How Outside Spending Shapes the American Democracy ∗

Nour Abdul-Razzak† Carlo Prato‡ Stephane Wolton§

First draft: August 15, 2016; Current draft: May 17, 2017

Abstract

We study the political consequences of lifting bans on contributions from corporations and unions to groups engaging in outside spending in elections (independent political advertising). We propose a model of electoral competition in which outside spending changes the salience of candidate-specific attributes relative to party labels. Empirically, we employ a differences- in-differences design using federally mandated changes to state regulations following recent judicial rulings in Citizens United and FEC v. SpeechNow.org. We find strong evidence that removing bans on outside spending increases the electoral success of Republican candidates and leads to more ideologically conservative state legislatures. We do not find evidence of an effect on ideological polarization and targeted public good provision. In line with our theory, the effects we identify vary with the local balance of power between corporate and labor interests.

∗We thank Avi Acharya, Chris Berry, Gabriel Carroll, Micael Castanhera, Benoit Crutzen, Bob Erikson, Jim Fearon, Dana Foarta, Anthony Fowler, Shigeo Hirano, Navin Kartik, Jan Zapal as well as conference and seminar participants at MPSA Annual Meeting, Stanford, and Columbia for helpful comments and conversations. Carlo Prato gratefully acknowledges support from the Hoover Institution. Nour Abdul-Razzak gratefully acknowledges support from the National Science Foundation (NSF) Graduate Research Fellowship Program. Any opinions, ﬁndings, and conclusions or recommendations expressed in this material are the authors’ and do not necessarily reﬂect the views of the NSF or the Hoover Institute. †University of Chicago - Harris School of Public Policy. Email: [email protected]. ‡Columbia University. Email: [email protected] §London School of Economics and Political Science. Email. [email protected]

1 1 Introduction

For a great majority of Americans, wealthy special interest groups (SIGs) wield too much power over elections (e.g., Rasmussen Reports, 2016). In practice, SIGs have two broad avenues of influence on electoral outcomes: they can use campaign contributions by transferring resources to candidates or parties, or they can engage in “outside spending” by directly funding independent political communication.1 While campaign contributions have been extensively studied in the literature, outside spending has received far less attention. A comprehensive understanding the consequences of outside spending has become more urgent in the wake of two judicial rulings issued in 2010: Citizens United v. Federal Election Commission (FEC) (558 U.S. 310) and FEC v. SpeechNow.org. In Citizens United, the U.S. Supreme Court ruled that restrictions on contributions to groups engaging in outside spending constitute a violation of freedom of speech, and are thus unconstitutional.2 The lifting of restrictions on outside spending led to a large increase in independent political advertising, which almost tripled (in absolute terms and as a percentage of total spending) between 2008 and 2012 (see Figure 1). This paper investigates theoretically and empirically how outside spending affects the partisanship, ideology, and targeted public good provision of elected officials. Our theory builds on the idea that outside spending changes the salience of local candidates’ attributes (ideology and commitment to targeted public spending) vis-a-vis national factors such as party labels. We find that, as a result of lifting a ban on outside spending, (i) the party aligned with the most efficient interest group should experience an increase in its electoral chances, (ii) the expected ideology of elected officials should move in its direction, and (iii) elected officials’ ideological extremism and targeted public spending should increase only if outside groups’ spending increases candidates’ average salience compared to the pre-ban level. Using data from state legislative elections in 1990-2015, we find robust evidence that the lifting of bans on the sources of funding of outside spending following Citizens United increased the

1Outside spending encompasses independent expenditures and electioneering communication, which are two slightly different categories of political advertising in favor or against a candidate made independently of the candidate or party. Electioneering communication is defined as taking place 60 days prior to a general election (or 30 days prior to a primary election to federal office). 2While the current regulation on outside spending is shaped by both Citizens United v. FEC and FEC v. SpeechNow.org (1:08-cv-00248-JR), the former was the key legal precedent for the latter. Hence, from now on we will refer to the effect of Citizens United as both its direct and indirect effect via SpeechNow.org.

2 Figure 1: Outside Spending in Federal Elections Source: opensecrets.org. The plain line corresponds to outside spending expenditures, excluding not party committees (left axis in millions USD). The dashed line corresponds to outside spending as a percent of total cost of election (right axis).

Republican vote and seat shares and the average ideological conservatism of state legislatures. Con- versely, we find no evidence of an effect on ideological polarization, and no systematic evidence of change in targeted public spending. In addition to a variety of robustness tests, we present prima facie evidence that, consistent with our model’s proposed mechanism, the pro-Republican effect is stronger in states where labor interests are substantially weaker than corporate interests, and weaker wherever the opposite holds true. These results paint a comprehensive picture of how outside spending shapes American democracy. First, Republican candidates have benefited more from relaxing regulations on outside spending, since corporate interests have (according to suggestive evidence) more effectively taken advantage of the new opportunities for influence following Citizens United. Second, in light of our theory, we can interpret the null findings on polarization and targeted public spending as evidence of an increase in the salience of local Republican candidates associated with a similar decrease in the salience of local Democratic candidates. While outside spending is often blamed for the increase in negative campaigning (e.g., Weismann, 2012; Nichols and McChesney, 2012), which tends to produce smaller and more ideologically polarized electorates (Ansolabehere and Iyengar, 1995), our analysis does not lend empirical support for this mechanism. To study the effect of removing restrictions on the funding of outside spending, we employ a tractable and parsimonious game theoretical framework, which features a Republican candidate R,

3 a Democratic candidate D, a representative voter (to whom we reserve the pronoun ‘she’), and two SIGs d and r that favor D and R, respectively. Candidates are office and ideology-motivated. They commit to a level of targeted public good provision, which is costly to secure once elected. Candidates vary in their ideology, modeled as a fixed attribute. The voter values targeted public goods and ideological moderation, but her electoral decision is also affected by aggregate-level factors, such as the relative appeal of the two national party labels. SIGs can engage in outside spending to affect the weight—which we refer to as “salience” (Aragonèset al., 2015; Dragu and Fan, 2016)—that the voter puts on candidates’ characteristics vis-à-visnational factors. The cost of political advertising is assumed to be higher when a ban on contributions from corporations and unions to SIGs engaging in outside spending (henceforth, a ban) is in place. Our theory predicts that after the lifting of a ban, the candidate supported by the most efficient SIG enjoys a higher winning probability, independently of the particular mechanism through which outside spending affects salience. This increased winning probability, in turn, implies that the expected ideology of an elected official moves in the direction of the party who enjoys stronger outside spending. The effect of the lifting of the ban on ideology and targeted public good provision is more nuanced, and depends on both the relative and absolute changes in salience. In our set-up, salience increases the “electoral return” on commitments to targeted public spending. Since more extreme candidates, due to their ideological preferences, have a stronger incentive to be elected, they commit to higher targeted public spending than moderate candidates and win the election with higher probability. An increase in salience exacerbates the differences between extremes and moderates, whereas a decrease mitigates them. Consequently, lifting a ban increases both targeted public spending and polarization (defined as the average ideological extremism of elected officials) only if the average salience of Democratic and Republican candidates does not decrease following the regulatory change. To estimate the effect of outside spending, we exploit state-level variations in campaign finance regulations prior to 2010. Before the Supreme Court’s decision, 23 states enforced a ban on contributions from corporations or unions to groups engaging in outside spending. Citizens United led to a sudden and unexpected elimination of these restrictions. We thus employ a differences-in-differences strategy in which states that never had a ban form the control group.

4 Using direct and indirect evidence, we first establish that in 2010 Republican-leaning interest groups were in a better position to take advantage of the regulatory change. In line with our theory, we find robust evidence that, in the average state legislature, the lifting of the ban resulted in an increase in the share of Republican votes of approximately 3.5 percentage points, and a conservative shift in average ideology of almost a third of a standard deviation. In turn, we do not find evidence of an increase in polarization: the change in ideological extremism between treatment and control is virtually the same. Similarly, we do not find evidence of an effect on targeted public spending. A variety of robustness tests confirms our baseline results implying that the relationships we find are causal rather than spurious correlations. To provide some first-hand evidence on the mechanism we propose, we proxy the strength of labor and corporate interests by (respectively) the share of union membership and firms’ regulatory exposure (provided by Fouirnaies and Hall, 2016). Consistent with our theory, the benefit of lifting the ban for Republicans is greater than the baseline effect when corporate interests are relatively stronger than labor interests, and closer to zero when the opposite is true.

Our theoretical framework is related to a large literature on the consequences of interest groups’ involvement into electoral politics. Our set-up builds on two approaches in the literature. As in models of persuasive political advertising (Klumpp, 2014; Feddersen and Gül,2014), we assume that SIG spending always benefits candidates. As in models of informative political advertising (Grossman and Helpman, 2001 Chap 6; Prat, 2002; Coate, 2004; Ashworth, 2006; Meirowitz, 2008; Prato and Wolton, 2016a), the electoral consequences of campaign spending depend on candidates’ policy commitments and attributes. In order to build a tractable model of outside spending, we combine insights from several recent contributions.3 First, we build on Aragonèset al.’s (2015) model of endogenous salience (see also Dragu and Fan, 2016). Second, we represent ideology as a fixed attribute (Besley and Coate, 1997; Galasso and Nannicini, 2011). Third, we model targeted public spending as contingent on effort provision, a common assumption in the democratic accountability literature (e.g., Ashworth and Bueno de Mesquita, 2009; Galasso and Nannicini, 2011; Prato and Wolton, forthcoming).

3To our knowledge, only Prato and Wolton (2016a) and Klumpp (2014), explicitly model outside spending. Both papers focus on imperfect information in policy-making, and reach mostly normative conclusions. Our focus on salience allows us to obtain a richer and largely non-overlapping set of positive implications.

5 A few empirical studies use time-series variation in state regulation of direct contributions to study SIG influence on legislators’ ideology (Barber, 2016) and electoral fortunes (Hall, 2016). Our paper studies similar outcomes, as well as targeted public good spending, while focusing on a different channel of SIG influence. It also significantly expands upon a few previous works on the impact of regulatory changes on outside spending, which look at partisan government control, incumbency, and corporate taxation (Werner, 2011; La Raja and Schaffner 2014). Empirically, this paper builds on Klumpp et al. (2016), who employ a similar design to study the consequences of Citizens United on Republican winning probability, incumbency advantage, number of candidates, and campaign contributions. In addition to proposing a novel theory of outside spending, we complement and expand their analysis in several directions. First, we study legislators’ ideology, polarization, and targeted spending. Second, we perform all our baseline analyses at the state level, consistently with our treatment. This also has the advantage to avoid any issue associated with redistricting. Third, we run a variety of robustness tests that are of both econometric and substantive importance. Fourth, we uncover important heterogeneity in the treatment effects which are informed by our theoretical framework.4

2 Background on federal and state regulation

Since, 1947, corporations and unions have been banned from directly spending general treasury funds in federal electioneering communication (Taft-Hartley Act). In 1974, Congress imposed strict limits on contributions and campaign expenditures, with spending restrictions overruled by the Supreme Court in Buckley v. Valeo (424 U.S. 1). When issuing its ruling, the Supreme Court made a distinction between “express advocacy,” explicitly supporting the victory or defeat of a candidate, and “issue advocacy,” which only endorses a certain policy position. Issue advocacy, according to the Supreme court, was protected by the First Amendment, and the FEC was only allowed to regulate express advocacy.

4In a working paper recently made available, Harvey and Kaslovsky (2017) perform a similar analysis as Klumpp et al. (2016). In addition, they also look at the effect of outside spending on ideology, but confine their analysis to state legislative districts that changed their representative in 2010. Doing so, they find radically different results than ours, which can possibly be attributed to the selection bias in their sample.

6 Congress did not propose a major overhaul of campaign finance regulations until 2002, with the Bipartisan Campaign Finance Reform Act (BCRA). The law was an attempt to address the use of “soft money” (i.e., unlimited contributions to party for the official purpose of party building— legally, a form of issue advocacy) as a vehicle for circumventing restrictions to contributions in the 1990s and early 2000s. In an effort to prevent similar bypassing tactics, the BCRA also prohibited the funding of electioneering communications (ads aired in the 60 days before a general election that mention federal candidates) by corporations, unions, or non-profit groups. This last provision quickly became the target of several legal challenges. In 2007, the Supreme Court’s ruling on FEC v. Wisconsin Right to Life (551 U.S. 449) established that restrictions on electioneering communication (as long as not used for express advocacy) by non-profit organization were unconstitutional. In the same year, the conservative non-profit group Citizens United chal- lenged the decision by the FEC to prohibit the airing of a documentary opposing then presidential candidate Hillary Clinton. The resulting case Citizens United v. FEC and subsequent Supreme Court’s decision in January 2010 removed restrictions on the use of corporations and unions’ treasury to fund groups engaging exclusively in outside spending. All contribution limits for outside spending were lifted a few months later by the U.S. Court of Appeals for the District of Columbia Circuit in FEC v. SpeechNow.org. These rulings not only affected federal regulation, but also state campaign finance laws. As stated by Justice Stevens in his dissenting opinion (page 7) “The Court operates with a sledge hammer rather than a scalpel when it strikes down [BCRA regulation on outside spending]. It compounds the offense by implicitly striking down a great many state laws as well.” Prior to Citizens United, 23 states had bans on corporations or unions’ funding of outside spending. Table A.1 in La Raja and Schaffner (2014) highlights that the introduction of these bans spans over a century (see Figure 4, which reports latest changes) and clusters around major nation-wide events: (i) the early 20th Century, with the rise of the Progressive movement, (ii) the mid 1970s, in the aftermath of the Watergate scandal, and (iii) the late 1990s-early 2000s (around the BCRA). By the end of March 2010, more than half of these 23 states had officially removed their restrictions. By November 2010 all states (with the possible exception of New Hampshire) had complied with the new regulation (see Table 10 in Appendix). It is therefore reasonable to conclude

7 that for the purpose of our analysis these 23 states were “treated” from 2010 on (we nonetheless perform robustness tests excluding New Hampshire).

