Do State Campaign Finance Reforms Reduce Public Corruption?
Adriana Cordis
Department of Economics
University of South Carolina Upstate
Jeff Milyo
Department of Economics
University of Missouri
Meg Patrick
Mercatus Center
George Mason University
July 16, 2012
Abstract:
The Supreme Court has long held that campaign finance regulations are permissible for the
purpose of preventing corruption or the appearance of corruption. Yet the implied hypothesis
that campaign finance reforms are effective tools for combating public corruption has gone
essentially untested. We conduct the first systematic evaluation of the treatment effects of
state campaign finance laws on actual corruption rates in the states. We examine within-state
effects of reforms on both convictions and filings in public corruption cases over the last 25
years; overall, we find no strong or convincing evidence that state campaign finance reforms
are in anyway related to public corruption. Earlier research that employs similar methods also
finds little support for the contention that state campaign finance regulations increase public
trust and confidence in government. Together, these results call into question the legal
rationale for campaign finance regulations.
1
Do State Campaign Finance Reforms Reduce Public Corruption?
Adriana Cordis, Jeff Milyo and Meg Patrick
1. Introduction
In the interest of preserving the basic constitutional freedoms of speech and
association, the United States Supreme Court has long held that government restrictions on the
financing of political campaigns must be narrowly tailored for the purpose of preventing “the
actuality and appearance of corruption.”1 This principle has been the basis for several court
decisions that have reigned in the scope of state and federal campaign finance regulations over
the last 35 years.2 For this reason, advocates for new and expanded restrictions on campaign
financing maintain that such reforms are highly effective tools for addressing political
corruption, preserving the integrity of democracy and restoring public confidence in
government.3 Yet, despite this continual and intense focus on campaign finance reform as anticorruption policy, there has been very little effort by scholars to evaluate whether campaign
finance reforms actually reduce corruption or the appearance of corruption.
1
Buckley v. Valeo, 424 U.S. 1 (1976).
2
Recent examples include: Randall v. Sorrell, 548 U.S. 230 (2006), striking low contribution limits in Vermont;
Davis v. FEC (2008), striking differential contribution limits for candidates with self-financing opponents; Citizens
United v. FEC, 130 S. Ct. 876 (2010), striking prohibitions on corporate independent expenditures; Arizona Free
Enterprise Club’s Freedom Club PAC et al. v. Bennett, 131 S. Ct. 2806 (2011), striking public matching funds for
candidates with high-spending opponents; and American Tradition Partnership v. Bullock, 567 U. S. ____ (2012),
which reaffirmed Citizens United application to the states.
3
Examples are ubiquitous, but the New York Times editorial page is a reliable source of hyperbole in this regard; in
the wake of the Citizens United decision, the Times characterized the majority decision as “radical” and striking “a
blow to the heart of democracy” (“The Court’s Blow to Democracy,” 2010). In a subsequent weekly radio address,
President Obama called for campaign finance reform, declaring: “what is at stake is no less than the integrity of our
democracy” (Obama 2010). For recent high profile calls for campaign finance reform as a means specifically to
address political corruption, see the Center for Public Integrity’s “State Integrity Investigation” at:
http://www.stateintegrity.org/ (last viewed July 13, 2012).
2
One explanation for the absence of systematic research on the campaign finance
reforms and corruption is that it is difficult to disentangle the impact of reforms at the federal
level from other factors which may change coincidentally over time. But as demonstrated in
Primo and Milyo (2006) and Milyo (2012), there is substantial variation in state campaign
finance laws both across states and over time; those authors exploit this state-level variation to
identify the treatment effects of campaign finance reforms on public opinion about elections
and government. In addition, a growing literature exploits the existence of state-level data on
public corruption convictions over time to analyze the causes and consequences of corruption
in the states (e.g., Meier and Schlesinger, 2002; Glaeser and Saks, 2006; Cordis, 2009 and Cordis
and Warren, 2012). Consequently, the states offer a laboratory well-suited for identifying the
treatment effect of campaign finance reforms on public corruption.
In this report, we conduct the first systematic within-state analysis of the effects of
campaign finance reforms on actual corruption. We measure public corruption in a variety of
ways using detailed data on both convictions and prosecutorial filings from the Transactional
Records Access Clearinghouse at Syracuse University (TRACfed).4 We also employ multiple
strategies for dealing with the fact that state campaign finance reforms may themselves be
caused by episodes of political corruption. Overall, we find that state campaign finance reforms
are unrelated to state-level convictions or filings in public corruption cases.
2. Literature Review
Only a handful of studies even tangentially examine whether state campaign finance
laws are associated with political corruption in the states. Of these, only Maxwell and Winters
4
We obtained this data under license from TRACfed (http://tracfed.syr.edu/).
