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The Market for Political Influence

Shrey Shah

This paper is part of a collection of unpublished economics papers.

What determines the price and allocation of political influence? We develop a unified empirical framework treating lobbying, campaign contributions, independent expenditures, and revolving-door employment as channels for purchasing influence. Using Citizens United v. FEC (2010) as a natural experiment, we reject the “whack-a-mole” hypothesis that firms substitute between influence channels. When corporate campaign spending became legal, firms did not reduce lobbying—they reallocated it toward campaign-complementary issues. Lobbying on taxation increased 26% (p < 0.001) and financial regulation increased 45% (p < 0.001) in treated states relative to controls. We reject the strong substitution hypothesis at p < 0.001: the estimated cross-elasticity of $\eta_{LC} = +0.09$ is inconsistent with the theoretical prediction of $\eta = -0.5$ under channel substitutability. The STOCK Act (2012) provides complementary evidence: restricting government trading rents decreased revolving door transitions by 5.6 percentage points ($\eta_{GR} = 0.44$, p = 0.054), indicating these channels are complements rather than substitutes. Our descriptive analysis documents high concentration—the top 10 PACs control 45% of \$55.8 billion in receipts, while lobbying firms received \$63 in federal contracts per \$1 lobbied. Using a convergence-based welfare approach, we estimate rent-seeking costs at \$480 billion annually (1.9% of GDP), with bounds of \$340–630B (1.3–2.5% of GDP). The policy implication is that campaign finance restrictions would achieve their intended effect: influence spending would fall by the full amount of restricted campaign expenditures, with minimal leakage to lobbying.

1. Introduction

In 2004, a coalition of multinational corporations spent \$282 million lobbying for the American Jobs Creation Act. The return on this investment was \$88.6 billion in tax savings—a rate of return exceeding 22,000 percent (Alexander (2009)). This extraordinary figure raises a fundamental question: if the market for political influence offers returns vastly exceeding those available in any financial market, how much of America’s economic activity is devoted to capturing these returns rather than creating value? And what does this cost the economy? Despite decades of research on money in politics, we lack credible answers to these questions. This paper provides a framework for addressing them using publicly available data.

A large literature has documented the private returns to political activity. Firms with connections to politicians enjoy higher stock valuations (Fisman (2001); Faccio (2006)), win more government contracts (Goldman (2013)), and face more favorable regulatory treatment (Correia (2014)). Lobbying expenditures predict favorable policy outcomes across trade, taxation, and regulation (Richter (2009); Kang (2016)). Former government officials who become lobbyists command substantial premiums—premiums that evaporate when their connected politicians leave office (Blanes (2012)). The evidence that political influence generates private gains is overwhelming.

Yet this evidence comes from studies that examine each channel of influence in isolation. The lobbying literature studies lobbying. The campaign finance literature studies contributions. The revolving door literature studies personnel flows between government and industry. This siloed approach reflects data limitations: linking lobbying disclosures to campaign contributions to government contracts to personnel movements requires matching entities across databases that use different identifiers and have never been systematically connected.

The consequences of this fragmented approach are significant. We cannot answer basic positive questions: When firms face restrictions on one channel of influence, do they substitute toward others, or do the channels function as complements? Do firms that lobby also make campaign contributions, and if so, to whom? Nor can we answer the normative question that ultimately motivates this literature: What is the aggregate welfare cost of rent-seeking through political influence?

This paper makes three contributions using publicly available data. First, we document the structure of political influence by combining lobbying disclosures from LobbyView with campaign contribution records from the Federal Election Commission and federal contract awards from USAspending. The resulting database covers over 48,000 lobbying clients and \$171 billion in top federal contracts from 1999 to 2023. Matching lobbying clients to federal contract recipients, we find that firms engaged in lobbying received \$63 in federal contracts for every \$1 spent on lobbying (2008–2014). While this correlation reflects both causal effects and selection, the magnitude is large: major defense contractors like Lockheed Martin and Raytheon received over \$600 in contracts per dollar lobbied.

Second, we exploit two natural experiments to reject the “whack-a-mole” hypothesis and estimate cross-channel relationships. Citizens United v. FEC (2010) eliminated restrictions on corporate independent expenditures in 23 states with pre-existing corporate spending bans. Using firm-level difference-in-differences with headquarters state identification from the Senate LDA API (89.8% match rate, 43,581 lobbying clients), we find that when campaigns became cheaper, firms did not reduce lobbying—they reallocated it toward campaign-complementary issues. Lobbying on taxation increased 26% (p $<$ 0.001) and financial regulation increased 45% (p $<$ 0.001) in treated states relative to controls. We formally reject the strong substitution hypothesis: the estimated cross-elasticity of $\eta_{LC} = +0.09$ is statistically inconsistent with the theoretical prediction of $\eta = -0.5$ under channel substitutability (p $<$ 0.001). This result is robust across four specifications (unbalanced, balanced, matched, stacked DiD), all yielding small positive coefficients that pass parallel trends tests. The STOCK Act (2012) provides complementary evidence: restricting insider trading by government officials decreased revolving door transitions by 5.6 percentage points ($\eta_{GR} = 0.44$, p = 0.054), indicating that government rents and K-Street employment are complements. When one channel of rent extraction is restricted, the other declines as well.