3 Theoretical framework

Following a long tradition in the literature, our model focuses on two aspects of representation: ideological extremism and the direct provision of beneﬁts to constituents.5 In addition to a representative voter, our model features two state-level candidates R and D, a representative voter, and two special interest groups (SIGs) d and r that favor D and R, respectively. Candidates value oﬃce for intrinsic (ideology) and instrumental (‘ego’ rent) reasons. Candidate

J ∈ {D,R} is characterized by an ideology parameter θJ , which at the beginning of the game is his

private information. It is common knowledge (without much loss of generality) that θR is drawn from a uniform [0, 1] and θD is drawn from a uniform [−1, 0]. Candidates also commit to a level of targeted public good provision (examples include securing funds for housing projects, the rejuvenation of industrial sites, or local infrastructure), denoted by y ∈ [0, y]. Once in office, a legislator’s marginal cost of local public good provision is k ∈ [0, 1].6 We assume that the direct benefit of being in office for a candidate is given by 1 − ky, while his ideological payoff depends on his ideological distance from the elected candidate e ∈ {D,R}. It can be represented by following utility function:

uJ (y, θ) = I{e=J}(1 − ky) − |θe − θJ |

After observing candidates’ ideology and proposed targeted public good provision, the voter elects one of the two candidates, denoted e ∈ {D,R}. Her payoﬀ from electing a candidate is increasing in his proposed public good provision and decreasing in his ideological extremism (i.e., voter’s ideology is θV = 0). Her electoral decision also depends on an “aggregate partisan tide,”

5Both dimensions are of positive and normative relevance: targeted spending is a widely employed measure of legislative accountability (Snyder and Strömberg, 2010; Anzia and Berry, 2011), ideological extremism and polarization have been shown to adversely affect economic performance (Azzimonti, 2011 and 2016). 6The assumption k ≤ 1 guarantees that an extreme candidate can propose a sufficiently high y to convince the voter to elect him against a moderate candidate without necessarily making the value of holding office negative. When k > 1, an extreme candidate would always prefer an ideologically close politician to hold office, which makes the presence of candidates with extreme ideology in the pool hard to justify.

8 which takes the form of a random shock ξ to her payoﬀ from electing candidate R, drawn from a

1 1 uniform [− 2ψ , 2ψ ]. While the voter places a constant weight, normalized to 1, on the partisan tide,

her payoﬀ from candidate J is scaled by a factor αJ ∈ [α, α], which is aﬀected by outside spending.

Using the language in Aragon`eset al. (2015), αJ captures the salience of candidate J. Salience thus captures the extent to which a campaign primes voters towards candidate-speciﬁc attributes (ideology and proposed spending) relative to national-level factors. The voter’s utility function from electing candidate J ∈ {D,R} assumes the following form:

uV (yJ , |θJ |,J) = αJ (yJ + 1 − |θJ |) + I{J=R}ξ,

where the indicator function I{J=R} equals to 1 if J = R and 0 otherwise. The constant 1 ensures that an SIG has no incentive to decrease the salience of his preferred candidate: higher salience always beneﬁts a candidate. It is important to stress that (i) the beneﬁt of higher salience depends on candidates’ attributes and (ii) SIGs spending can decrease the salience of the opposing candidate.

SIG j ∈ {d, r} can engage in outside spending, denoted aj, to manipulate candidate’s salience

αJ . We suppose that the cost of outside spending depends on the regulatory environment. It is prohibitively high under a ban on contributions from corporations and unions (in which case

j ar = ad = 0) and equal to c (aj) otherwise. In the absence of a clear empirical foundation, we remain agnostic about how spending aﬀects salience, and simply assume that salience can be

represented as αJ = A(aj, a−j), increasing in aj, decreasing in a−j, and such that A(0, 0) = α. 7 Observe then that under a ban both candidates’ salience equals αJ = α, J ∈ {D,R}. Absent a ban, the salience of candidates can diﬀer as a consequence of SIGs’ strategies. Each SIG j ∈ {d, r} cares about the electoral success of candidate J, and its preferences can be represented by:

j j u (aj) = I{e=J} − c (aj)

To summarize, the timing of the game is:

1. SIGs d and r choose their level of outside spending;

2. Nature draws candidates’ ideology: θD and θR; 7Notice that this is equivalent to assuming that groups face the same cost function under a ban and play a symmetric strategy.

9 3. Candidates observe αD, αR, and their own ideology;

4. Candidates choose a level of local public good provision y ≥ 0 (henceforth, a platform);

5. The voter observes candidates’ commitments, ideology, salience;

6. Nature draws the national tide ξ, and the voter elects a candidate;

7. The game ends and payoﬀs are realized.

The equilibrium concept is Perfect Bayesian Equilibrium. As customary in probabilistic voting models, we impose parametric restrictions on the space (ψ, α, α, y, k) to ensure that the problem is well-behaved.8 Before proceeding to the analysis, we stress that SIGs choose their outside spending before candidates’ ideologies and platforms are determined. This assumption captures the legal requirement that SIGs do not coordinate with candidates (for a discussion on this point, see Heineman, 2012) and matches the qualitative evidence collected in Klumpp et al. (2016) indicating that groups’ outside spending strategy is decided long before the electoral campaign. Crucially, it also distinguishes this model from existing theories of electoral competition with endogenous campaign spending.

3.1 Analysis

Let yJ be the level of commitment to targeted public good provision by candidate J ∈ {R,D}. The

voter elects candidate R if and only if αR(yR +1−θR)+ξ ≥ αD(yD +1−|θD|) (recall θD ≤ 0). Given the voter’s behavior and the distribution of ξ (realized after candidates choose their platforms), the probability that candidate J ∈ {D,R} wins the election when his opponent (denoted −J) promises

y−J and has ideology (or type) |θ−J | is:

1 pJ (y; |θ|, |θ−J |) = + ψ αJ y + 1 − |θ| − α−J y−J + 1 − |θ−J | (1) 2 | {z } | {z } Payoﬀ from candidate J Payoﬀ from candidate −J

8Speciﬁcally, the restrictions guarantee that (i) for each proﬁle of platforms and ideologies, candidates’ winning probabilities are interior and (ii) for each ideology level, candidates’ platform choices (y) are interior. See the Appendix for details.

10 Since his opponent’s ideology is his private information, J must take into account all possible types: at the time of his platform choice, candidate J solves the following maximization problem:

max θ pJ (y; |θ|, |θ−J |)(1 − ky) − |θ − θ−J | 1 − pJ (y; |θ|, |θ−J |) (2) y E −J

Intuitively, candidate J considers how a change in y affects (i) his winning probability (pJ ), (ii) his office payoff conditional on being elected (1 − ky), and (iii) the ideological extremism of his opponent conditional on being defeated (|θ − θ−J |). We can now study how candidates’ strategies depend on their ideology. Our first result establishes that more extreme candidates commit to higher levels of public good provision, denoted by

∗ yJ (θ) (see Figure 2a for an illustration).

∗ Lemma 1. yJ (|θ|) is strictly increasing in |θ|.

While an extreme candidate is all things equal electorally disadvantaged against a more moderate candidate, he has a stronger incentive to make himself more appealing, since he experiences a larger ideological loss from losing (|θ − θ−J | increases in |θ|). Due to candidates’ strategic provision of targeted public good (Lemma 1), it is a priori unclear whether in equilibrium the voter prefers an extreme candidate or a moderate one. In this model, however, the higher commitment to targeted public good provision more than compensates for the

∗ ∗ ideological distance. Denoting pJ (θ) := pJ (|θ|; yJ (|θ)|) J’s equilibrium winning probability as a function of his ideology, we obtain:

∗ Lemma 2. pJ (|θ|) is strictly increasing in |θ|.

Since ideological moderation and public spending are perfect substitutes, more extreme candidates— due to their higher ideological cost from defeat—more than compensate their primitive disadvantage with public good commitments, generating a higher payoﬀ for the voter (αJ (1 + y − θ)) than moderate candidates (Figure 2c). This, in turn, implies that an extreme Republican is more likely to win than a moderate Republican against all types of Democrats, and that both are more likely to defeat a moderate Democrat than to defeat an extreme Democrat, as illustrated in Figure 2c. Using the previous two lemmas, we can now examine how lifting a ban on corporations and unions’ contributions to SIGs engaging in outside spending shapes electoral outcomes and candi-

11 θR=3/4

0.5 Probability R wins Targeted spending Voter's policy payoff θR=1/4

0 0 0.5 1 0 0.5 1 0 0.5 1 R's ideology ( R) R's ideology ( R) D's ideology (| D|) (a) Targeted public good (b) Voter’s payoﬀ from (c) R’s winning probability spending candidates’ attributes

Figure 2: Equilibrium under a ban ∗ ∗ The quantity represented in Figure 2a is yR(θR). The quantity represented in Figure 2b is EξuV (yR(θR), θR,R). The quantity represented in Figure 2c is pR(yR(θR); θR, |θD|) for θR = 1/4 (long dashed line) and θR = 3/4 (plain line). Parameter values: k = 1/3, ψ = 1/8, α = α = 4/5, α = 1, y = 3.

dates’ behavior. Since SIGs choose their spending strategy under imperfect knowledge of candidates’ ideology, they try to maximize their preferred candidate’s ex-ante winning probability. Under a ban

(αD = αR = α), the two candidates have the same expected ideological extremism and thus the same ex-ante winning probability. Without a ban, SIG j ∈ {d, r} wants to maximize (resp., minimize) the voter’s evaluation of its preferred candidate (resp., its opposed candidate) by manipulating candidates’ salience. As the next proposition shows, this problem reduces to maximizing the diﬀerence between candidates’ salience.

Proposition 1. Candidate J’s ex-ante winning probability is strictly increasing in αJ − α−J .

By Proposition 1, if a SIG has a cost advantage (e.g., cj(a) = δc−j(a), δ < 1 for all a ≥ 0), then its preferred candidate’s equilibrium winning probability is strictly greater than 1/2, independently of the specific mechanism through which outside spending affects salience. The increased winning probability of the candidate associated with the most efficient SIG has a direct effect on the ideology of the average elected official.

Proposition 2. Absent a ban, elected oﬃcials are on average more conservative than under a ban

if and only if αR ≥ αD (strictly if αR > αD), and strictly more liberal otherwise.

One could further expect that the lifting of a ban increases polarization as extreme candidates provide a higher payoﬀ to the voter. This intuition, however, turns out to be only partially correct. The impact of the lifting of a ban on polarization depends on absolute and relative changes in

12 salience. To match available data, we deﬁne polarization as the average extremism (absolute value of ideology) of an elected oﬃcial:

E ∗ ∗ θ = E{θRpR(θR, θD) + |θD|pD(θR, θD)}

∗ where pJ (θJ , θJ ) denotes candidate J’s equilibrium winning probability when his ideology equals θJ and his opponent’s equals θ−J . The eﬀect of lifting a ban on polarization operates through public good provision since the success of extremist candidates is inherently tied to it (Lemma 1). It is thus useful to deﬁne the expected public good provision as:

E ∗ ∗ ∗ ∗ y = E{yR(θR)pR(θR, θD) + yD(θD)pD(θR, θD)}

Critically, changes in salience (both in a candidate’s own salience and in his opponent’s) differentially affect extreme and moderate candidates’ incentives to commit to targeted public good provision. Suppose, for instance, that the salience of both candidates increases after the ban is lifted. This raises the importance of candidates’ ideology and platforms in the voter’s evaluations of her political options. As a result, all candidates propose higher levels of targeted public good provision. However, within each party, the increase is more pronounced for more extreme candidates as these candidates have a stronger incentive to avoid a defeat. Extreme candidates’ commitment to targeted public good provision is thus more responsive to salience than their moderate counterparts’, which exacerbates their electoral advantages. Consequently, an increase in both candidates’ salience causes an increase in public good provision and polarization. Things become more subtle when only the salience of one candidate increases, whereas the other candidate’s decreases. On the one hand, the lower salience reduces the electoral return from −J’s targeted public good provision. On the other hand, the higher salience of J creates an electoral disadvantage for −J, who then has incentive to offer a more appealing platform. The first effect dominates whenever the increase in αJ is relatively small compared to the decrease in α−J so that both polarization and average public good provision decrease as a result. Indeed, a substantial decrease in candidate −J’s salience generates a discouragement effect: his commitment to public good decrease. J is then more secure electorally and does not need to propose higher level of public

13 good despite the heightened importance of his attributes: yJ decreases and so does polarization. Proposition 2 summarizes these results.

Proposition 3. Absent a ban,

αR+αD (i) polarization is higher than under a ban if and only if α ≤ 2 (ii) there exists α(α , α ) ≥ αR+αD such that expected targeted public spending is higher than under b R D 2 a ban if and only if αD and αR satisfy α ≤ αb(αR, αD).