3
(2005) use data on actual corruption convictions; however, the authors analyze just a single
cross-section of data, so cannot identify the within state effects of reform. The remaining
studies (Alt and Lassen 2003 and 2008; and Rosenson 2009) instead use Boylan and Long’s
(2003) survey of statehouse reporters to measure state-level corruption. However, the Boylan
and Long survey data is only available for a single year, so these authors are also unable to
identify within-state effects of campaign finance reforms.5
Apart from this, the corruption measures employed in these studies are of dubious
quality. Maxwell and Winters (2005) employ data on convictions from the Public Integrity
Section of the Department of Justice. This is by far the most common source of data on statelevel public corruption employed by social scientists.6 However, Cordis, Milyo and Patrick (in
progress) describe several problems with the DOJ data, from a failure to add-up to inconsistent
and poorly documented data-collection methods. On the other hand, the survey-based
measure of corruption used in other studies is also problematic in that it is based on the
subjective opinions of a small number of journalists. Further, as noted in Cordis, Milyo and
Patrick (in progress), these measures are not highly correlated with the more detailed and
objective corruption data from the TRACfed archive.
5
Stratmannn (2003) examines a single cross-section of 14 democratic countries to analyze the effects of national
campaign finance laws on corruption; he finds more restrictive contribution limits are associated with higher levels
of public corruption, as measured by the Transparency International Bribe Payers Index and the World bank
Corruption Index. This is the only study of which we are aware that investigates the connection between campaign
finance laws and corruption across countries.
6
For example, Adser et al. (2003), Alt and Lassen (2008), Cordis (2009), Dincer et al. (2010), Fisman and Gatti
(2002), Glaeser and Saks (2006), Goel and Nelson (2011), Hill (2003), Johnson et al. (2011), Leeson and Sobel
(2008), Maxwell and Winters (2005), Meier and Holbrook (1992), Meier and Schlesinger (2002), and Nice (1983).
4
It merits mention that neither Maxwell and Winters (2005) nor Alt and Lassen (2003 and
2008) set out to investigate campaign finance regulations as a determinant of reform. In fact,
these authors examine only a single indicator for state campaign finance laws and even so only
in some of their statistical models. The campaign finance regulation variable used in all three
studies describes states with any restrictions on “campaign spending by or on behalf of
candidates”; however, mandatory spending restrictions were rendered unenforceable by the
landmark 1976 Buckley decision. Consequently, these authors really examine only the crosssectional association between voluntary spending restrictions and corruption, absent controls
for other prominent and more relevant features of state campaign finance regulatory regimes,
such as contribution limits for different types of contributors.7
In contrast, Rosenson (2009) undertakes specifically to investigate the question of
whether state campaign finance laws affect political corruption by examining the crosssectional correlation between an index of major state campaign finance laws and statehouse
reporters’ subjective evaluations of corruption in their own state. Rosenson also attempts to
address the potential endogeneity of reforms by using an instrumental variables estimation
procedure. However, this exercise is problematic for two reasons: 1) the first stage regression
does not include all exogenous variables in the structural model, only the excluded instruments;
and 2) the proposed instruments (government ideology, membership in Common Cause and
population) are themselves unlikely to be truly exogenous.
7
Most states with voluntary spending ceilings for candidates offer public financing for candidates that abide by
these limits; however, the indicator used by Maxwell and Winters (2005) and Alt and Lassen (2003 and 2008) also
includes states such as Colorado with purely voluntary spending limits. Further, this indicator does not distinguish
between states that offer public financing to only gubernatorial candidates versus those that also include state
legislative candidates.
5
As a consequence of these shortcomings in both data and methods, the existing
literature is uninformative about whether campaign finance reforms affect public corruption in
the states. However, even putting aside all such concerns, these studies offer no consistent
evidence. Maxwell and Winters observe no significant relationship; Alt and Lassen find a
negative association between voluntary spending restrictions and reporters’ perceptions of
corruption; and Rosenson finds a positive association between state campaign finance laws and
reporters’ perceptions of corruption. However, none of these studies convincingly identifies
the treatment effect of state campaign finance laws on state corruption.
There have been likewise few serious efforts to estimate the causal effects of state
campaign finance laws on the “appearance of corruption,” or similar public-opinion based
measures of trust and confidence in government. In fact, only two studies examine the withinstate effects of campaign finance laws on relevant public attitudes. Primo and Milyo (2006) find
no strong evidence that reforms increase political efficacy, while Milyo (2012) finds no effect of
campaign finance reforms on trust and confidence in government. These studies stand out for
their implementation of “best-practice” evaluation methods, such as estimating treatment
effects via difference-in-differences and performing multiple checks for the presence of timevarying unobservable factors that might confound identification in these models. We now
employ similar empirical methods to the question of whether campaign finance reforms reduce
public corruption in the states.
3. Data and Methods
We seek to evaluate the treatment effect of state campaign finance reforms on the
occurrence of public corruption. An immediate concern is that state campaign finance reforms
6
may themselves be caused by the presence of public corruption. We address this potential
endogeneity in three ways. First, we examine the raw data for any long-run relationship
between the levels of (or changes in) campaign finance laws and the levels of (or changes in)
public corruption in the states. Second, we estimate regressions with state fixed-effects to
sweep out time-invariant unobservables and otherwise mitigate endogeneity bias (e.g. Levitt
1994).8 Finally, we look for trends in state corruption in the years leading up to or just after
episodes of campaign finance reform. These methods are fairly standard in the evaluation
literature; however, our task is complicated by the challenge of measuring public corruption in
the states.
