (1984), and the states that experienced
a redistricting pattern different from Arizona, as they would have prevented us from having
balanced panels. Despite these restrictions, our donor pool spanned the U.S. geographically,
socially, and economically and included states that varied considerably on our predictor
variables.
The results of our synthetic analysis appear in Tables 2 and 3 and in the two panels of
Figure 2. Table 2 reveals the make-up of the synthetic Arizona as a weighted combination of
Alaska, California, Delaware, Pennsylvania, and West Virginia. This weighted combination of
21
Table 3: Incumbency Advantage Predictor Means, 1980–1998
Variables
Incumbency Advantage Lag
Partial Public Funding
Individual Limits
Organization Limits
Disclosure Law
Corporate Spending Ban
Union Spending Ban
Legislative Professionalism
Percentage Multi-member
Economic Conditions (state)
Turnout
South
Arizona
Observed Synthetic
2.32
2.27
0.00
0.00
0.57
0.83
1.00
0.90
1.00
1.00
1.00
0.34
1.00
0.10
0.24
0.24
100.00
20.54
1.76
1.82
47.86
49.82
0.00
0.00
Weighted
Average of 42
Control States in
TSCS Model
2.78
0.08
0.57
0.78
0.99
0.32
0.28
0.23
19.62
1.80
53.90
0.12
Note: All variables are averaged for the 1980–1998 preintervention period.
states, based upon the entered predictors, minimized the distance between the incumbency
advantage of our preintervention synthetic and observed Arizona. On average, in the
preintervention period, the distance between these incumbency advantages was -0.12 percentage
points. Panel (a) in Figure 2 illustrates this fit showing the time trend for both units across the
entire time period, demonstrating that the preintervention fit between Arizona and its synthetic
was much tighter than the postintervention fit. To get a better sense of both the magnitude and
direction of this difference, Panel (b) in Figure 2 plots the across time difference (Arizona –
Synthetic) in the incumbency advantage, and although the difference preintervention crosses
back-and-forth around zero, it never strays far from it.
To further assess the performance of our synthetic in the preintervention period, we also
compared the weighted means for the predictor variables across the synthetic and observed
Arizona in Table 3, which also shows the weighted means for these variables among the 42
control states in our TSCS dataset. In general, the differences between the predictor means for
22
6
4
2
0
2
Incumbency Advantage Estimate
Arizona
Synthetic Arizona
1980
1984
1988
1992
1996
2000
2004
2008
Cycle
8
8
4
0
4
Arizona
Control States
12
Incumbency Advantage Difference
(Real Synthetic Advantage)
12
(a)
1980 1984 1988 1992 1996 2000 2004 2008
Cycle
(b)
Figure 2: Panel (a) plots the incumbency advantage in synthetic Arizona and Arizona, 1980–
2008; panel (b) plots the difference in the incumbency advantage (between the actual advantage
and the synthetic advantage) by state, 1980–2008. The vertical lines at 2000 demarcate the
introduction of full public funding for legislative elections in Arizona.
23
observed Arizona and its synthetic are minor; the obvious exceptions are for union spending ban,
corporate spending ban, and percentage multi-member; however, given the weighted means of
these variables among all of the control states, it would have been hard for our synthetic to have
higher (and hence, closer to observed Arizona) values.
Having demonstrated the quality of the preintervention fit, we can examine the
intervention’s effect. Again, we can turn to Figure 2’s panels. In panel (a), we can see that a
significant gap opens up between the synthetic and observed Arizonas in 2000, with the latter
having a lower incumbency advantage in every post-intervention election. This gap captures the
treatment effect of our intervention, that is, the effect of full public funding. Had Arizona not
adopted a full public funding system, we would have expected its incumbency advantage trend to
follow that of its synthetic’s. Instead, in the postintervention period, the incumbency advantage
is, on average, 1.65 percentage points lower in observed Arizona. Although this average drop is
lower than that uncovered by our TSCS model, it is largely consistent with it, and it should be
noted that the TSCS model also included data from the interventions in Maine and Connecticut.
We can also turn to Panel (b) to illustrate the intervention effect. Here, the plot reiterates
a sustained and negative difference between observed Arizona and its synthetic postintervention.
Additionally, Panel (b) plots this difference not just for Arizona but for a set of placebo tests in
which we used the same technique on the 22 control states in the donor panel. That is, we
constructed a synthetic for each state using the same predictor variables, after placing Arizona in
the donor pool and then rotating each state out of the donor pool as we used the method.