Figure 3 summarizes how changes in salience affect polarization and targeted public good provision. The main difference between the two figures is that an increase in average salience is necessary

but not suﬃcient to increase targeted public spending (in other words, the threshold αb is larger than

(αR + αD)/2). This interesting diﬀerence results from the strategic complementarity in candidates’

targeted public good commitments. A decrease in yD relaxes competitive pressures on R and tends to marginally reduce his incentive to propose targeted transfers, which in turn diminishes further D’s commitment. Hence, it is not suﬃcient for average salience to remain constant for expected public good provision to remain constant after the lifting of the ban.

(a) Eﬀect on polarization (b) Eﬀect on targeted public good provision

Figure 3: Changes in polarization and targeted public good provision Parameter values: k = .91, ψ = 1, α = α = .42, α = .56, y = .49.

Our theoretical framework establishes two distinct sets of predictions. On the one hand, the lifting of a ban should have a clear eﬀect on winning probabilities and average ideology because its impact only depends on relative changes in salience. On the other hand, the implications for polarization and targeted public spending should be more nuanced, because they depend on both

14 absolute and relative changes in salience. In order to derive clear implications from Propositions 1 and 2, it is enough to know which party is supported by the most efficient SIG. In order to derive clear implications from Proposition 3, it is necessary to know the effect of outside spending on salience. While some conjecture that Citizens United has effectively allowed candidates to outsource negative advertising—which should reduce salience—our theory cannot generate sharp predictions without making somewhat arbitrary assumptions. In the remaining of the paper, we use Proposition 3 to provide context for our estimates and a way to interpret them. This, however, does not imply that our theory is not empirically falsifiable. Indeed, it is inconsistent with a large increase in polarization without a parallel increase in public spending (Proposition 3).9 In the next sections, we empirically evaluate these theoretical predictions, and provide some prima facie evidence consistent with the mechanism we posit.

4 Empirical strategy

4.1 Preliminary considerations

To identify the effect of outside spending on electoral outcomes and politicians’ behavior, we take advantage of the state-level variations in campaign finance regulation prior to 2010 (see Figure 4). Twenty-three states had a ban in place and were forced to change regulations. In our differences-in- differences strategy, they constitute the treatment group. The 25 other states form the control group (throughout we exclude from the analysis Nebraska, which has a non-partisan unicameral legislature, and Louisiana, which elects its representatives via nonpartisan blanket primaries). Information on state-level bans on funding of outside spending were kindly provided by La Raja and Schaffner and complemented by our own research (see Table 10 for more details). Table 1 summarizes changes in outside spending for state-level races after 2010. Consistent with the findings in Spencer and Wood (2014), we document a significant increase in outside spending in the treated states (by 70%—65% per capita), and only a moderate increase in control states (by 18%—14% per capita).10 Further, and in line with the evidence presented in Klumpp et

9Similarly, our theory is not compatible with a large increase in the winning probability of Republicans without any change in the chamber’s average ideology (Propositions 1 and 2). 10This last increase, which might be due to spillover from federal-level races, would tend to bias our estimates downward.

15 Figure 4: State campaign ﬁnance regulation before Citizens United Map is reproduced from Klumpp et al. (2016). Years in parentheses indicate the year the ban was implemented.

al. (2016), groups supporting Republican candidates experienced a significantly larger spending increase compared to groups supporting Democrats. (Democrat and Republican levels are based on targeted ads and differ from the total which also includes issue advocacy and ads aimed to influence ballot measures.) By ruling out that Citizens United had no effect on state-level outside spending, Table 1 provides preliminary evidence that outside spending increased differentially across parties and across treatment and control groups. These results, however, should be interpreted with caution for three reasons. First, only 20 states have some form of disclosure requirements (7 from the control group and 13 from the treated one).11 Second, states differ in their disclosure requirements (e..g, nine states—AR, ME, MA, MI, MN, MO, TN, TX, and WI—do not require disclosure of advertising spending in the weeks before the election, or only under restrictive conditions). Third, spending decisions alone are endogenous to a variety of potential confounders (e.g., the distribution of competitive districts, the cost of advertising).

11The states are: AK, AZ, CA, CO, CT, FL, IA, ID, MA, ME, MI, MN, MO, NC, OH, OK, TN, TX, VA, WA.

16 2006-09 2010-12 Change Total 218.25 / 2.80 257.96 / 3.20 +18% / +14% Control (N=7) Republican SIG 45.23 / 0.58 62.56 / 0.78 +38% / +34% Democrat SIG 77.63 / 0.14 97.26 / 0.35 +25% / +21% Total 78.07 / 0.83 133.23 / 1.36 +70% / + 65% Treatment (N=13) Republican SIG 12.88 / 0.14 33.96 / 0.35 +163% / +155% Democrat SIG 27.07 / 0.29 36.4 / 0.37 +37% / +30%

Table 1: Outside spending in 20 states: total / per capita Source: followthemoney.org. Aggregate ﬁgures are in millions USD; per capita in USD.

Nonetheless, in light of Table 1 and Propositions 1 and 2, we expect that the removal of bans should favor Republican candidates and lead to more conservative state legislatures. Table 1, however, provides little insight about the impact of these regulatory changes on salience. Hence we do not have a strong prior on the effect of lifting bans on polarization and targeted public good provision. A fundamental concern regards the exogeneity of the treatment (i.e., the treatment must not be correlated with trends in treated states). During the hearings of Citizens United v. FEC, the justices of the Supreme Court only considered the constitutionality of a ban on the funding of outside spending for federal elections. While Justice Stevens’ dissenting opinion foresaw the consequences of the ruling for state-level legislation, state-level regulation was not part of the matter of the case before the Court. Consequently, we can be confident that the treatment did not coincide with any state specific change that could influence our outcomes of interest. While the timing of the treatment can be considered exogenous to state-level outcomes, the presence of a ban is hardly random since it depends on past state-level decisions. This is not a concern as long as the implementation of ban was due to some time-invariant factors. Selection into treatment becomes a threat to identification only if two conditions are met: (i) factors affecting to the adoption of a ban (e.g., the strength of local SIGs) have evolved differently over time in treated and control states and (ii) these same factors are correlated with our outcomes of interest (Republican winning probability, legislators’ ideology, targeted public spending). The discussion in Section 2 about the timing of the introduction of these bans only partially mitigates these concerns. We address them in three different ways. First, we provide indirect evidence that trends in the variables of interest were parallel in both sets of states in the years prior to Citizens United. Second, our preferred specification includes state specific time trends, which weakens the assumption

17 required for identification. Third, we examine the stability of our estimates under the introduction of leads of the treatment (see Section 7). Through historical research, we also find evidence that many of these spending bans were intro- duced for reasons that are not explicitly partisan. For example, in 2002 over 66% of Colorado voters supported a ballot initiative banning outside spending by corporations and unions (in addition to other campaign finance reforms) despite the opposition of both party leaders (Colorado Campaign Finance, 2002; Hall 2013; Booth 2002). Similarly, in 1996 the Alaska legislature reformed the state’s campaign finance laws in order to preempt a ballot initiative aimed at achieving the same goal. According to the proponents of the initiative, many citizens believed that “after candidates got elected they ’went bad’ or ’became corrupt’ or ’got crooked’ or ’went on the take’ and began accepting contributions and favors from the interests they were supposed to regulate” (State of Alaska v. Alaska Civil Liberties Union), and “the constant refrain [...] from citizens was that the Legislature was owned by special interests.”

4.2 Electoral outcomes

We first consider the effect of outside spending on election outcomes using state election returns compiled by ICPSR and purchased from Klarner Politics. Our dependent variable is the Republican share of state-wide votes in a chamber, state, and year denoted by RepV Sst. We also report results for the share of seats that went to a Republican in state s and year t, denoted by RepSSst. We consider all elections from 1990 to 2015 (because data are aggregated at the state level, redistricting is not a concern for our estimation). Our baseline specification is given by:

RepV Sst = βCitUnt × BanStates + γs + δt + st (3)

CitUnt takes value 1 for the post-2010 elections and 0 otherwise, BanStates takes value 1 if state

s had a ban on funding of outside spending. Equation 3 also includes state (γs) and year (δt) ﬁxed

effects. The inclusion of these two fixed effects subsumes the effect of BanStates and CitUnt which

therefore do not need to be included in (3). The coeﬃcient of CitUnt × BanStates captures the eﬀect of lifting a ban on contributions from corporations and unions to groups engaging in outside spending.

18 4.3 Representatives’ ideology

We use two measures of ideology: the NPAT score, compiled by Boris Shor and Nolan McCarthy (2011), and the DIME score, compiled by Adam Bonica (2014). The NPAT score is generated using a roll-call based strategy similar to Poole and Rosenthal’s (1997) NOMINATE score, complemented by survey results from the Project Vote Smart National Political Awareness Test for compara- bility across chambers, states, and time. The DIME score, instead, is based on direct political contributions flowing to candidates. The two measures have different advantages and shortcomings. On the one hand, the NPAT is time-invariant and provides a unique (average) score for a legislator’s tenure, whereas the DIME score is term-specific. On the other hand, NPAT is less vulnerable than the DIME contribution- based measure to SIGs’ possible substitution from contributions to outside spending post-Citizens United (this is especially problematic if moderate groups are more likely than extreme groups to substitute outside spending from contributions). Even though (i) most of the variation in Bonica’s data comes from individual contributions and (ii) regulatory changes do not seem to have a strong or significant effect on contributions (Kumpp et al., 2016), this remains a potential concern. We thus use the NPAT score as our preferred measure. While both measures are available over a longer time-periods, in our main specifications we restrict the sample to the period 2000-2014 in order to increase the likelihood that the parallel trend assumption is satisfied (see Figure 6). First, we look at the effect of outside spending on a chamber’s

12 average ideology (AvgIPst), with higher scores indicating a more conservative legislature. Our baseline speciﬁcation is as follows:

AvgIPst = βCitUnt × BanStates + γs + δt + st (4)

To measure ideological polarization, we follow Barber (2016) and use the average absolute value

NPAT score of all legislators in state s at year t, AbsIPst (again dropping independents). Our

12 Due to the structure of the data, in the NPAT sample we define the CitUnt dummy slightly differently: Since 2010 scores refer to candidates in office in 2010 and thus elected in previous electoral cycles, CitUnt takes a value of 1 starting in 2011.

19 baseline speciﬁcation is then:

AbsIPst = βCitUnt × BanStates + γs + δt + st (5)

In the Robustness section, we report results for an alternative measure of polarization: the share of moderate legislators in a given state-year.

4.4 Targeted public good provision

To look at the effect of outside spending on targeted public good provision by state legislators, we use state intergovernmental transfers to local governments. These transfers, which account for 35-40% of all state government spending, are compiled from the US Census State and Local Government Finance (SLGF) database. We consider total transfers as well as itemized transfers covering 9 different categories: education, highways, general local government support (state aid applied at the discretion of the receiving government), health and hospital, transit, housing and community development, public welfare, sewerage, and other (a residual category). While originally available at the local government level, in our main specification we aggregate this measure at the state level. Given the level of aggregation, we do not distinguish between lower and upper chambers (both would produce the same result). Data are available every year for the period 1990-2008, and for 2012.13 While this approach is consistent with previous empirical studies of state legislator’s effort in securing discretionary spending, our dependent variable is an imprecise measure of targeted public good provision. On the one hand, our data only includes funds transiting through local governments and not direct spending, which underestimate legislators’ efforts in securing funds. For example, funds secured in order to build a state prison in a legislator’s district (with positive implications for local employment) would not be included in our data set. On the other hand, due to overlapping jurisdictions, multiple politicians might claim responsibility and benefit electorally from the same expenditures, which might overstate the effect a legislator’s effort. While no alternative data source

13We were unable to obtain aggregated yearly state intergovernmental data between the years 2008-2012 from Census.

20 overcomes these limitations (see Ansolabehere and Snyder, 2006 for a discussion), Gosling (1985) documents that legislators make use of these transfers to provide tangible beneﬁts to their district.14

Equation 6 describes our speciﬁcation: the dependent variable Yst is the log of (one plus) total transfers or itemized transfers in 2012 US dollars.

Yst = βCitUnt × BanStates + ρP opst + γs + δt + st (6)

4.5 Weakening the parallel trend assumption

Finally, we complement the baseline specifications described in Equations 3-6 by adding two specific time trends. First, to account for a differential trend in voter partisanship, we include a “Deep South” time trend (Alabama, Georgia, Mississippi, South Carolina, and Florida). Second, to relax the assumptions required for identification, we also run all regressions with state specific time trends.

5 Empirical Results

Table 11 reports summary statistics (mean and standard deviation) for our dependent variables. Republican seat shares are slightly higher in states with spending bans. Further, states with spending bans have more extreme state legislators (for both parties in both chambers). For about half of the transfer categories, these states also receive more transfers.

Republican vote and seat share

The trends in Republican vote and seat share for the lower chamber in control (no ban) and treated (ban) states are illustrated in Figure 5.15 Variations in both sets of states are relatively similar, which is consistent with the parallel trend assumption.

14To study the impact of Citizens United on targeted transfers, one could also use yearly state governmental expenditures. This variable, however, is a less accurate proxy of a legislator’s effort than a revenue-based measure, because not all IG allocated transfers are spent, and sometimes spending happens with substantial delays. Further- more, expenditure measures could include a greater share of formula-based transfers, by definition unrelated to state legislators’ effort. 15Trends are shown for the years in which both states with and without spending bans held elections. Since only states without spending bans have elections during odd years, those are not included in the figure.