2.1 Public Corruption in the States
As noted above, most empirical research on public corruption in the U.S. employs
convictions data from the DOJ; however, in addition to the problems already mentioned, the
Public Integrity Section does not disaggregate state-level conviction data by type of government
official, nor do they provide state-level breakdowns for cases filed. For these reasons, we
follow Cordis and Warren (2012) and Alt and Lassen (2011) in utilizing the TRACfed data archive
compiled by the Transactional Records Access Clearinghouse (TRAC) at Syracuse University.
TRAC systematically employs the Freedom of Information Act to make available to the public
large quantities of records from various Federal agencies. Information on criminal cases from
the DOJ is available beginning in 1986. Under license from TRAC, we collected data on all
8
In principle we could use instrumental variable methods to address potential endogeneity, but we are at a loss
for credible instruments. Previous studies that consider the determinants of state campaign finance regulations
suggest variables like party control of government (Stratmann and Aparacio-Castillo 2006) or the presence of an
initiative process in the state (Witko 2005); however, party control of government is also a likely determinant of
corruption, while there is too little variation over time in the number of initiative states.
7
convictions and case filings classified by prosecutors as official corruption. From this data, we
created annual series of state level public corruption convictions and filings from 1986-2011.
Figure 1 plots corruption convictions for federal, state and local officials over time.
From this figure, it is apparent that convictions of state officials are relatively rare. So, while
one advantage of TRACfed data is that it allows us to analyze corruption among state officials,
the paucity of such convictions produces some challenges for our subsequent regression
analyses. Figure 1 also suggests that federal prosecutors focus more on corruption among
federal officials than non-federal officials. On the other hand, a recent report from the
Corporate Crime Reporter claims the vast majority of state and local official corruption cases (as
many as 80%) are handled by U.S. district attorneys.9 Even so, not all corrupt activity is
observed or prosecuted, so convictions are at best a proxy for public corruption. We remain
agnostic regarding how best to measure state public corruption and therefore utilize both total
convictions in a state and convictions of only state government officials in our empirical
analysis.
Another advantage of the TRACfed data is the availability of prosecutorial filings in
corruption cases disaggregated by state. Not all corruption can be demonstrated sufficiently in
court to achieve a conviction, so prosecutorial filings give us another proxy for the presence of
state corruption. Further, there is less delay from acts of corruption to filings compared to
convictions (see below). Consequently, we perform all of our statistical analyses using both
convictions and filings.
9
“Public Coruption in the United States,” 2007. Report by the Corporate Crime Reporter to the National Press Club,
available at: http://corporatecrimereporter.com/corrupt100807.htm (last viewed June 25, 2012).
8
In order to compare corruption convictions and filings across states, we normalize these
by the pool of government officials in the state. For example, we examine total official
corruption convictions per 10,000 government full-time equivalent civilian employees
(including employment in federal, state and local government); however, when restricting our
attention to corruption convictions among state officials only, we examine convictions per
10,000 state government full-time equivalent employment (FTEs).
In Figures 2a and 2b, we show how average conviction rates in the states vary from the
1990’s to the 2000’s. For total convictions per government FTE, there is a great deal of
persistence in state-level corruption across all states; this underscores the importance of
controlling for unobserved state-specific time invariant determinants of corruption. In addition
Montana stands out as a particularly corrupt state by this measure (with North Dakota and New
Jersey receiving dishonorable mentions). However, when limiting attention to only state
officials convicted for public corruption, there are many more transitions from low corruption
to high corruption and vice versa across decades. Also, by this measure, it is Illinois, Mississippi,
Tennessee and West Virginia that exhibit the highest persistent levels of corruption. The
differences observed across these two measures of corruption are the primary reason that we
utilize both of these measures of corruption in our empirical investigation.
2.2 Delays in Case Filings and Convictions
The TRACfed data archive also allows us to generate information on the median and
average time from initial referral of a case to filing or conviction. From 1986-2011, the median
time from referral to case filing is 112 days and the average is 260 days; for convictions the
median and average times are 386 days and 556 days, respectively. Consequently, measures of
9
corruption based on filings and convictions generally lead the calendar year in which the
associated corruption occurred. In addition, these data are reported on a fiscal year cycle, so
will lead the calendar year by another 90 days.
In order to identify the effect of changes in state campaign finance laws, it is necessary
to take account of the delay in observing corruption filings or convictions. We address this
complication in several ways. As a first pass, we examine patterns in the raw data over the
course of decades in order to observe slow-moving trends. We then pool our annual data into
five non-overlapping five-year waves; this permits us to examine the effects of state campaign
finance regulations in year t on average corruption convictions and filings for years t through
t+4. However, in order to utilize all of our annual data, we also consider two other strategies.
We use leading averages to construct “adjusted filings” and “adjusted convictions” as a
means to get a better proxy for public corruption occurring in a given state in a particular year.