Effectively, we gave all 22 states a treatment in 2000 to assess whether our postintervention
difference is capturing something other than the introduction of a full public funding program.
The grey lines in Figure (b) show significant noise in the control states’ trends, with some states
24
experiencing bad fits pre or postintervention and some states in both periods. A few points are
worth highlighting. First, only one state has a consistently lower incumbency advantage
difference than Arizona postintervention: Georgia. Georgia, however did not have a good fit
preintervention, suggesting that the difference between synthetic and observed Georgia
postintervention is unlikely to have been caused by a treatment in 2000. Second, a way to assess
the overall significance of an intervention effect in synthetic control is to calculate the ratio of
the mean square error postintervention to the mean square error preintervention. In the case of
Arizona, that ratio is 6.32; for the 22 states in the donor pool the ratio was 2.06, as there was not
as significant a difference for these states pre- and postintervention as there was for Arizona.
The reason for the smaller ratio in the donor pool is not as important, however, as the fact that
this ratio is 3.1 times greater for Arizona, indicating that a substantively significant shift occurred
in its electoral environment in 2000.
Ultimately, our synthetic control method results corroborate the results for our TSCS
analysis: the incumbency advantage decreased significantly in the wake of the introduction of
full public funding. Across all three states that enacted these programs, the TSCS model
estimates a mean reduction in the incumbency advantage of 2 percent of the two-party vote (a
54% reduction), and the synthetic control method estimates a lower but still consistent drop of
1.65 percent of the two-party vote (a 41% reduction) postintervention in Arizona.
Discussion
Our major finding is that the institution of a public funding program reduces the
incumbency advantage in state legislative elections by half. We demonstrate this through both a
TSCS regression model and synthetic control methods and find consistent evidence that public
25
funding programs trim, on average, approximately two points off of the incumbency advantage
in state lower chamber elections. This is a statistically and substantively significant finding, and
it is robust to numerous alternative models, specifications, and falsification tests. A two-point
reduction in the incumbency advantage cuts it by half, and no other institutional reform or
electoral factor that we examined comes close to demonstrating such an effect. This finding is
in-line with and strengthens earlier findings in the public funding literature (Malhotra 2008;
Mayer, Werner, and Williams 2006), as well as the literature on congressional elections that
shows that challenger spending has a significant effect on vote percentages (Jacobson 2009). We
believe that two non-mutually exclusive mechanisms are behind this result.
First, the wide availability of what we might call “easy money” – that is, funding that is
available to candidates who meet relatively low viability thresholds – likely encourages the entry
of high-quality challengers who now have additional reason to believe that the electoral
environment has turned in their strategic favor (see, e.g., Lazarus 2008 for a game-theoretic
approach to this sort of candidate decision-making process). In fact, this theoretical argument is
buttressed by survey-based evidence that shows full public funding encourages higher-quality
candidates to consider running (Hamm and Hogan 2009).
Second, there is the possibility that the introduction of full public funding belongs to a
narrow category of institutional shocks that can destabilize the competitive equilibrium of an
electoral system. 11 Obviously, we know that candidates alter their behavior in response to
systemic campaign reforms (Miller 2008), and it may well be that, overtime, incumbents will
11
An example of such a shock is the reapportionment revolution, which had an effect strong
enough to permanently change many states’ electoral systems. See, Mayer and Werner
(2007) on such shocks in Connecticut’s legislative history.
26
learn to become more efficient, become better candidates, and learn to leverage their other
advantages in the face of the challengers who now contest races because of the availability of full
public funding. Over time, the incumbent advantage may return to its long-term “equilibrium”
value as incumbents learn and adapt. Although this may eventually occur, through the first
decade of these programs, we can conclude that they have delivered shocks to their electoral
systems that have significantly lowered the advantages of incumbency.
Beyond this central finding, we believe our results can contribute to two broader
campaign finance discussions. First, we worry that the elimination of the matching funds
provisions through the Arizona Free Enterprise decision may deliver a serious blow to the
efficacy of full public funding programs. Since we have only experienced one election since the
demise of matching funds, it is too early to evaluate this claim using the techniques of this paper.