21 (a) vote share (b) seat share

Figure 5: Trends in average Republican vote and seat share for the lower chamber

Tables 2 and 3 present the estimates from Equation 3. While our lower chamber baseline specification points to positive but not statistically significant increase in the Republican seat and vote shares (Column 1), the inclusion of state specific time trends (Column 3), leads to a coefficient that is double in size and statistically significant. Column 2 suggests that Deep South states account for most of the difference, as these states did not have a ban and were trending Republican over the time period considered. Results using data from upper house are very similar. The implied magnitude of the effect is substantial: lifting a ban corresponds to a 11.5% increase the Republican seat share (that is, over five seats for every hundred state legislative districts) and to a 7.2% increase in the Republican vote share (that is, 3.5 more percentage points in vote share). In both cases, the effect exceeds a third of a standard deviation (using Column 3). To put these results in context, the victory margins was smaller than 3.5 percentage points in one in every ten races in our sample.

Ideology

As Figure 6 illustrates, control and treated states do not seem to experience the same trends in ideology before 2000. In the analysis, we thus restrict our sample to the years 2000-2014. Due to the presence of a few visually noticeable differences in trends in the post-2000 period, including state specific trends is crucial. Table 4 suggests that both chambers became on average more conservative following the lift of a ban on the source of funding of outside spending. Again, magnitude and statistical significance of

22 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep VS Rep VS Rep VS Rep VS Rep VS Rep VS

CitUn×BanState 0.019 0.037* 0.035** 0.034 0.045* 0.036* (0.019) (0.019) (0.015) (0.024) (0.023) (0.020) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 606 606 606 564 564 564 R-squared 0.815 0.841 0.919 0.682 0.690 0.791 Robust standard errors are clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 2: Eﬀect of Citizens United on Republican vote share

Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep SS Rep SS Rep SS Rep SS Rep SS Rep SS

CitUn×BanState 0.025 0.051 0.052** 0.054 0.076* 0.050 (0.036) (0.037) (0.026) (0.046) (0.045) (0.032) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 606 606 606 564 564 564 R-squared 0.827 0.846 0.933 0.702 0.712 0.821 Robust standard errors are clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 3: Eﬀect of Citizens United on Republican seat share the results improve after the inclusion of state speciﬁc trends (Column 3). These results suggest that lifting a ban leads to an increase in conservatism of almost a third of a standard deviation. Table 22 in the Appendix shows similar results (with slightly larger magnitudes and smaller standard errors) when using the contribution-based DIME measure.

23 (a) lower chamber (b) upper chamber

Figure 6: Trends in average ideology

Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP

CitUn×BanState 0.042 0.065* 0.095*** 0.063 0.091* 0.095* (0.035) (0.038) (0.035) (0.049) (0.050) (0.051) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 668 668 668 663 663 663 R-squared 0.960 0.962 0.983 0.933 0.937 0.969 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 4: Eﬀect of Citizens United on average ideology (NPAT scores)

Polarization

Unsurprisingly, polarization exhibits similar features as ideology (Figure 7). The parallel trend assumption is violated prior to 2000 (which are thus excluded from the analysis) and noticeable difference in the period 2000-2014 make it necessary to include state specific time trends. Table 5 suggests that removing bans on outside spending has no detectable effect on ideological polarization. The coefficients are generally negative, very small in magnitude, and very far from any conventional levels of statistical significance. Tables 25 and 26 in the Appendix show similar results when using the DIME data. In light of our theory and the rest of the evidence presented,

24 (a) lower chamber (b) upper chamber

Figure 7: Trends in polarization (absolute value of NPAT)

Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Abs IP Abs IP Abs IP Abs IP Abs IP Abs IP

CitUn×BanState -0.006 -0.001 -0.001 -0.031 -0.029 -0.007 (0.032) (0.033) (0.025) (0.034) (0.034) (0.027) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 668 668 668 663 663 663 R-squared 0.945 0.946 0.984 0.930 0.930 0.976 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 5: Eﬀect of Citizens United on polarization (absolute value of NPAT) this suggests that the increase in the salience of Republican candidates has been associated with a similar reduction in the salience of Democratic candidates.

Intergovernmental transfers

In this subsection, we examine the eﬀect of Citizens United on targeted public good provision, measured by intergovernmental transfers. Figure 8 provides visual evidence consistent with the presence of parallel trends. This suggests that our baseline (and more parsimonious) speciﬁcation is appropriate for (at least) total transfers.

25 Figure 8: Trends in Total transfers

Figure 9 shows point estimates and 95% confidence intervals obtained from our baseline specification for the effect of lifting a ban on total transfer and the various itemized categories. For total transfers, as well as all but one category of spending (Highways), the treatment effect is not statistically significant, close to zero and in some cases even negative. We further explore the results on highways in Figure 10 and Table 6. Columns (1) and (2) indicate that the lifting of a ban increases highway transfers by about 30%. However, the effect goes to almost zero (and loses significance) after the inclusion of state specific trends. This suggests that our parallel trends assumption is violated, as illustrated in Figure 10. As such, this deeper analysis confirms the overall message of this subsection. Outside spending does not not seem to have any effect on any form of targeted transfers (modulo the caveats raised above regarding our outcome variable). This broad pattern is confirmed by a district-level analysis (details available upon request).16

16The district level analysis cannot fully account for redistricting due to the fact that the earliest post-Citizens United year covered in our data is 2012.

26 Figure 9: Effect of Citizens United on intergovernmental transfers Solid dots represent the point estimates of the baseline specification, and the lines the 95% confidence interval (not correcting for multiply hypothesis testing). All estimates have robust standard errors clustered at the state level and are obtained using the baseline specification Equation 6.

Figure 10: Trends in Highways

27 (1) (2) (3) VARIABLES Ln(Highways) Ln(Highways) Ln(Highways)

Citizen × Ban 0.306** 0.287** 0.077 (0.137) (0.133) (0.275) State and Year FE XXX Deep South Trend X State Speciﬁc Trends X

Observations 882 882 882 R-squared 0.914 0.914 0.958 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 6: Eﬀect of Citizens United on Ln Highways State Transfers

6 Heterogeneous eﬀects

6.1 Relative strength of labor and corporate interests

Our empirical results robustly demonstrate that Republican candidates have benefited electorally from the deregulation of corporations and unions’ funding to outside spending groups. This result is in line with our theoretical predictions, given the evidence collected in this paper and by Klumpp et al. (2016) that Republican-leaning interest groups have reacted more to the change in regulation. This conclusion is further confirmed by evidence that state legislatures have become on average more conservative (Proposition 2). Proposition 1 further implies that these effects should be stronger (resp. weaker) in states where corporate interests are relatively strong (resp. weak). We test this prediction by exploiting variation across states in the relative strength of corporate and labor interests. To measure union strength, we create the dummy variable Union, which equals 1 when the pre-2010 union density in the state is above the median, with the expectation that the treatment effect should be weaker in states with high union density. We approximate the strength of corporate interests by computing an industry-weighted index of exposure to regulation, using data kindly provided by Hall and Fouirnaies (2016).17 As with union strength, we create a dummy variable Corp, which equals 1 if the pre-2010 state-specific weighted

17See Appendix for more details on the construction of this variable.

28 regulatory exposure is above the median. (The correlation between Union and Corp is only 0.12.) While Corp is a highly imperfect measure of corporate strength, we expect the treatment effect to be larger in states with low regulatory exposure (that is, Corp = 0). This is motivated by Hall and Fouirnaies’ (2016) finding that “firms exposed to more government regulation distribute their campaign contributions in a more access-seeking manner than do other firms, allocating more of their contributions based purely on incumbency status and not on the basis of ideology, district type, or other political factors” (page 2). This conclusion suggests that corporations are less aligned with Republicans when highly exposed to regulation. In light of the many possible confounders (e.g., corporate interests more vulnerable to regulation may have a stronger incentive to influence the political process), this exercise should only be interpreted as a prima facie assessment of the mechanism we posit. In Table 7, we consider again the effect of lifting a ban on Republican’s vote (VS) and seat share (SS) in state legislatures. For appropriate comparison, columns (1) and (3) reproduce our baseline specification with a Deep South Trend, for the years 1994 onward (Hall and Fouirnaies’ regulatory exposure data are not available prior to 1994). Columns (2) and (4) includes our two dummy variables and their interactions with the treatment variables. The coefficients all have the expected sign. In states where unions are weaker and corporations are more aligned with the Republican party, the effect of lifting the ban is more than twice our baseline estimate (almost 8 percentage point when considering vote share and almost 13 percentage points when considering the share of chamber seats). Conversely, in states in which unions are stronger and corporations are less aligned with the Republican party (that is, Corp = 1), the effect of lifting the ban is less than half of our baseline estimate and (for the vote share) not statistically different from zero. Table 8 reports heterogeneous effects for chamber’s average ideology using the NPAT score. Columns (1) and (3) again report our baseline estimation with a deep South time trend for the years 2000-2014. Columns (2) and (4) include the new dummy variables and all interactions. As can be observed, the sign of the coefficients and their implied magnitude mirror those of Table 7. In states where unions are weaker and corporations are more aligned with the Republican party, the average conservative shift in the chamber’s average ideology is more than twice our baseline estimate. In the Appendix, we perform the analysis with the DIME data and find substantially the same effects (Table 27).

29 Lower Chamber Upper Chamber (1) (2) (3) (4) (1) (2) (3) (4) VARIABLES Rep VS Rep VS Rep SS Rep SS Rep VS Rep VS Rep SS Rep SS

CitUn×BanState 0.036** 0.078** 0.047 0.129** 0.040* 0.134** 0.062 0.257*** (0.017) (0.035) (0.035) (0.050) (0.021) (0.054) (0.041) (0.063) · · · ×Union -0.047 -0.037 -0.098 -0.166** (0.044) (0.064) (0.060) (0.079) · · · ×Corp -0.052 -0.174 -0.118 -0.272** (0.059) (0.104) (0.086) (0.128) · · · ×Union×Corp 0.036 0.083 0.088 0.124 (0.070) (0.125) (0.094) (0.143) State and Year FE XXXXXXXX Deep South Trend XXXXXXXX

Observations 468 468 468 468 435 435 435 435 R-squared 0.885 0.891 0.865 0.878 0.733 0.752 0.745 0.774 F-statistic p-value 0.180 0.024 0.103 0.001 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 7: Effect of Citizens United on the Republican vote and seat share Columns 1 and 3 show the baseline effect with the modified time frame. Columns 2 and 4 include Union, Union × CitUn, Corp, Corp × CitUn, Corp × Union, Corp × CitUn × Union. The F-statistics report test of the null hypothesis of joint zero values of all four coefficients.

Lower Chamber Upper Chamber (1) (2) (3) (4) VARIABLES Avg IP Avg IP Avg IP Avg IP

CitUn×BanState 0.065* 0.157** 0.091* 0.262*** (0.038) (0.076) (0.050) (0.096) · · · ×Union -0.082 -0.207* (0.085) (0.108) · · · ×Corp -0.182 -0.270** (0.118) (0.130) · · · ×Union×Corp 0.157 0.230 (0.135) (0.150) State and Year FE XXXX Deep South Trend XXXX

Observations 668 668 663 663 R-squared 0.962 0.966 0.937 0.945 F-statistic p-value 0.073 0.081 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 8: Heterogeneous effect of Citizens United on average ideology (NPAT scores) Columns 1 and 3 show the baseline effect with the modified time frame. Columns 2 and 4 include Union, Union × CitUn, Corp, Corp × CitUn, Corp × Union, Corp × CitUn × Union. The F-statistics report test of the null hypothesis of joint zero values of all four coefficients.

30 6.2 Changes in ideology by party

We also consider the impact of Citizens United on the ideology of elected Democrats and Repub- licans separately. In the Appendix (Proposition 4), we provide necessary and suﬃcient conditions under which the lifting of the ban increases candidate J’s ideological extremism and targeted public

∗ spending conditional on being elected (E{|θJ ||J = e} and E{yJ (θJ )|J = e}). Consistent with the results summarized in Proposition 3, candidate J’s targeted spending and ideological extremism increase if and only if his salience increases while his opponent’s does not decrease too much. See Figure 11 for an illustration.

Figure 11: Eﬀect of lifting a ban on extremism and targeted public good provision

Empirically, we calculate the average ideology in a chamber of all legislators of party p ∈ {R,D}

in state s and time t (dropping independents), AvgIPpst. In addition to state and time ﬁxed eﬀects,

our most flexible specification also includes all interactions between the treatment variables (CitUnt and BanStatet) and Repp, a dummy equal to 1 for the Republican party, to allow for differential party trends and state effects. We thus run the following baseline regression:

AvgIPpst = αRepp + φCitUnt × BanStates + ψCitUnt × BanStates × Repp + γs + δt + pst (7)

In Equation 7, the coefficient φ captures the effect of lifting a ban on outside spending on the ideology of Democratic legislators, φ+ψ captures its effect on the ideology of Republican legislators.

31 It is important to stress that the variable Repp is affected by our treatment. The effects we identify thus encompass new Republican legislators replacing representatives from the same party as well as taking over districts previously held by Democrats. The combined intuition from our model and our previous estimates suggests that the increase in the salience of Republicans should increase their extremism and the decrease in salience of Democrats should decrease their extremism. If, contrary to our theory, moderate Democrats are simply replaced by moderate Republicans, one should observe an increase in extremism among Democrats and a decrease in extremism among Republicans. Table 9 displays our estimates. Overall, evidence point to both Democrats and Republicans becoming more ideologically extreme and so do not permit to adjudicate between the simple replacement hypothesis and our theory. The magnitude of the estimates, however, suggest the presence of a dampening force on the replacement effect.18 A more rigorous decomposition is unfortunately unachievable with the data available. It should be noted that the magnitude and statistical significance of our estimates are significantly weakened by the inclusion of party-specific time trends (compare Columns 1-2 and Columns 3-4). This indicates that the overall trend in polarization in American politics (McCarty et al., 2016) explains most of the estimated effect.