Based on the observed median and average number of days from referral to filing, we define
“adjusted filings” in year t as the average of filings in years t and t+1. “Adjusted convictions” in
year t are defined as the weighted average of years t through t+3, where the weights are
introduced to account for the observed increase in median and average time to conviction of
about 15 days per year over the 25-year time period.10 Even so, our subsequent regression
results are little changed whether we use this weighted leading average or an unweighted
leading average for adjusted convictions.
10
In 2010, “adjusted convictions” = .75(average convictions in years t through t+2) + .25(convictions in year t); for
each prior year, the weights shift by .01 away from the second term in the sum. We do not use a similarly
weighted average for filings, because we cannot reject the hypothesis of no linear time trend in either the median
or average time to filing.
10
Finally, we analyze unadjusted annual convictions and filings and estimate eleven
separate indicators for each year before and after the implementation of a particular reform
from t-5 to t+5, as well as an indicator for the presence of that same reform for years t+6 and
beyond. We then plot the estimated coefficients and 95% confidence interval for these
indicators; this allows us to easily observe any delayed impacts of reform, as well as evidence of
“reverse causality” from episodes of corruption to reform.
Descriptive statistics for each of the measures of state corruption described above are
listed in Table 1. The paucity of observed corruption among state officials is demonstrated by
the high proportion of “zeroes” for each of our corruption measures (see Panel 2 of Table 1).
Consequently, when analyzing corruption among state officials, we employ a Tobit model (see
below).
2.3 State Campaign Finance Regulations
All data on state campaign finance laws are taken from Milyo (2012), who in turn relied
on several sources, including the National Council of State Legislatures, state government
websites and the Federal Election Commission. As noted in Milyo (2012) and Primo and Milyo
(2006), state campaign finance regulatory regimes fall into five broad and nested types: i) no
contribution limits, ii) limits on corporate contributions to candidates, iii) limits on corporate
and individual contributions to candidates, iv) contributions limits and public funding of
gubernatorial elections, and v) contributions limits and public funding of gubernatorial and
state legislative elections. Therefore, we create a campaign finance index (CFR) that ranges
from 0 to 4, respectively. In addition to this simple index, we also examine the effects of the
11
component laws by employing separate indicators for limits on corporate contributions, limits
on individual contributions and each type of public funding.
Table 2 describes the number of states with each type of campaign finance law, as well
as the average value of the campaign finance regulation index, by decade. Over the last 30
years, there has been a net increase in the number of states with contribution limits, and a
smaller increase in the number of states that employ public funding of campaigns. However,
because some states adopt, repeal and adopt campaign finance regulations over time (e.g.,
California and Missouri), the total number of changes is greater than the net change over time.
2.4 Campaign Finance Reform and Public Corruption: A First Look
In Figures 3a and 3b, we consider the long-run association between average annual
corruption convictions and the average state campaign finance regulation index over the last
twenty years. Since many state campaign finance laws remain unchanged over this time
period, any strong equilibrium relationship should be revealed in this diagram. However, there
does not appear to be a strong negative (or positive) relationship between corruption and
campaign finance regulations, regardless of whether we consider total convictions or only
convictions among state officials.
Figures 4a and 4b compare the change in the average campaign finance index from the
1990’s to the 2000’s to the change in average annual corruption rates from the same periods.
In both figures, it is apparent that among states that did not change their campaign finance
laws, the average change in corruption was about zero. The same is also true for the set of
states that did change their campaign finance laws. These patterns in the raw data do not
suggest that campaign finance reforms reduce public corruption. However, it may be the case
12
that some important determinants of state corruption are spuriously correlated with campaign
finance regulations, masking the true causal relationship. Consequently, we now consider
multivariate models that include controls for potential confounding variables.
2.5 Multivariate Evaluation Methods
We estimate several different versions of linear models of state corruption rates where
the independent variables of interest are indicators for each of the four major types of state
campaign finance laws. All of these models include controls for year and state fixed effects, as
well as controls for state demographics (age, education, ethnicity, income, race, population,
poverty, unemployment and union membership), the state political environment (party control
of state government, legislative term limits, FOIA laws and state government expenditures) and
the number of government FTEs. Definitions and descriptive statistics for all of these control
variables are listed in Table 3. In estimating every model, we adjust standard errors for
clustering by state (Primo et al. 2007; Bertrand et al. 2004).
We use both total corruption rates and rates that include only state officials for our
dependent variable in alternative models. As noted above, our corruption measures for state
officials contain many zero observations. These may be considered either true zeroes, or
instances of censored data. We entertain both possibilities. In the former case, we simply
estimate an ordinary least squares model with state fixed effects. By doing so, we follow the
advice of Angrist and Pischke (2009), who argue that linear estimation is always useful for
estimating marginal effects that have a causal interpretation.11 In the latter case, a Tobit model
can be used; however, including state indicators will render the Tobit estimator biased and
11
We do not use count models, as these non-linear models also do not permit estimation with true fixed effects.