Nevertheless, we believe that Arizona, Maine, and Connecticut should monitor the performance
of their programs from 2010 onward and, if the efficacy of their programs decline, adjust
upwardly their initial grants to keep publicly funded candidates as competitive as possible.
A second discussion we believe this paper contributes to is the efficacy of various
campaign finance reforms and what this means for national-level responses to the Supreme
Court’s decision in Citizens United v. Federal Election Commission, 558 U.S. 50 (2010).
Among the many campaign finance reforms we examined, only full public funding affected the
incumbency advantage. Partial public funding, donation limits for individuals and organizations
and to parties, disclosure, and independent spending bans on corporations and unions all had no
discernable effect on the advantage. These last two findings – that the presence of a disclosure
law and independent spending bans are not associated with the incumbency advantage (in either
direction) – are particularly important in light of the expansion of independently spent “dark
27
money” at the national level in the wake of the Citizens United decision. The identity of donors
need not be disclosed in this category of funds, which includes unlimited donations to 501(c)
organizations, in contrast to the mandatory identification of donors giving more than $250 to
individual candidates, political action committees (including, SuperPACs), or other independent
organizations (e.g., 527s). If our model is correct and its findings can scale up to the nationallevel, then this dark money may not be as problematic as reformers argue. This implication is inline with other research that suggests that the discourse surrounding the effects of the Citizens
United decision may be overblown (see, e.g., Franz 2010 or Werner 2011).
Conclusion
This paper contributes to the extensive literature on the incumbency advantage by
exploring how state-level campaign finance reforms affect the magnitude of the advantage.
Specifically, we found that the introduction of full public funding programs is associated with a
statistically and substantively significant decrease in the incumbency advantage: The advantage
appears to be cut roughly in half in states with such programs.
Ultimately, we see our efforts here as identifying a path forward for reformers in an evertrickier campaign finance environment. We believe our findings to be of substantive import not
only for the on-going debate over the effects of various campaign finance reforms on electoral
competiveness but for discussions regarding the uncertainties introduced by the Supreme Court’s
Arizona Free Enterprise and Citizens United decisions. The evidence presented here, which
relies on data from 45 states over 28 years, suggests that proponents of campaign finance reform,
post-Arizona Free Enterprise, need to ensure such programs maintain their efficacy through
larger lump sum grants and that reformers, more broadly, should note the efficacy of these state-
28
level programs, especially in comparison to other potential responses to the new environment
ushered in by Citizens United.
29
Appendix: State–Election Cycle Availability & Notes
State
AK
AL
AR
AZ
CA
CO
CT
DE
FL
GA
HI
IA
ID
IL
IN
KS
KY
MA
MD
ME
MI
MN
MO
Cycles in
Data Set
9
3
8
7
9
9
9
9
7
8
8
9
9
9
9
9
7
8
3
8
9
9
9
Redistricting
Before
82, 92, 02
94, 02
82, 90, 92, 02
82, 92, 94, 02, 04
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02, 04
82, 84, 92, 02
82, 92, 02
84, 92, 02
82, 92, 02
82, 92, 02
80, 92, 02
84, 92, 02
90, 94, 02
82, 92, 02
78, 84, 94, 04
82, 92, 02
82, 92, 02
82, 92, 02
Notes
4-year terms
Kentucky switched to
even cycles for
legislative races in 1984
4-year terms
30
State
MT
Cycles in
Data Set
9
Redistricting
Before
84, 94, 04
NC
ND
NH
NM
NV
NY
OH
OK
OR
PA
RI
SC
SD
TN
TX
UT
5
9
7
9
9
9
9
9
9
9
9
6
6
6
6
9
82, 84, 92, 02, 04
82, 92, 02
82, 84, 92, 02, 04
84, 92, 02
84, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 02
82, 92, 98, 02, 04
84, 92, 96, 02, 08
80, 84, 92, 94, 02
84, 92, 94, 98, 02
82, 92, 02
VT
WA
WI
WV
WY
6
9
8
9
9
82, 92, 02
82, 92, 02
82, 84, 92, 02
82, 92, 02
82, 92, 02
Notes
Missing 1986, 1988,
1990
4-year staggered terms
Missing 1980, 1984,
1986
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Supporting Information
Table 2: A Fixed Effects Vector Decomposition Model of the Incumbency Advantage,
1980–2008
Lagged Incumbency Advantage
Full Public Funding
Partial Public Funding
Individual Donation Limits
Organizational Donation Limits
Disclosure Law
Soft Money Ban
Corporate Spending Ban
Union Spending Ban
Legislative Professionalism
Term Length
Percentage Multimember
Economic Conditions
(National)
Turnout
South
State Unit Effects?