Table 23 in the Appendix shows similar results when using the contribution-based DIME measure. Taken together with our previous estimates, our analysis suggests that lifting bans on outside spending does not have strong detectable eﬀects on legislators’ ideological extremism.

7 Robustness tests

In this section, we discuss several robustness checks. First, in Tables 13 and 14 in Appendix C, we augment Equation 3 by the leads of the treatment variable. If pre-2010 trends are parallel, the coefficient on the lead treatment should be zero and the coefficient on the treatment variable should be unchanged. We indeed find that this is true.19 This analysis suggests that our treatment effect cannot be attributed to the heterogeneity in the dynamics of partisanship across states.

18If the most moderate 5% of the Democratic state representatives were to be removed, Democrats’ average ideal point would decrease by almost .20 units, or four times the estimated effect. 19For our purpose, it is enough that the lead treatment is not statistically significant after the inclusion of state specific time trends (or our Deep South trend). All analyses, however, yield substantively the same results.

32 Lower Chamber Upper Chamber (1) (2) (3) (4) (1) (2) (3) (4) VARIABLES Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP

CitUn×BanState -0.134** -0.149*** -0.051 -0.062* -0.119* -0.113** -0.053 -0.017 (0.061) (0.037) (0.084) (0.032) (0.067) (0.046) (0.088) (0.048) · · · ×Rep 0.223** 0.253*** 0.058 0.054 0.164 0.154** 0.032 -0.038 (0.111) (0.054) (0.160) (0.061) (0.113) (0.062) (0.159) (0.069) State and Year FE XXXXXXXX Rep XXXXXXXX Rep × Ban XXXX Rep × Citizen XXXX State Speciﬁc Trends XX

Observations 1,336 1,336 1,336 1,336 1,326 1,326 1,326 1,326 R-squared 0.915 0.915 0.916 0.918 0.914 0.914 0.916 0.919 F-statistic p-value 0.104 0.000 0.613 0.037 0.210 0.040 0.444 0.364 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 9: Eﬀect of Citizens United on average ideology by party (NPAT scores) The F-statistics reported are testing the null hypothesis of joint zero values of Rep×CitUn×BanState and CitUn×BanState.

Second, we perform placebo tests for the analysis of the Republican seat share and chamber ideology. Figure 12 (coefficients can be found in Appendix C) displays point estimates and 95% confidence intervals as we change the date of the treatment (x-axis) in our preferred specification (which includes state specific time trends). The resulting estimate is statistically significant only for the 2009 placebo in the lower chamber (since only a handful of states in the control group hold elections in odd years, the coefficient captures the same variation as our treatment). We perform similar tests for average ideology. Figure 13 displays placebo point estimates and 95% confidence intervals for average ideology in both chambers with state specific trends. Estimates are negative for the lower chamber in years 2005, 2006 and 2007. This suggests that prior to 2010, legislatures in treated states were becoming more liberal due to reasons not accounted for in our specifications. Our results indicate that the lifting of outside spending bans have fully reversed this trend. Our identification strategy can also be threatened by other nationwide events that were contem- poraneous with Citizens United and had an independent effect on our outcomes of interest. One possible confounder is the Redistricting Majority Project (REDMAP). REDMAP is an electoral strategy designed by the Republican State Legislative Committee (RSLC) in 2009 to gain control of

33 (a) lower chamber seat share (b) upper chamber seat share

Figure 12: Placebo tests for Republican seat share

(a) NPAT, lower chamber (b) NPAT, upper chamber

Figure 13: Placebo tests for Ideology, NPAT

key state legislatures and dominate the redistricting process following the 2010 Census.20 Doing so, the Republican party targeted several states in our treatment group (and a few in the control group), and this targeting might be the source of the Republican gains we capture in our analysis.21 Based on the information found in official documents, we create a dummy variable (REDMAPs) which equals one for states in which REDMAP spending exceeded USD 1M in 2010.22 The estimated coefficients of our treatment variable remain virtually unaffected (see Tables 18-20). We also consider the impact of Citizens United at the district level. In practice, we replicate the analysis in Klumpp et al. (2015) with a few minor differences (see Appendix C for more details).

20Previous research, however, has suggested that the REDMAP strategy would not have been possible before Citizens United, because of the nature of the RSLC (a 527 group) and their use of corporate funding (Klumpp et al., 2016). 21See redistrictingmajorityproject.com for details on the plan and its execution. 22Results are robust to creating a dummy variable for receiving any REDMAP spending.

34 Because of redistricting issues, we limit the analysis to 47 states (excluding North Carolina) in the period 2002-2010. We find that the lifting of a ban is associated with an increase of 4 to 6 percentage points in Republican winning probability (statistically significant only for the lower chamber), which echoes our state-level results (Table 21). Since the analysis of polarization does not yield statistically significant results, it is important to explore how robust our result is to alternative measures of polarization. Following Hirano et al. (2010), we use the share of ideologically moderate legislators (we define a moderate legislator as being in the lowest decile of absolute value NPAT scores—see the Appendix for details). Table 24 in the Appendix shows that the removal of a ban has negative, but mostly statistically insignificant effects on the share of moderate legislators. This further supports our claim that Citizens United did not contribute to the increase in state legislative polarization observed in recent years. For intergovernmental transfers, we correct standard errors by adjusting for multiple hypothesis testing using the Westfall and Young’s (1993) family-wise error rate procedure.23 We find that the Highways result loses statistical significance at conventional levels (p-value drops to 0.176) even without the addition of state-specific trends. As additional robustness tests, we run all our specifications postponing to 2012 the treatment for states which might have changed their laws after 2010 election (i.e., NH and NC). We also distinguish between states that had only a ban on funding of outside spending by corporations (IA, KT, ME, MN, MT, RI, TN, WV) from states that imposed a ban on contributions by both corporations and unions.24 All our results are robust to these alternative specifications (details available upon request).

8 Conclusion

This paper oﬀers a theoretical framework and an empirical approach to understand and evaluate the consequences of outside spending on electoral outcomes, the ideology of elected legislators, and targeted public good provision. Our theory, based on the idea that outside spending aﬀects the

23This procedure computes the probability that one outcome of interest among many is statistically signiﬁcant when the null hypothesis of no eﬀect is true allowing for dependence between outcomes. 24NH was the only state with a ban on contributions by unions and not by corporations. Corporations, however, were capped at $5, 000 per electoral circle. Following Klumpp et al. (2016), we classify it as a complete ban.

35 salience of candidates’ attributes, suggests that lifting a ban on outside spending should increase the electoral strength of Republican candidates and move the average ideology of state legislatures in a conservative direction. Both predictions are robustly confirmed by the data. The effect on ideological polarization and targeted public good provision is expected to be more nuanced, as it depends on relative and absolute changes in salience. The null empirical effects we obtain suggest, in light of our theory, that the salience of Republican candidates is likely to have increased by a similar amount as the salience of Democratic candidates has decreased. Our set-up, like all salience models (e.g., Aragonèset al., 2015; Dragu and Fan, 2016), has little to say about the mechanism through which outside spending increases candidates’ salience. Outside spending might improve information held by voters by either increasing congruence between coverage and candidates, as in in Strömberg (2004), by increasing the effectiveness of candidates’ advertising (Prato and Wolton, 2016b), or by increasing negative advertising, which as argued by Geer (2008) can also improve information. Future research would do well in providing more precise micro-foundations for the effects documented here. Our model also assumes that the distribution of candidates’ ideologies is unaffected by the regulation of outside spending, thereby focusing our model and empirical evaluations on general election outcomes. An important direction for future work is to investigate the effect of outside spending on primary elections.

36 References

Ansolabehere, Stephen, and James M. Snyder. 2006. “Party control of state government and the distribution of public expenditures.” The Scandinavian Journal of Economics 108(4): 547-569.

Anzia, Sarah and Berry, Christopher. 2011. “The Jackie (and Jill) Robinson Eﬀect: Why Do Congresswomen Outperform Congressmen?” American Journal of Political Science 55(3): 478- 493.

Aragon`es,Enriqueta, Micael Castanheira, and Marco Giani. 2015. “Electoral competition through issue selection.” American Journal of Political Science 59(1): 71-90.

Ashworth, Scott. 2006. “The Economics of Campaign Finance” in The new Palgrave Dictionary of economics (2nd edn). Basingstoke : Palgrave Macmillan.

Ashworth, Scott and Ethan Bueno de Mesquita. 2009. “Elections with Platform and Valence Competition.” Games and Economic Behavior 67(1): 191-216.

Austen-Smith, David. 1998. “Allocating access for information and contributions.” Journal of Law, Economics and Organization 14(2): 277-303.

Azzimonti, Marina. 2011. “Barriers to investment in polarized societies.” The American Economic Review. 101(5): 2182-2204.

Azzimonti, Marina. 2016. “Does partisan conﬂict deter FDI inﬂows to the US?” NBER Working Paper No. 22336. http://www.nber.org/papers/w22336.

Barber, Michael J. 2016. “Ideological Donors, Contribution Limits, and the Polarization of Amer- ican Legislatures.” The Journal of Politics 78(1): 296-310.

Besley, Tim and Stephen Coate. 1997. “An economic model of representative democracy.” The Quarterly Journal of Economics 112(1): 85-114.

Bonica, Adam. 2014. “Mapping the ideological marketplace.” American Journal of Political Science 58(2): 367-386.

Buckley v. Valeo. 75-436 (424 U.S. 1 1976).

Coate, Stephen. 2004. “Pareto-improving campaign ﬁnance policy.” The American Economic Re- view 94(3): 628-655.

Citizens United v. Federal Electoral Commission. 08-205 (558 U.S. 310 2010).

Dragu, Tiberiu, and Xiaochen Fan. 2016. “An Agenda-Setting Theory of Electoral Competition.” The Journal of Politics 78(4): 1170-83.

Feddersen, Timothy and G¨ul, Faruk. 2014 “Polarization and Income In- equality: A Dynamic Model of Unequal Democracy.” Working paper. http://www.econ.as.nyu.edu/docs/IO/33147/Polarizationtf.pdf.

37 Hall, Andrew B. 2013. “Systemic Eﬀects of Campaign Spending: Evidence From Corporate Cam- paign Contribution Bans in State Legislatures.” Political Science Research & Methods 4(2): 343- 359.

Galasso, Vincenzo, and Tommaso Nannicini. 2011. “Competing on good politicians.” American Political Science Review 105(1): 79-99.

Geer, John G. In Defense of Negativity: Attack Ads in Presidential Campaigns. University of Chicago Press, 2008.

Gosling, James J. 1985. “Patterns of inﬂuence and choice in the Wisconsin budgetary process.” Legislative Studies Quarterly 10(4): 457-482.

Hall, Andrew and Alexander Fouirnaies. 2016. “The Exposure Theory of Access: Why Some Firms Seek More Access to Incumbents Than Others.” Working Paper. https:dropbox.com/Fouirnaies Hall Regulation.pdf/

Heineman, Ben W. Jr. 2012. “Super PACs: The WMDs of Cam- paign Finance. The Atlantic, January 6. Last Accessed: April, 24 2016. http://www.theatlantic.com/politics/archive/2012/01/super-pacs-the-wmds-of-campaign- ﬁnance/250961/.

Hirsch, Barry T., David A. Macpherson, and Wayne G. Vroman. 2001. “Estimates of Union Density by State”, Monthly Labor Review, Vol. 124(7): 51-55.

Klumpp, Tilman. 2014. “Populism, Partisanship, and the Funding of Political Campaigns.” Uni- versity of Alberta Working Paper. https://sites.ualberta.ca/ klumpp/docs/populism.pdf

Klumpp, Tilman, Hugo M. Mialon, and Michael A. Williams. 2016. “The Business of American Democracy: Citizens United, Independent Spending, and Elections.” Journal of Law and Eco- nomics, 59, 1?43.

La Raja, Raymond J., and Brian F. Schaffner. 2014. “The effects of campaign finance spending bans on electoral outcomes: Evidence from the states about the potential impact of Citizens United v. FEC.” Electoral Studies 33: 102-114.

McCarty, Nolan, Keith T. Poole, and Howard Rosenthal. 2016. Polarized America: The Dance of Ideology and Unequal Riches. Cambridge, MA: MIT Press.

Meirowitz, Adam. 2008. “Electoral contests, incumbency advantages, and campaign ﬁnance.” The Journal of Politics 70(3): 681-699.

Nichols, John and Robert W. McChesney. 2012. “ After ‘Citizens United’: The Attack of the Su- per PACs.” The Nation, Jan 18. https://www.thenation.com/article/after-citizens-united-attack- super-pacs/.

North Dakota Attorney General. 2010. “Press Release: STENEHJEM CREATES ELECTION LAWS TASK FORCE.” January 22. https://www.ag.nd.gov/NewsReleases/2010/01-22-10.pdf.