13
inconsistent. Instead, we control for unobserved time-invariant heterogeneity by including a
“starting value”: the sum of convictions from 1976-1982 per 10,000 government FTEs.12
3. Results
In this section we present the results of three different types of multivariate regression
analyses; each with its own strengths and weaknesses. The first analysis examines the effects
of campaign finance regulations on average corruption over five non-overlapping five-year
waves; this is one method of addressing the delay between the occurrence of corrupt activities
and the observation of prosecutorial filings or convictions, but we do lose the statistical power
associated with more observations. The second analysis uses all of the state-year observations,
but employs our measure of adjusted convictions and adjusted filings to address the lag in
observed corruption. The third analysis differs from the second in that we use unadjusted
measures of corruption, rather than our somewhat ad hoc adjusted measures. We address the
time lag in observed corruption by plotting time indicators for several years before and after
the implementation of each type of reform; this also permits us to check for the presence of
time-varying unobserved trends in corruption that may be associated with adoption of reforms.
Other than the number of observations, construction of the dependent variables and the
presence of indicators surrounding episodes of reform, the statistical models examined are
similar across each analysis.
3.1 Non-Overlapping Five-Year Waves
In Table 4 we report the estimated coefficients of interest from the analysis of average
state-level public corruption over five-year waves for both conviction rates (Panel 1) and filing
12
Cordis, Milyo and Patrick (in progress) note that this time period precedes several problems exhibited in the DOJ
data series.
14
rates (Panel 2). Looking at the results in the first column of Panel 1, state campaign finance
laws are neither individually nor jointly significant. 13 This pattern is repeated when we restrict
attention to only state officials and\or employ filing rates as our measure of corruption. As
noted above, neither the linear model nor the Tobit model is fully satisfactory in (2) and (3), so
it is reassuring that these estimates are not dramatically different across the three models.
Ignoring statistical significance, the substantive importance of these estimates is
likewise modest. Consider the coefficient on corporate convictions in (1); the implied causal
impact of limits on corporate contributions to state candidates is a drop in corruption
convictions per 10,000 government employees of 0.04, or about 1/5th of a standard deviation in
that variable. The implied effect of corporate limits on convictions among state officials is
somewhat larger – about 1/3rd of a standard deviation ---, due to the smaller variance in
convictions per 10,000 state government FTEs across states.
Because this model does not differentiate between reforms that have been just
implemented versus those that have been in place for some time, we also estimate the model
using the number\log of years that a particular law has been in place (since 1976) as the
dependent variable; these specifications also yield no significant effects of reforms. Likewise,
we can replace the separate indicators for each type of law with the campaign finance
regulation index, the natural log of that index or even the index squared without altering the
implications of reform on corruption.
3.2 Annual Observations; Adjusted Corruption Rates
13
Of course, the imprecision in these estimates means that we also cannot reject the null hypothesis of some
salutary effect of campaign finance laws on corruption. But neither can we reject the null of a similar perverse
effect of reforms on corruption.
15
In Table 5, we present the results of a parallel analysis, except that we now estimate our
models using all available state-year observations and employ our measures of adjusted
corruption based on four-year leading averages in the role of dependent variable. With only
one exception, we observe no statistically significant effects of state campaign finance laws
(either individually or jointly) across all the model specifications. The lone exception is that
state laws are jointly significant for adjusted filings in column (1) of Panel 2. As before, we also
do not see any dramatic differences in coefficient estimates across models (1) – (3), or between
convictions and filings.
Again ignoring statistical significance, the substantive impact of state reforms is modest
in this analysis, as well. For example, limits on corporate contributions to candidates now
suggest a reduction in total convictions per 10,000 government employees of 0.10, or less than
1/3rd of the standard deviation in this variable. The implied effect of corporate limits is larger
(one standard deviation) when restricting attention to only state officials, again due to smaller
variance in this variable.
As above, we have also estimated these models using the number\log of years that
regulations have been in place, the campaign finance index, the log of that index and its square.
These alternative specifications do not yield any significant effects of state campaign finance
reforms on public corruption.
3.2 Time Trends Before and After Reform
To this point, the only manner in which we have addressed the potential endogeneity of
state campaign finance laws and corruption is through the use of state-level fixed effects. As
noted above, we are not sanguine about the prospects for instrumental variables in this
16
context; therefore, we let the data for itself regarding the presence of any time-varying trends
in corruption before or after episodes of reform.
In order to check for the presence of confounding time trends changes in state
corruption, we re-estimate our models above with a set of time indicators for five-year leads
and lags of a given reform. Each type of state law is examined thusly in a separate regression;
for example, when examining time trends around the implementation of corporate limits, we
estimate the model in column (1) of Panel 1 in Table 5 using unadjusted conviction rates, but
now we include separate indicators for five-years prior to adopting corporate limits, four years
prior, and so on up to five years after the adoption of limits. In addition, we estimate a
common effect for six years out and beyond. We then repeat this exercise for each of the state
laws and for both unadjusted convictions and filings (as well as for state officials only).