Cycle Period Effects?
r2
n
Coeff.
Estimate
-0.14
-2.14
1.09
1.15
-1.39
-0.08
1.92
-1.62
1.32
3.59
-0.16
-0.02
0.38
(Standard
Error)
(0.07)
(1.32)
(0.99)
(0.95)
(1.19)
(6.69)
(2.00)
(0.80)
(0.84)
(1.72)
(0.73)
(0.01)
(0.30)
0.04
-0.31
(0.03)
(0.68)
Yes
Yes
0.35
360
Unbalanced panel fixed effect regression model with vector decomposition.
Dependent variable is the by state-cycle incumbency advantage for state
house/assembly candidates, estimated using Gelman and King’s (1990) approach.
Observations are weighted by the number of cases used in the estimation of the
dependent variable. Post-redistricting cycles are excluded; see the Appendix for
election cycles excluded by state.
36
Table 2: A First Differences Model of the Incumbency Advantage, 1980–2008
Full Public Funding (D)
Individual Donation Limits (D)
Organizational Donation Limits (D)
Soft Money Ban (D)
Corporate Spending Ban (D)
Union Spending Ban (D)
Legislative Professionalism (D)
Economic Conditions (D)
(National)
Turnout (D)
State Unit Effects?
Cycle Period Effects?
r2
n
Coeff.
Estimate
-2.29
3.09
-3.86
-1.95
-1.10
2.88
7.49
0.16
(Standard
Error)
(0.93)
(1.32)
(1.58)
(2.44)
(1.62)
(2.25)
(5.74)
(0.19)
0.01
(0.03)
Yes
Yes
0.12
317
Unbalanced panel model with heteroskedastic panel corrected standard errors.
Dependent variable is the first difference of the by state-cycle incumbency
advantage for state house/assembly candidates, estimated using Gelman and
King’s (1990) approach. Observations are weighted by the number of cases used
in the estimation of the dependent variable. Post-redistricting cycles are excluded;
see the Appendix for election cycles excluded by state. All independent variables
were first-differenced (D), but not all variables from the model reported in the
paper have difference terms estimated due to their time invariant nature within a
state.
37
Table 3: An Error Correction Model of the Incumbency Advantage, 1980–2008
Incumbency Advantage
Full Public Funding
Partial Public Funding
Individual Donation Limits
Organizational Donation Limits
Soft Money Ban
Corporate Spending Ban
Union Spending Ban
Legislative Professionalism
Term Length
Percentage Multi-member
Economic Conditions
(National)
Turnout
South
ρ
State Unit Effects?
Cycle Period Effects?
r2
n
Lagged (L) or
Differenced
L
(D)
D
L
L
D
L
D
L
D
L
D
L
D
L
D
L
L
L
D
L
D
L
L
Coeff.
Estimate
-1.05
-2.77
-1.42
-0.27
0.61
1.34
-2.13
-0.96
1.55
2.41
-1.83
-1.34
1.76
1.09
6.41
0.66
2.02
0.01
0.17
-0.27
0.04
0.03
-0.87
-0.09
Yes
Yes
0.58
317
(Standard
Error)
(0.07)
(0.79)
(0.67)
(1.60)
(1.10)
(0.79)
(1.27)
(0.91)
(1.87)
(1.23)
(1.23)
(0.70)
(1.68)
(0.90)
(4.99)
(3.79)
(1.48)
(0.01)
(0.10)
(0.28)
(0.03)
(0.04)
(1.67)
Unbalanced panel model with heteroskedastic panel corrected standard errors and a common
AR(1) process. Dependent variable is the by state-cycle incumbency advantage for state
house/assembly candidates, estimated using Gelman and King’s (1990) approach. Observations
are weighted by the number of cases used in the estimation of the dependent variable. Postredistricting cycles are excluded; see the Appendix for election cycles excluded by state. Not all
variables from the model reported in the paper have both a lag and difference term estimated due
to their slow-moving or invariant nature across time and/or states. Since Disclosure Law was time
and cross-sectionally invariant, coefficients could not be estimated for either a lagged or a
differenced measure of the variable.
38