38 Poole, Keith T., and Howard Rosenthal. 1997. Congress: A Political-economic History of Roll Call Voting. Oxford: Oxford University Press. Prat, Andrea. 2002. “Campaign spending with office-seeking politicians, rational voters, and multiple lobbies.” Journal of Economic Theory 103(1): 162-189. Prato, Carlo, and Stephane Wolton. 2016a. “Citizens United: A Theoretical Evaluation.” LSE Working Paper. http://papers.ssrn.com/sol3/papers.cfm?abstract id=2790175. Prato, Carlo, and Stephane Wolton. 2016b. “Electoral Imbalances and their Consequences.” LSE Working Paper. http://papers.ssrn.com/sol3/papers.cfm?abstract id=2538690. Prato Carlo, and Stephane Wolton. “Campaign Cost and Electoral Accountability.” Political Sci- ence Research & Methods, forthcoming. https://www.cambridge.org/campaign-cost-and-electoral- accountability. Rasmussen Reports Poll. 2016. “Political Influence.” Feb. 9-10. http://www.rasmussenreports.com/public content/politics/general politics/february 2016/voters say money media have too much political clout Shor, Boris, and Nolan McCarty. 2011. “The ideological mapping of American legislatures.” Amer- ican Political Science Review 105(3): 530-551. Snyder, Jim and David Strömberg. 2010 “Press coverage and political accountability.” Journal of political Economy, 118(2), 355-408. Speech Now v Federal Election Commission. 08-5223 (1:08-cv-00248-JR 2010). Spencer, Douglas M., and Abby K. Wood. 2014. “Citizens United, states divided: an empirical analysis of independent political spending.” Indiana Law Journal 89: 315-372. Stern, Robert M. 2012. “Sunlight State by State After Citizens United.” Corporate Reform Coali- tion, June. https://www.citizen.org/documents/sunlight-state-by-state-report.pdf. Strömberg, David. 2004. “Mass media competition, political competition, and public policy.” The Review of Economic Studies 71(1): 265-284. US Census Bureau, Governments Division. 2000. “Federal, State, and Lo- cal Governments. Government Finance and Employment Classification Manual.” https://www.census.gov/govs/www/class ch7 ir.html Werner, Timothy. 2011. “The sound, the fury, and the nonevent: Business power and market reactions to the Citizens United decision.” American Politics Research 39(1): 118-141. Weismann, Robert. 2012. “Super PACs Promote Attack Ads and Special Interests.” U.S. News & World Report, Jan 13. http://www.usnews.com/debate-club/are-super-pacs-harming-us- politics/super-pacs-promote-attack-ads-and-special-interests. Westfall, P. H., & Young, S. S. 1993. Resampling-based multiple testing: Examples and methods for p-value adjustment (Vol. 279). New York: John Wiley & Sons.

39 Online Appendix (Not for publication)

A Proofs

First, we state the parametric assumptions which guarantee that (i) each candidate’s winning probabilities is always (i.e., for each pair of eﬀorts and ideologies) interior and (ii) candidates’ optimal eﬀort choices are always (i.e., for each pair of ideologies) interior. (i) is guaranteed by

1 > α(1 + y) (8) 2ψ

while (ii) follows from

1 8k−1 + 2 1 + 19k−1 21k−1 − 3 ∈ α − y − α + (α − α) n −1 o , α (9) I y< 1+19k 2ψ 12 12 12 12

To see why the two conditions are compatible, we impose the additional restriction that y = k−1

(so that the value of oﬃce is always positive). Then In 1+19k−1 o = 1 and the two conditions boil y< 12 1 h n −1 15k−1+3 o 21k−1−3 i down to 2ψ ∈ α max 1 + k , 12 , α 12 . It can be veriﬁed that when k = .1, α = 1, 4 and α = 3 the interval above is non-empty.

Proof of Lemma 1

We ﬁrst solve the unconstrained problem (i.e., not considering the constraint y ∈ [0, y]), whose

solution we denote by yJ (|θ|). We then show that under the assumptions the optimal eﬀort is always interior (i.e., yJ (|θ|) ∈ [0, y], and conclude by showing that yJ (|θ|) is strictly increasing. Let

YJ := Eθ(yJ (|θ|)),J ∈ {D,R} be the average eﬀort of candidate J.

40 Rearranging candidate J’s maximization problem (Equation 2), we obtain:

1 Z 1 max pJ (y; |θ|)(1 − ky) − |θ| − + pJ (y; |θ|, z)(|θ| + z)dz y 2 0 1 Z 1 = max pJ (y; |θ|)(1 − ky + |θ|) − |θ| − + pJ (y; |θ|, z)zdz y 2 0 ψαJ = max pJ (y; |θ|)(1 − ky + |θ|) + y y 2

25 Solving for optimal eﬀort, we obtain that yJ (|θ|) is the unique solution of:

dp (y, |θ|) ψα J (1 − ky + |θ|) + J = kp (y, θ) dy 2 J

Since we can write

1 h α i p (y, |θ|) = + ψ α y + α (1 − |θ|) − α Y − −J , (10) J 2 J J −J −J 2 it must be that

−1 k + 1 1 −1 1 1 α−J α−J yJ (|θ|) = |θ| − + k − − 1 − + Y−J (11) 2 2 4ψαJ 4 αJ 2αJ

This implies that YJ and Y−J solve:

−1 1 1 α−J α−J YJ =k − − 1 − + Y−J 4ψαJ 4 αJ 2αJ −1 1 1 αJ αJ Y−J =k − − 1 − + YJ 4ψα−J 4 α−J 2α−J

The linear system has a unique solution, which yields

4 −1 α−J 1 1 α−J YJ = k 1 + − − 1 − (12) 3 2αJ 2ψαJ 6 αJ −1 k + 1 1 4 −1 α−J 1 1 α−J yJ (|θ|) = |θ| − + k 1 + − − 1 − (13) 2 2 3 2αJ 2ψαJ 6 αJ

25 pJ is linear and increasing in y, which implies strict concavity of candidate’s objective function.

41 2 Showing that yJ (|θ|) is interior is equivalent to showing that for all pairs (αJ , α−J ) ∈ [α, α] (i) k−1+1 k−1+1 YJ − 4 ≥ 0 and (ii) YJ + 4 ≤ y. The two conditions can be rewritten as

8k−1 + 2 13k−1 − 5 1 α + α ≥ (14) 12 −J 12 J 2ψ 8k−1 + 2 19k−1 + 1 1 α + − y α ≤ (15) 12 −J 12 J 2ψ

It is immediate (albeit algebraically tedious) to verify that both conditions are implied by (Equa- tion 9). The lemma then follows from direct observation of (13).

Proof of Lemma 2

Plugging (12) and (13) into (10) yields

1 k−1 − 1 1 1 + 4k−1 p (y∗ (|θ|); |θ|) = + ψ α |θ| − + (α − α ) (16) J J 2 J 2 2 J −J 6

The lemma follows from k < 1.

Proof of Proposition 1

∗ 1 1+4k−1 Using (16), we obtain pJ = E|θ|{pJ (yJ (|θ|); |θ|)} = 2 + ψ(αJ − α−J ) 6 , which proves the Propo-

sition. Notice that pJ ∈ [0, 1] follows from (Equation 8).

Proof of Proposition 2

∗ ∗ The average ideology of the elected candidate is: M(αD, αR) := pR(yR(θR); θR)E(θR|e = R) + ∗ ∗ pR(yR(|θD|); |θD|)E(θD|e = D). Using (16) and E(|θJ ||e = J) characterized in the proof of Propo- sition 4, we obtain:

−1 Z 1 −1 Z 0 αR − αD −1 k − 1 1 k − 1 1 M(αD, αR) = (1 + 4k ) + ψαR z z − dz − ψαD z z + dz 3 2 0 2 2 −1 2 α − α ψ = R D 1 + 4k−1 + (k−1 − 1) . (17) 3 8

The claim follows from k < 1.

42 Proof of Proposition 3

(i) Ideological polarization can be written as

∗ ∗ E{pR(θR, θD)θR + pD(θR, θD)|θD|} Z Z ∗ ∗ ∗ ∗ = {pR(yR(w), yD(z), w, z)w + (1 − pR(yR(w), yD(z), w, z))w} dzdw w∈[0,1] z∈[0,1] Z Z ∗ ∗ = pR(yR(w), w)wdw + pD(yD(z), z)zdz w∈[0,1] z∈[0,1] 1 k−1 − 1 1 + 4k−1 k−1 − 1 1 + 4k−1 = + ψ α + (α − α ) + ψ α + (α − α ) 2 R 24 R D 12 D 24 D R 12 1 k−1 − 1 = + ψ (α + α ) 2 R D 24

where pR(yR, yD, w, z) comes from Equation 1 and the third line comes from equation Equation 16. It is immediate to verify that polarization is higher absent a ban than under a ban if and only if

αR + αD > α.

(ii) Following the same reasoning as part (i), we obtain that the ex-ante average targeted public good provision is given by

∗ ∗ ∗ ∗ E(αD, αR) := E{pR(θR, θD)yR(θR) + pD(θR, θD)yD(θD)} Z Z ∗ ∗ ∗ ∗ ∗ ∗ = {pR(yR(w), yD(z), w, z)yR(w) + (1 − pR(yR(w), yD(z), w, z))yD(w)} dzdw w∈[0,1] z∈[0,1] Z Z ∗ ∗ ∗ ∗ = pR(yR(w), w)yR(w)dw + pD(yD(z), z)yD(z)dz w∈[0,1] z∈[0,1]

∗ k−1+1 1 From (13), we can write yJ (t) = 2 t − 2 + YJ . From (10) we obtain

1 h i 1 p (y∗ (t), t) = + ψα y∗ (t) + 1 − t − ψα + Y J J 2 J J −J 2 −J 1 h 1 i α − α = + ψα y∗ (t) + − t − ψα Y + ψ J −J 2 J J 2 −J −J 2 1 hk−1 − 1 1 i α − α = + ψα t − + Y − ψα Y + ψ J −J 2 J 2 2 J −J −J 2

43 Hence, we can write:

Z ∗ ∗ pJ (yJ (t), t)yJ (t)dt t∈[0,1] Z −1 h1 αJ − α−J i hk + 1 1 i = − ψα−J Y−J + ψ t − + YJ dt 2 2 t∈[0,1] 2 2 Z hk−1 − 1 1 ihk−1 + 1 1 i + ψαJ t − + YJ t − + YJ dt t∈[0,1] 2 2 2 2 −2 Z 2 YJ αJ − α−J h 2 k − 1 1 i = − ψα−J Y−J YJ + ψ YJ + ψαJ YJ + t − dt 2 2 4 t∈[0,1] 2 Y α − α k−2 − 1 1 = J + ψY [α Y − α Y ] + ψ J −J Y + ψα 2 J J J −J −J 2 J J 4 12

−1 1 Under a ban (αJ = α−J ), we have that YJ := Y = 2k − 2ψα . Expected public good provision then equals k−2 − 1 E(α, α) = Y + ψα . 24 Absent a ban, we can rewrite the expected public good provision as

−2 X YJ αJ − α−J k − 1 1 E(α , α ) = + ψY [α Y − α Y ] + ψ Y + ψα D R 2 J J J −J −J 2 J J 4 12 J∈{R,D} Y + Y ψ k−2 − 1 1 = R D + (α − α )(Y − Y ) + ψ(Y − Y )(α Y − α Y ) + ψ(α + α ) 2 2 R D R D R D R R D D R D 4 12

Observe that:

−1 α−J − αJ 4k + 1 1 1 1 YJ − Y = − − αJ 6 2ψ αJ α −1 αD αR 4k + 1 1 1 1 YR − YD = (YR − Y ) − (YD − Y ) = − − − αR αD 6 2ψ αR αD 4k−1 − 2 α Y − α Y = (α − α ) R R D D R D 6

44 Hence, we obtain:

E(αD, αR) − E(α, α) Y + Y − 2Y ψ k−2 − 1 1 = R D + (α − α )(Y − Y ) + ψ(Y − Y )(α Y − α Y ) + ψ(α + α − 2α) 2 2 R D R D R D R R D D R D 4 12 2 −1 2 −1 2 −1 1 (αR − αD) 4k + 1 ψ (αR − αD) 4k + 1 1 (αR − αD) 4k − 2 = − (αR + αD) − 1 + 2 αRαD 6 2 αRαD 6 2ψ αRαD 3 1 1 1 1 k−2 − 1 1 − + − 2 + ψ(αR + αD − 2α) 4ψ αR αD α 4 12 2 −1 −1 (αR − αD) 4k + 1 4k + 1 = 1 − ψ (αR + αD) αRαD 6 6 1 1 1 1 k−2 − 1 1 − + − 2 + ψ(αR + αD − 2α) (18) 4ψ αR αD α 4 12

1 4k−1+1 4k−1+1 1 By assumption 2ψα < k−1+1 . Hence, 1 − ψ 6 (αR + αD) > 1 − 6(k−1+1) > 3 (since k > 0) so the

ﬁrst term in Equation 18 is strictly positive for αR 6= αD. Observe further that E(αD, α)−E(α, α) >

0 for all αD > α. We now prove that ﬁxing αR, E(αD, αR) − E(α, α) is strictly increasing with αD. 2 dE(αD,αR)−E(α,α) (αR−αD) αR αD Denote H(αD, αR) = . Using Equation 18, we obtain (using = + −2): dαD αRαD αD αR

−1 −1 2 −1 −1 1 αR 4k + 1 4k + 1 (αR − αD) 4k + 1 4k + 1 H(αD, αR) = − 2 1 − ψ (αR + αD) − ψ αR αD 6 6 αRαD 6 6 1 1 k−2 − 1 1 + 2 + ψ 4ψ αD 4 12 −1 −1 2 1 1 αR − αD 4k + 1 αD + αR 4k + 1 (αD + αR) = 2 − − ψ − (αR − αD) 4ψ αD αDαR 6 αD 6 αD k−2 − 1 1 + ψ 4 12 2 α +α D R −2 1 1 αR − αD 1 αD k − 1 1 ≥ − 2 + ψ 2 (αD+αR) 4ψ αD αDαR 4ψ − (αR − αD) 4 12 αD 2 −2 1 αR − αD (αR + αD) k − 1 1 = 2 1 − 2 + ψ 4ψαD αR (αR + αD) − αD(αR − αD) 4 12 2 −2 1 αR − αD (αR + αD) k − 1 1 = 2 1 − 2 + ψ 4ψαD αR (αR + αD) − αD(αR − αD) 4 12 2 −2 1 (αR + αD) − αR(αR − αD) k − 1 1 = 2 + ψ 4ψαD αR((αR + αD) − αD(αR − αD)) 4 12 >0

45 The inequality comes from f(x) = x(a − xb), a > 0 and b > 0, being maximized at x = a/2b. By

symmetry, we also have E(αD, αR) − E(α, α) strictly increasing with αR (ﬁxing αD). The properties of E(αD, αR) − E(α, α) then imply that there exists a unique αb(αD, αR) such that expected public good increases after the lifting of a ban if and only if αR and αD satisfy α ≤ αb(αD, αR). To ﬁnish the proof, we now establish that α(α , α ) ≥ αD+αR . To to so, assume (without loss of b D R 2

generality that) αR = α + δ and αD = α − δ, δ > 0. Rearranging Equation 18, we obtain:

E(αD, αR) − E(α, α) 4δ2 4k−1 + 1 4k−1 + 1 1 2δ2 = 1 − ψ 2α − αRαD 6 6 4ψ αRαDα 4δ2 1 1 2δ2 ≤ − αRαD 8ψα 4ψ αRαDα =0

The inequality again follows from f(x) = x(a − xb), a > 0 and b > 0, being maximized at x = a/2b. This completes the proof of the proposition.