Figures 5-8 illustrate the estimated time paths for corruption conviction rates before
and after the implementation of a specific reform, based on the estimated coefficients of the
leads and lags. For example, in Figure 5, we show the time path for convictions for states that
implement limits on corporate contributions. The estimated trend in convictions is shown in
the solid line and the dotted lines indicate the 95% confidence interval. The fact that the
confidence intervals always bound zero indicates that none of the leading or lagging indicators
is statistically significant (nor can we cannot reject the null hypothesis that all of the lead or lag
indicators are jointly zero). Consequently, we are fairly confident that there are no unobserved
trends that confound our estimate of the treatment effect of corporate contribution limits in
this case.
17
Figure 6-9 tell a similar story. And not surprisingly, we observe similar time trends when
filings are used for the dependent variable. In no case do we observe anything like an inverted
V-shape centered on t=0; this alleviates any concern that our fixed-effects models may be
confounded by an endogenous relationship between reform and corruption. Nor do we see
significant effects of any reform after some delay; this further alleviates concerns about the lag
between acts of corruption and convictions (or filings). We don’t even observe significant
reductions in corruption leading up to episodes of reform. All in all, state campaign finance
reforms appear to be completely unrelated to public corruption.
4. Discussion
We conduct the first systematic and comprehensive test of the hypothesis that state
campaign finance reforms reduce actual instances of public corruption. We employ several
modeling strategies to overcome the time delay between acts of corruption and observations
of corruption, as well as addressing the potential endogeneity of reforms and corruption.
Overall, we find that state campaign finance reforms implemented in that last 25 years have no
significant effect on public corruption; nor do we observe any evidence to suggest that longer
standing differences in state campaign finance regulatory regimes yield any reduction in public
corruption.
These findings are consistent with other research that demonstrates an absence of any
treatment effect of state campaign finance regulations on public trust and confidence in state
government (Milyo 2012). And while these findings may be unsurprising to scholars of
American politics, they are wildly at odds with the popular wisdom espoused by many
18
politicians, reform advocates and media pundits.14 Beyond this, the apparent impotence of
campaign finance regulations in ameliorating the “actuality or appearance of corruption” has
dramatic implications for the longstanding legal rationale for all existing campaign finance
regulations. Heretofore, many judges and legislators have considered it self-evident that
restrictive campaign finance regulations are a prophylactic for public corruption; we
demonstrate that this presumption is baseless.
14
The disconnect between the views of scholars of American politics and others is nicely demonstrated in a recent
New York Times news analysis of the effects of Citizens United (Kirkpatrick 2010).
19
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22
Table 1: Public Corruption per 10,000 Government FTEs, 1986-2010
N
Median
Mean
Standard
Deviation
Zero Values
1,250
1,250
0.22
0.26
0.29
0.36
0.32
0.40
15.2%
12.8
250
250
0.25
0.30
0.29
0.36
0.22
0.30
0.8%
0.0
1,150
1,250
0.25
0.28
0.30
0.36
0.34
0.34
2.3%
5.3
1,250
1,250
0.00
0.00
0.11
0.14
0.24
0.31
65.0%
64.4
250
250
0.06
0.07
0.11
0.14
0.14
0.19
34.8%
51.5
1,150
1,250
0.05
0.00
0.11
0.14
0.16
0.24
38.4%
50.6
Panel 1: All Public Corruption
Reported
Convictions
Filings
5-Year Waves
Convictions
Filings
Adjusted
Convictions
Filings
Panel 2: State Officials Only
Reported
Convictions
Filings
5-Year Waves
Convictions
Filings
Adjusted
Convictions
Filings
Note: Adjusted convictions are the average for years t to t+3, so are defined only for the period 19862008; adjusted filings are the average for years t to t+1.
23
Table 2: State Campaign Finance Regulations
1990
2000
2010
Changes
1980-2010
Changes
1986-2008
States with Contribution Limits
Corporate
35
Individual
25
37
28
44
36
44
36
15
17
14
16
States with Public Funding
Gubernatorial
6
Legislative
4
7
3
13
6
13
7
11
7
9
5
1980
Average CFR Index
1.40
1.50
1.98
2.00
50
44
for all 50 states
Notes: CFR Index is the sum of the indicators for each type of law present in a state. Changes include
instances of repeals as well as the adoption of campaign finance regulations.
24
Table 3: Descriptive Statistics for Control Variables (1986-2010; n=1,250)
Mean
Standard Deviation
334,341
80,217
360,403
68,175
State Demographic Controls
% Black
% Other Race
% Hispanic
% Under Age 18
% Age 65 and Over
% High School Degree
% College Degree
% Union
% Poverty
% Unemployed
Log (Real Per Capita Income)
Log (Population)
10.0
6.0
7.3
25.6
12.6
81.8
23.4
13.1
12.9
5.5
10.4
15.0
9.4
9.6
8.7
2.3
2.0
6.5
5.2
6.0
3.7
1.8
0.2
1.0
State Political Characteristics
Unified Control of State Government
Democrat*Unified Control of State Government
Legislative Term Limits
FOIA Index
Log(Real Per Capita State Expenditures)
.42
.24
.26
6.1
8.5
.49
.43
.44
2.5
0.3
Government FTE’s in State
Federal, State and Local
State
Notes: All data on state demographics, government FTE’s and state expenditures are from the U.S
Census. Data on legislative term limits are from the National Council of State Legislatures. The FOIA
index is taken from Cordis and Warren (2012). Partisan control of state government indicators were
obtained from the archive of state data compiled by Carl Klarner at Indiana State University
(http://www.indstate.edu/polisci/klarnerpolitics.htm).