Proposition 4. Absent a ban, for each candidate J ∈ {R,D}, there exists α˜J (α, α−J ) such that the expected extremism and targeted public good provision of an elected candidate J are higher than

under a ban if and only if αJ ≥ α˜J (α, α−J ).

b b b Proof. Under a ban, as explained in the text, αR = αD = α. Denote by yJ , E {θJ |J = e}, and pJ

the associated equilibrium quantities. When the ban is lifted, we allow αR to diﬀer from αD. To

αJ 26 prove the proposition is useful to deﬁne KJ (αJ , α−J ) := 1+4k−1 . 1+ψ(αJ −α−J ) 3 We ﬁrst compute the expected extremism of an elected candidate J: E{|θJ ||J = e}.

Z 1 Z 1 −1 pJ (z) 1 1 k − 1 1 E{|θJ ||J = e} = z dz = + ψαJ z − zdz 0 pJ 2 pJ 0 2 2 1 ψ(k−1 − 1) α = + J 2 12 1+4k−1 1 + ψ(αJ − α−J ) 3

26 2 Notice that pJ > 0 guarantees that KJ (αJ , α−J ) > 0 for all (αJ , α−J ) ∈ [α, α] .

46 Since k < 1, extremism strictly increases when a ban is lifted if and only if :

1 − ψα 1+4k−1 K (α , α ) > α ⇔ α > α˜ (α, α ) := α −J 3 . (19) J J −J J J −J 1+4k−1 1 − ψα 3

We now compute the expected targeted public good provision (henceforth, ‘public good’) of an

∗ elected candidate J: E{yJ (|θ|)|J = e}.

k−1 + 1 1 ψ(k−2 − 1) α E{y∗ (|θ|)|J = e} =E Y + |θ| − |J = e = Y + J J J 2 2 J 24 1+4k−1 1 + ψ(αJ − α−J ) 3

Hence, public good increases when a ban is lifted if and only if:

−2 −2 4 −1 α−J 1 1 α−J ψ(k − 1) −1 1 ψ(k − 1) k 1 + − − 1 − + KJ (αJ , α−J ) > 2k − + α 3 2αJ 2ψαJ 6 αJ 24 2ψα 24 −1 −2 1 1 1 1 4k + 1 αJ − α−J ψ(k − 1) − − + (KJ (αJ , α−J ) − α) > 0 2ψ α αJ 2 3 αJ 24 1+4k−1 ! −2 1 1 1 + ψ(αJ − α−J ) 3 ψ(k − 1) − + (KJ (αJ , α−J ) − α) > 0 2ψ α αJ 24 1 1 1 ψ(k−2 − 1) − + (KJ (αJ , α−J ) − α) > 0 (20) 2ψ α KJ (αJ , α−J ) 24

It is immediate to see that (20) is satisﬁed if and only if KJ (αJ , α−J ) > α ⇔ αJ > α˜J (α, α−J ).

47 B Empirical Results

State Date ban lifted Alaska 19-Feb-10 Arizona 1-Apr-10 Colorado 25-May-10 Connecticut 8-Jun-10 Iowa 8-Apr-10 Kentucky 24-Mar-10 Massachusetts 8-Feb-10 Michigan 21-Jan-10 Minnesota 18-May-10 Montana 18-Oct-10 New Hampshire North Carolina 10-Jul-10 North Dakota 22-Jan-10 Ohio 26-Feb-10 Oklahoma 1-Feb-10 Pennsylvania 4-Mar-10 Rhode Island 13-Jul-10 South Dakota 11-Mar-10 Tennessee 23-Jun-10 Texas 21-Apr-10 West Virginia 13-Mar-10 Wisconsin 10-May-10 Wyoming 21-Jan-10

Table 10: State Responses to Citizens United Source: Spencer and Wood (2014) except for Montana (Klumpp et al., 2015), North Carolina, North Dakota, and Rhode Island (authors’ research). For Montana, the date is based on an injunction from the Montana District Court ruling (Klumpp et al., 2015).27 For North Carolina, the date is based on House Bill 748.28 For North Dakota, the date is the date of a task force recognizing that the state laws were void (North Dakota Attorney General, 2010).29 For Rhode Island, the source is Stern (2012). An exact date could not be found for New Hampshire.30

27The court injunction was reversed by the Montana Supreme Court in 2011 only to be upheld by the US Supreme Court in 2012 so Montana is considered as treated for both elections. 28Under section 5 of the Voting Rights Act, any change to voting laws in North Carolina must be approved by the Department of Justice. House Bill 748 was approved in 2011. 29The campaign ﬁnance law to create disclosure rules for IEs by corporations and unions was not amended until 2011. 30Given the ambiguity with respect to the when New Hampshire and North Carolina’s laws were implemented, we run robustness checks with these states not changing their laws until 2012 for a regressions. All results remain qualitatively the same.

48 C Robustness tests

C.1 Trends for Upper Chamber Vote and Seat Share

(a) vote share (b) seat share

Figure 14: Trends in average Republican vote and seat share for the upper chamber

C.2 Placebo test on electoral outcomes

We show that our results hold when we augment Equation 3 with a lead treatment indicating the treatment status in the next year (lead1), in the next 2 years, etc. up to the next 4 years (lead4). As Tables 13 and 14 indicate, the eﬀect of lifting a ban still increases Republican vote and seat share. These results mitigate potential concerns about the failure of the parallel trend assumption. Tables 16, 15, and 17 report estimated coeﬃcients for the placebo test of changing the year of the treatment.

C.3 REDMAP as a potential confounder

Tables 18, 19, and 20 show that our results hold when we include an indicator for receiving REDMAP spending.

49 (a) Republican vote share With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.489 0.097 0.486 0.088 upper chamber 0.490 0.100 0.484 0.092

(b) Republican seat share With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.479 0.157 0.453 0.166 upper chamber 0.472 0.175 0.454 0.192

(c) Avg Ideology (NPAT) With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.025 0.341 -0.090 0.383 Republican 0.715 0.321 0.649 0.368 Democrat -0.711 0.330 -0.773 0.374 upper chamber 0.006 0.350 -0.068 0.344 Republican 0.728 0.317 0.654 0.345 Democrat -0.765 0.352 -0.769 0.380 (c) Polarization (NPAT–Absolute Value) With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.756 0.196 0.759 0.239 upper chamber 0.780 0.204 0.735 0.226 (c) Polarization (NPAT–Share of Moderate Legislators) With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.079 0.087 0.119 0.131 upper chamber 0.068 0.090 0.115 0.153

Table 11: Pre-Treatment Summary Statistics

50 (d) Avg Ideology (DIME) With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. lower chamber 0.190 0.408 0.097 0.426 Republican 0.713 0.301 0.540 0.321 Democrat -0.371 0.427 -0.321 0.410

upper chamber 0.221 0.438 0.116 0.453 Republican 0.710 0.330 0.545 0.338 Democrat -0.302 0.448 -0.323 0.403 (e) Intergovernmental transfers With Spending Bans Without Spending Bans Mean St. Dev. Mean St. Dev. Total 15.119 1.157 15.314 1.216 Education 14.759 1.128 14.605 2.826 Highways 11.585 2.117 11.967 1.331 General Support 12.065 1.686 11.770 2.826 Health & Hospital 10.469 2.984 10.562 3.002 Transit 8.128 3.839 8.284 4.038 House & Comm Dvt 9.115 2.278 9.008 2.116 Public Welfare 10.715 3.188 10.225 3.427 Sewage 4.901 4.096 4.933 3.990 Other 12.180 1.218 12.165 1.643

Table 12: Pre-Treatment Summary Statistics (continued)

51 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep VS Rep VS Rep VS Rep VS Rep VS Rep VS

CitUn × BanState 0.018 0.040* 0.075** 0.035 0.049* 0.046 (0.023) (0.023) (0.031) (0.028) (0.027) (0.041) CitUn × BanState Lead1 -0.004 0.012 0.038 -0.001 0.009 0.007 (0.019) (0.017) (0.024) (0.021) (0.022) (0.032) CitUn × BanState Lead2 -0.003 0.012 0.034 0.005 0.014 0.012 (0.017) (0.014) (0.022) (0.022) (0.020) (0.028) CitUn × BanState Lead3 -0.009 0.002 0.021 -0.004 0.002 -0.001 (0.015) (0.014) (0.019) (0.018) (0.017) (0.025) CitUn × BanState Lead4 -0.001 0.008 0.023 0.011 0.016 0.013 (0.012) (0.012) (0.015) (0.017) (0.017) (0.019) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 606 606 606 564 564 564 R-squared 0.815 0.842 0.920 0.682 0.691 0.792 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 13: Lead treatment Placebo Test for Vote Share

C.4 District-level analysis of electoral outcomes

To analyze the impact of outside spending on district level electoral outcomes, we deﬁne a dummy variable, RepW insdst, which takes the value 1 (0) when a Republican candidate wins (respectively loses) district d in state s in year t. Due to redistricting issue, we only consider the years 2002 to 2010 (9 states experience mid-decade redistricting and we use only the years with similar district as in 2010). Since North Carolina experiences multiple redistricting episodes up to 2009, we drop it from the analysis. Furthermore, we exclude multi-member districts (approximately 5% of our sample) unless they have staggered elections or separate ballots so we can attribute electoral outcomes to a single candidate. Overall, we are left with 19,794 observations for the lower chamber and 5,363 for the upper chamber. We run the following baseline speciﬁcation, with standard errors clustered at the state level:

RepW insdst = βCitUnt × BanStates + γds + δt + dst (21)

52 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep SS Rep SS Rep SS Rep SS Rep SS Rep SS

CitUn × BanState 0.019 0.053 0.064 0.058 0.087 0.059 (0.043) (0.044) (0.048) (0.057) (0.057) (0.072) CitUn × BanState Lead1 -0.020 0.004 0.011 -0.008 0.012 -0.010 (0.033) (0.030) (0.036) (0.045) (0.046) (0.060) CitUn × BanState Lead2 -0.032 -0.010 -0.003 0.020 0.038 0.023 (0.029) (0.026) (0.032) (0.044) (0.043) (0.055) CitUn × BanState Lead3 -0.010 0.008 0.013 -0.013 -0.001 -0.012 (0.023) (0.021) (0.023) (0.037) (0.038) (0.040) CitUn × BanState Lead4 0.001 0.015 0.019 0.041 0.052 0.044 (0.018) (0.018) (0.016) (0.034) (0.035) (0.040) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 606 606 606 564 564 564 R-squared 0.827 0.846 0.933 0.703 0.714 0.822 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 14: Lead treatment Placebo Test for Seat Share

The results of the baseline and additional estimations (with Deep South Trend and State specific trends) are summarized in Table 21. Across the columns, we find a consistent positive effect of the lifting of spending bans on the probability that a Republican is elected. Notice that the coefficient (and statistical significance) of our estimates is different when we augment the baseline specification in column 1 with state specific time trends (column 3). Columns 2 and 3 show that this discrepancy can be reasonably attributed to a few Deep South states that are already trending Republican during this time period and experience no change in the spending bans, inducing a downward bias in our first specification. When we correct for this in column 2, we see that the coefficient becomes significant and closer in magnitude to column 3’s specification. Using our preferred specification in column 3, we can see that outside spending increases the probability of Republican victory in the lower house by approximately 5.7 percentage points. The effect is not significant when looking at the upper chamber, but across specifications coefficients are

53 Lower Chamber Upper Chamber 2003 0.006 0.023 0.009 0.016 0.026 -0.007 (0.018) (0.016) (0.013) -0.019 -0.018 -0.02 2004 0.006 0.023 0.009 0.016 0.026 -0.007 (0.018) (0.016) (0.013) (0.019) (0.018) (0.020) 2005 0.010 0.027 0.023* 0.021 0.032 0.014 (0.018) (0.017) (0.012) (0.021) (0.020) (0.020) 2006 0.010 0.027 0.023* 0.021 0.032 0.014 (0.018) (0.017) (0.012) (0.021) (0.020) (0.020) 2007 0.014 0.031* 0.027** 0.024 0.035 0.017 (0.018) (0.017) (0.012) (0.022) (0.022) (0.022) 2008 0.014 0.031* 0.027** 0.024 0.035 0.017 (0.018) (0.017) (0.012) (0.022) (0.022) (0.022) 2009 0.019 0.037* 0.035** 0.034 0.045* 0.036* (0.019) (0.019) (0.015) (0.024) (0.023) (0.020) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Table 15: Vote Share: Changing Year of treatment (Citizens United) For each year, the coeﬃcient represents the point estimates in Equation 3 when CitUnt × BanStates is assumed to take value 1 starting that year. Robust standard errors are clustered at the state level in parentheses.

remarkably similar to the ones for the lower chamber. Our estimates are comparable to, but slightly smaller than Klumpp et al.’s (2015) who use a similar approach (see Table 3). The diﬀerence could be due to two factors. First, we exclude districts which experienced mid-decade redistricting so our number of observations is lower than theirs (19,794 against 21,656 for the lower chamber). Second, we take a more parsimonious approach omitting controls such as the number of candidates running which could induce post-treatment bias.

C.5 Alternative measure of ideology

In this subsection, we look at the effect of lifting a ban on ideology using Bonica’s (2014) DIME scores. Figure 15 shows that, as for Shor and McCarty’s measure, trends between control and treated states are markedly different before 2000. While the problem seems less severe in the period 2000-2014, there still exist visible differences between control and treated states which we address using state specific trends.

54 Lower Chamber Upper Chamber 2003 -0.001 0.024 -0.012 0.022 0.042 -0.036 (0.032) (0.031) (0.022) (0.042) (0.041) (0.032) 2004 -0.001 0.024 -0.012 0.022 0.042 -0.036 (0.032) (0.031) (0.022) (0.042) (0.041) (0.032) 2005 0.002 0.027 0.001 0.033 0.054 0.007 (0.033) (0.033) (0.023) (0.042) (0.041) (0.033) 2006 0.002 0.027 0.001 0.033 0.054 0.007 (0.033) (0.033) (0.023) (0.042) (0.041) (0.033) 2007 0.014 0.039 0.033 0.036 0.057 0.013 (0.034) (0.035) (0.025) (0.043) (0.043) (0.034) 2008 0.014 0.039 0.033 0.036 0.057 0.013 (0.034) (0.035) (0.025) (0.043) (0.043) (0.034) 2009 0.025 0.051 0.052** 0.054 0.076* 0.050 (0.036) (0.037) (0.026) (0.046) (0.045) (0.032) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Table 16: Seat Share: Changing Year of treatment (Citizens United) For each year, the coeﬃcient represents the point estimates in Equation 3 when CitUnt × BanStates is assumed to take value 1 starting that year. Robust standard errors are clustered at the state level in parentheses.

In Bonica’s DIME, state legislators’ ideology is measured each election year (rather than averaged across their whole tenure). As a result, the statistical power of our tests is significantly higher than in the baseline analysis. However, as explained above, ideal points are measured using contributions which are affected by the regulatory change (see Klumpp et al., 2015). The results should thus be interpreted with caution. Table 22 confirms the results in the main text: legislatures become more conservative as a result of the lifting of a ban. The point estimates are slightly larger and of higher statistical significance. Table 23 looks at the effect by party. Results are slightly weaker than when we use the NPAT data (and in some cases no longer statistically significant).31

31Running Equation 4 for each party separately returns non statistically signiﬁcant coeﬃcients, as for the NPAT data.

55 Lower Chamber Upper Chamber 2001 0.008 0.025 0.008 0.007 0.029 -0.029 (0.030) (0.030) (0.020) (0.039) (0.038) (0.026) 2002 0.002 0.019 -0.000 0.026 0.049 -0.007 (0.029) (0.029) (0.020) (0.037) (0.036) (0.028) 2003 0.002 0.020 -0.000 0.034 0.058 0.007 (0.030) (0.031) (0.023) (0.039) (0.038) (0.036) 2004 -0.006 0.012 -0.021 0.023 0.047 -0.020 (0.031) (0.031) (0.020) (0.036) (0.036) (0.032) 2005 -0.014 0.004 -0.051* 0.015 0.038 -0.050 (0.033) (0.034) (0.026) (0.037) (0.037) (0.034) 2006 -0.013 0.005 -0.059** 0.014 0.039 -0.061* (0.032) (0.033) (0.023) (0.037) (0.037) (0.034) 2007 -0.015 0.004 -0.072*** 0.014 0.038 -0.069 (0.032) (0.034) (0.026) (0.039) (0.038) (0.044) 2008 -0.003 0.017 -0.032* 0.027 0.053 -0.018 (0.032) (0.033) (0.019) (0.039) (0.039) (0.031) 2009 0.009 0.031 0.011 0.040 0.068 0.027 (0.033) (0.035) (0.028) (0.042) (0.042) (0.033) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Table 17: Average Ideology: Changing Year of treatment (Citizens United) For each year, the coeﬃcient represents the point estimates in Equation 4 when CitUnt × BanStates is assumed to take value 1 starting that year. Robust standard errors are clustered at the state level in parentheses.

C.6 Alternative measure of polarization

Since the analysis of polarization does not yield statistically significant effects, it is important to explore the effect of the treatment on an alternative measure of polarization. We employ a method inspired by Hirano et al. (2010), who study how the introduction of primaries affects polarization in Congress. In one of their tests, they look at the share of “moderates” in the Senate, and define a moderate as having a DW-NOMINATE score between −.15 and .10. In our analysis, we define a moderate as a legislator whose score is between the 45th and 55th percentile (that is, a NPAT score between −.194 and .149 for the lower chamber and between −.178 and .143 for the upper chamber). Table 24 confirms that the removal of bans had no statistically discernible effect on the share of moderate legislators (if anything, the coefficients seem to point towards an increase in the share of

56 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep VS Rep VS Rep VS Rep VS Rep VS Rep VS

CitUn × BanState 0.019 0.036* 0.034** 0.034 0.045* 0.036* (0.019) (0.019) (0.015) (0.024) (0.023) (0.020) REDMAP 0.011 0.003 0.014 -0.010 -0.016 -0.003 (0.017) (0.011) (0.010) (0.026) (0.022) (0.022) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 606 606 606 564 564 564 R-squared 0.815 0.841 0.919 0.682 0.690 0.791 Robust standard errors are clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 18: Eﬀect of Citizens United on Republican vote share with REDMAP

Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep SS Rep SS Rep SS Rep SS Rep SS Rep SS

CitUn × BanState 0.024 0.051 0.052* 0.053 0.076* 0.050 (0.036) (0.037) (0.026) (0.046) (0.045) (0.032) REDMAP 0.014 0.002 -0.003 0.015 0.003 0.009 (0.033) (0.021) (0.018) (0.055) (0.047) (0.045) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

moderates). The results are robust to alternative cutoﬀs for moderation (e.g., the 47.5th and 52.5th percentiles).32

32Details upon request.

57 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP

CitUn × BanState 0.042 0.065* 0.093** 0.063 0.091* 0.094* (0.035) (0.038) (0.036) (0.049) (0.050) (0.052) REDMAP -0.019 -0.017 -0.031 0.003 0.003 -0.008 (0.032) (0.031) (0.028) (0.028) (0.029) (0.042) State & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 668 668 668 663 663 663 R-squared 0.960 0.962 0.983 0.933 0.937 0.969 Robust standard errors are clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 20: Eﬀect of Citizens United on Average Ideology (NPAT) with REDMAP

C.7 Polarization eﬀects using DIME

Tables 25 and 26 show how the polarization results hold using the DIME contribution data as well.

C.8 Heterogeneous eﬀects: Data and eﬀect on ideology using DIME

Union membership density data (from 1964-2015) used represents the percentage of each state’s nonagricultural wage and salary employees who are union members. Data was obtained from Hirsch et al. (2001), and was created using the Current Population Survey and the discontinued BLS publication Directory of National Unions and Employee Associations. Our Corp variable is based on an industry weighted index of exposure to regulation. Industry weights were obtained from disaggregated state level GDP data from the Bureau of Economic Analysis. The measure of industry level regulatory exposure developed by Hall and Fouirnaies, is based on publicly traded ﬁrms’ annual 10-K ﬁlings with the SEC. Using text analysis, Hall and Fouirnaies construct an industry-level measure of self-reported regulatory risk.

58 lower chamber upper chamber (1) (2) (3) (1) (2) (3) VARIABLES Rep Win Rep Win Rep Win Rep Win Rep Win Rep Win

CitUn×BanState 0.030 0.039* 0.057** 0.032 0.052 0.049 (0.021) (0.022) (0.027) (0.048) (0.044) (0.054)

District & Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 19,794 19,794 19,794 5,363 5,363 5,363 R-squared 0.831 0.831 0.835 0.862 0.863 0.868 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 21: Eﬀect of Citizens United on Republicans’ winning probability at the district level

Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP

CitUn×BanState 0.047 0.069* 0.108** 0.072* 0.087** 0.113* (0.034) (0.036) (0.043) (0.039) (0.041) (0.066) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 306 306 306 278 278 278 R-squared 0.955 0.957 0.973 0.929 0.930 0.945

Table 22: Eﬀect of Citizens United on average ideology using DIME database Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1

59 (a) lower chamber (b) upper chamber

Figure 15: Trends for Average Ideology using DIME

Lower Chamber Upper Chamber (1) (2) (3) (4) (1) (2) (3) (4) VARIABLES Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP Avg IP

Rep×CitUn×BanState 0.268*** 0.167*** 0.216 -0.000 0.282*** 0.221*** 0.222 0.072 (0.090) (0.041) (0.139) (0.051) (0.104) (0.068) (0.151) (0.083) CitUn×BanState -0.134** -0.084*** -0.108 0.007 -0.162** -0.132** -0.132 -0.054 (0.050) (0.029) (0.073) (0.028) (0.068) (0.053) (0.088) (0.064) Rep 0.983*** 0.915*** 0.972*** 0.865*** 0.952*** 0.907*** 0.940*** 0.865*** (0.057) (0.072) (0.058) (0.071) (0.055) (0.068) (0.056) (0.068) State and Year FE XXXXXXXX Rep×Ban XXXX Rep×Citizen XXXX State Speciﬁc Trends XX

Observations 609 609 609 609 553 553 553 553 R-squared 0.891 0.894 0.891 0.899 0.881 0.883 0.882 0.889 F-statistic p-value 0.017 0.001 0.305 0.945 0.033 0.008 0.327 0.668 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 23: Eﬀect of Citizens United by party (DIME score)

60 Lower Chamber Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Moderates Moderates Moderates Moderates Moderates Moderates

CitUn×BanState 0.033* 0.024 -0.010 0.031* 0.028* 0.005 (0.017) (0.018) (0.012) (0.016) (0.017) (0.014) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 668 668 668 663 663 663 R-squared 0.900 0.904 0.973 0.929 0.929 0.973 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 24: Eﬀect of Citizens United on average share of moderate legislators (NPAT scores in [−.194,.149] for lower house and in [−.178,.143] for upper house).

Lower Chamber (1) (2) (3) (1) (2) (3) VARIABLES Abs IP Abs IP Abs IP Moderates Moderates Moderates

CitUn × BanState 0.010 0.008 -0.003 0.002 -0.003 -0.002 (0.019) (0.018) (0.026) (0.018) (0.015) (0.020) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 306 306 306 306 306 306 R-squared 0.944 0.944 0.968 0.728 0.731 0.860 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 25: Eﬀect of Citizens United on Polarization using DIME scores in Lower Chamber

61 Upper Chamber (1) (2) (3) (1) (2) (3) VARIABLES Abs IP Abs IP Abs IP Moderates Moderates Moderates

CitUn × BanState 0.049 0.046 0.047 -0.022 -0.029 -0.020 (0.031) (0.031) (0.035) (0.018) (0.019) (0.030) State and Year FE XXXXXX Deep South Trend XX State Speciﬁc Trends XX

Observations 278 278 278 278 278 278 R-squared 0.895 0.895 0.936 0.612 0.616 0.716 Robust standard errors clustered at the state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 26: Eﬀect of Citizens United on Polarization using DIME scores in Upper Chamber

Lower Chamber Upper Chamber (1) (2) (3) (4) VARIABLES Avg IP Avg IP Avg IP Avg IP

CitUn×BanState 0.069* 0.058 0.087** 0.138** (0.036) (0.036) (0.041) (0.059) · · · ×Union 0.026 -0.073 (0.058) (0.073) · · · ×Corp -0.079 -0.115 (0.099) (0.118) · · · ×Union×Corp 0.109 0.143 (0.140) (0.153) State and Year FE XXXX Deep South Trend XXXX

Observations 306 306 278 278 R-squared 0.957 0.958 0.930 0.932 F-statistic p-value 0.124 0.093 Robust standard errors clustered at state level in parentheses. *** p<0.01, ** p<0.05, * p<0.1 Table 27: Heterogeneous effect of Citizens United on average ideology (DIME scores). Columns 1 and 3 show the baseline effect. Columns 2 and 4 include additional independent variables Union, Union × CitUn, Corp, Corp × CitUn, Corp × Union, Corp × CitUn × Union. The F-statistics reported are testing the null hypothesis of joint zero values of all four coefficients.