25
Table 4: Effects of the Campaign Finance Regulations (Non-Overlapping 5-Year Waves)
Total
(1)
OLS
State Officials Only
(2)
(3)
OLS
Tobit
Panel 1: Average Annual Convictions per 10,000 Government FTEs (N=250)
Corporate Contribution Limits
-0.04
(0.42)
-0.12
(1.32)
-0.04
(0.88)
Individual Contribution Limits
-0.00
(0.01)
0.07
(0.80)
0.04
(1.01)
Gubernatorial Public Funding
-0.07
(0.71)
-0.03
(0.56)
-0.05
(1.78)
Legislative Public Funding
-0.02
(0.17)
0.05
(0.61)
0.07
(1.35)
No
No
No
Joint Significance
Panel 2: Average Annual Filings per 10,000 Government FTEs (N=250)
Corporate Contribution Limits
-0.00
(0.03)
-0.05
(1.08)
0.03
(0.65)
Individual Contribution Limits
-0.00
(0.02)
-0.00
(0.01)
0.01
(0.25)
Gubernatorial Public Funding
-0.04
(0.35)
0.03
(0.47)
-0.03
(0.88)
Legislative Public Funding
-0.08
(0.65)
0.02
(0.26)
0.02
(0.34)
No
No
No
Joint Significance
Notes: The dependent variables are leading averages from year t to t+4; the independent variables are
from year t. Estimated coefficients and absolute value of t-statistics reported for each model (standard
errors are adjusted for clustering by state). All models include indicators for each 5-year period and
controls for state demographics and political characteristics. The OLS model also includes state
indicators, while the Tobit model instead controls for convictions per government FTE from 1976-1982.
26
Table 5: Effects of Campaign Finance Regulations (Annual Observations)
Total
(1)
OLS
State Officials Only
(2)
(3)
OLS
Tobit
Panel 1: Adjusted Convictions per 10,000 Government FTEs (N=1,150)
Corporate Contribution Limits
-0.10
(1.29)
-0.11
(1.77)
-0.05
(1.03)
Individual Contribution Limits
0.06
(0.68)
0.06
(1.09)
0.05
(1.25)
Gubernatorial Public Funding
-0.07
(0.92)
-0.01
(0.32)
-0.04
(1.35)
Legislative Public Funding
-0.00
(0.06)
0.04
(0.71)
0.06
(1.00)
No
No
No
Joint Significance
Panel 2: Adjusted Filings per 10,000 Government FTEs (N=1,250)
Corporate Contribution Limits
-0.10
(1.24)
-0.05
(1.12)
0.04
(0.52)
Individual Contribution Limits
0.10
(1.23)
0.01
(0.22)
0.02
(0.35)
Gubernatorial Public Funding
-0.09
(1.01)
-0.00
(0.04)
-0.03
(0.82)
Legislative Public Funding
-0.04
(0.51)
-0.03
(0.58)
-0.02
(0.25)
Joint Significance
p<.05
No
No
Notes: The dependent variables are adjusted based on leading averages. Estimated coefficients and
absolute value of t-statistics reported for each model (standard errors are adjusted for clustering by
state). All models include indicators for years and controls for state demographics and political
characteristics. The OLS model also includes state indicators, while the Tobit model instead controls for
convictions per government FTE from 1976-1982.
27
Figure 1:
Public Corruption by Level of Government
0
100
200
300
400
(Source: TRACfed)
1985
1995
2005
Year
Federal
Local
State
28
Figure 2a
Public Corruption in the States:
1.5
Avg. Annual Convictions per 10K Gov't FTEs
2001 - 2010
1
MT
ND
DE
NJ
.5
LA
0
PA HI
VA
AL
MI
AZ
ILCT
NV OK
CA FL
MD MO AK OH
OR
TX
AR
SD INME
GA
NE
WY
NM
SC
UT CO
KS
WI
NC VT
WA
MN
NH IA
ID
0
.2
MS
MA
TN
WV KY
NY
RI
.4
.6
1991 - 2000
Figure 2b:
Public Corruption in the States: State Officials Only
.4
Avg. Annual Convictions per 10K State Gov't FTEs
CT
MS
RI
.3
TN
.2
.1
NE
OR
WI
NV
VT
HI
PA
VA
NC AZ
MD TX
OH
MI
WA
WV
GA
NJ
KS
ID CO
IA
SD
UT
0
IL
AR
NM
MT
AK
0
2001 - 2010
AL
NY
LA
KY
CA
OKDE
FL
MA
IN
SC
MO
ME
MN
NH
ND
.1
.2
1991 - 2000
29
WY
.3
.4
Figure 3a:
Campaign Finance Regulations and Public Corruption
1
Annual Averages from 1991-2010
.8
MT
.6
ND
NJ
MS
.4
TN
PA
CA
AL
MO
TX
IN
.2
VA
IL
OH
NM
OR
UT
CO
ID
KY
CT
WV
AR
AK
GA
OK
WY
SC
NV
SD NE
NC
KS
WA
NH
HI
RI
FL
MD AZ
MI
ME
MN
WI
VT
0
IA
LA
NY
MA
DE
0
1
2
3
Campaign Finance Regulation Index
4
Figure 3b:
Campaign Finance Regulations and Corruption: State Officials
Annual Averages from 1991-2010
IL
.3
MS
TN
NY
WV
KY
.2
LA
MA
AR
GA
CT
RI
PA
AL
NJ
FL
SC
WY
DE
OK
MO
CA
TX
.1
NM
VA
MT
AK
NC
OH
IN
OR
ND
0
UT
0
IA
1
ID
CO
HI
ME
AZ
NE
WA NV
NH
KS
SD
MD
MI
2
3
Campaign Finance Regulation Index
30
WI
MN
VT
4
Figure 4a:
Campaign Finance Reform and Public Corruption
Difference in Annual Avg. from 1991-2000 to 2001-2010
.6
DE
MT
.4
ND
-.2
0
.2
OR
MI
NV
PA
HI
AL
OK
LA
VA
UT
KS
NM
NJ
TX
IL
MD
SD
WI
NH
IN
NC
MS
IA
MA
AK
AR
FL
GA
WY
SC
AZ
WA
MO
CT
TN
OH
CO
VT
ID
NE
ME
CA
MN
WV
RI
KY
NY
0
.5
1
1.5
Campaign Finance Regulation Index
2
Figure 4b:
Campaign Finance Reform and Corruption: State Officials
.4
Difference in Annual Avg. from 1991-2000 to 2001-2010
CT
.2
RI
AL
-.2
0
NM
MT
AK
NE
AR
NJ
VA
OR
MS
NC
MD
NV
WI
GA
TX
PA
KS
MI
HI
IA
SD
OK
UT
IN
DE
WV
FL
MN
NH
ND
IL
TN
WA
LA
NY
SC
KY
MO
OH
VT
AZ
CO
CA
ID
ME
WY
-.4
MA
0
.5
1
1.5
Campaign Finance Regulation Index
31
2
Figure 5:
Effect of Corporate Contribution Limits
-.4
-.2
0
.2
.4
(Estimates and 95% CI)
-5
-4
-3
-2
-1
0
1
Year
2
3
4
5
6
7
Notes: Based on ordinary least squares regression of unadjusted total convictions per 10,000
government FTEs on indicators campaign finance laws, state demographics, state political
characteristics, year and state-fixed effects (standard errors adjusted for clustering within state). The
plot shows coefficient estimates and 95% confidence interval for time indicators from t-5 to t+5 (and a
common indicator for t+6 and onward), where t coincides with the implementation of corporate
contribution limits.
32
Figure 6:
Effect of Individual Contribution Limits
-.4
-.2
0
.2
.4
(Estimate and 95% CI)
-5
-4
-3
-2
-1
0
1
year
2
3
4
5
6
7
Notes: Based on ordinary least squares regression of unadjusted total convictions per 10,000
government FTEs on indicators campaign finance laws, state demographics, state political
characteristics, year and state-fixed effects (standard errors adjusted for clustering within state). The
plot shows coefficient estimates and 95% confidence interval for time indicators from t-5 to t+5 (and a
common indicator for t+6 and onward), where t coincides with the implementation of individual
contribution limits.
33
Figure 7:
Effect Of Gubernatorial Public Funding
-.4
-.2
0
.2
.4
(Estimates and 95% CI)
-5
-4
-3
-2
-1
0
1
Year
2
3
4
5
6
7
Notes: Based on ordinary least squares regression of unadjusted total convictions per 10,000
government FTEs on indicators campaign finance laws, state demographics, state political
characteristics, year and state-fixed effects (standard errors adjusted for clustering within state). The
plot shows coefficient estimates and 95% confidence interval for time indicators from t-5 to t+5 (and a
common indicator for t+6 and onward), where t coincides with the implementation of gubernatorial
public funding.
34
Figure 8:
Effect of Legislative Public Funding
-.4
-.2
0
.2
.4
.6
(Estimates and 95% CI)
-5
-4
-3
-2
-1
0
1
Year
2
3
4
5
6
7
Notes: Based on ordinary least squares regression of unadjusted total convictions per 10,000
government FTEs on indicators campaign finance laws, state demographics, state political
characteristics, year and state-fixed effects (standard errors adjusted for clustering within state). The
plot shows coefficient estimates and 95% confidence interval for time indicators from t-5 to t+5 (and a
common indicator for t+6 and onward), where t coincides with the implementation of legislative public
funding.
35