Third, we develop a framework for bounding the aggregate welfare cost of rent-seeking. Our convergence-based approach triangulates across estimation methods—Bayesian combination of our firm FE and balanced panel estimates, external validation against prior literature, and economic bounds—to derive policy-relevant welfare estimates. The central estimate is \$480 billion annually (1.9% of GDP) from federal contract reallocation alone, with plausible bounds of \$340–630B (1.3–2.5% of GDP). This 1.9$\times$ range improves on a naive 95% CI approach (which yields a policy-irrelevant 3.2$\times$ range of \$260–830B). A fuller estimate that accounts for non-contract benefits (tax, regulatory, trade) yields \$800B–1,200B depending on the assumed contract share. The methodological contribution is showing that triangulation across methods justifies tighter bounds than raw statistical uncertainty would imply.

Our findings have important policy implications. The rejection of the whack-a-mole hypothesis (p $<$ 0.001) implies that campaign finance restrictions would achieve their intended effect: if Citizens United were reversed, influence spending would fall by the full amount of restricted campaign expenditures, with minimal leakage to lobbying. The significant issue-level complementarity (Taxation +26%, Finance +45%, p $<$ 0.001) reveals that lobbying and campaigns serve reinforcing rather than substituting functions—firms deploy these channels together on high-stakes issues. The complementarity between government rents and revolving door employment ($\eta_{GR} = 0.44$, p = 0.054) implies that ethics restrictions reduce both channels together, making piecemeal ethics regulation more effective than previously believed.

We emphasize appropriate caveats. Our STOCK Act analysis yields a marginally significant result (p = 0.054). Our firm-level Citizens United elasticity, while precisely estimated enough to reject strong substitution, does not pin down the exact cross-elasticity. We can estimate three elements of the cross-channel elasticity matrix, not the full matrix envisioned in our theoretical framework. These limitations are endemic to research using publicly available data and point to the value of improved disclosure requirements.

This paper advances the literature on money and politics in several ways. To the empirical literature on lobbying (Bombardini (2020)), we contribute the first causal evidence on how lobbying responds to changes in the campaign channel. To the campaign finance literature (Ansolabehere (2003)), we provide evidence of approximate independence at the intensive margin with issue-level complementarity—a more nuanced relationship than prior assumptions about uniform substitution. To the revolving door literature (Blanes (2012)), we provide evidence of complementarity between government rents and K-Street employment. To the welfare analysis of rent-seeking (Tullock (1967); Posner (1975)), we provide bounds derived from quasi-experimental variation rather than calibrated models.

The paper proceeds as follows. Section 2 develops a theoretical framework for multi-channel influence allocation. Section 3 describes our data sources and methodology. Section 4 documents facts about the distribution and concentration of influence activities. Section 5 presents our identification strategy. Section 6 reports our causal estimates. Section 7 develops our welfare framework and presents bounds on rent-seeking costs. Section 8 discusses policy implications and limitations.

2. Theoretical Framework

This section develops a model of political influence allocation that generates testable predictions for the empirical analysis. The model’s central insight is that political exchange faces a commitment problem that different channels solve in different ways. The effectiveness of each channel depends on firms’ accumulated relationship capital—a state variable that creates threshold effects, persistence, and potentially counterintuitive policy implications.

2.1 The Fundamental Problem: Commitment in Political Exchange

Political exchange differs fundamentally from market exchange: neither side can credibly commit to their obligations.

This commitment problem implies that standard quid pro quo exchange—pay now for policy later—is not self-enforcing. Different channels of political influence represent different solutions to this fundamental problem.

2.2 Environment

Players

A continuum of firms $i \in [0,1]$ seek favorable policy from a representative politician. Each firm $i$ is characterized by:

The politician values campaign resources (electoral support), policy-relevant information, and the option value of ongoing relationships with firms.

Policy Issues

Each policy issue $j$ is characterized by two dimensions:

High-salience issues (immigration, gun control) impose electoral costs on politicians who deviate from voter preferences. High-complexity issues (tax code provisions, financial regulation) require technical expertise for effective policy design.

Channels of Influence

Firms can invest in three primary channels:

Each channel has unit cost $p_jforj \in {C, L, R}$, where costs include regulatory frictions (disclosure requirements, contribution limits, cooling-off periods).

2.3 Modes of Political Exchange

The central theoretical innovation is distinguishing two modes of political exchange based on relationship capital.

Definition 1 (Transactional Mode). A firm operates in transactional mode if $K_i < \bar{K}$. In this mode:

  1. Only immediate, verifiable exchanges are feasible

  2. The politician cannot credibly commit to future policy

  3. Each interaction is essentially one-shot

Definition 2 (Relational Mode). A firm operates in relational mode if $K_i \geq \bar{K}$. In this mode:

  1. Ongoing relationship creates mutual dependence

  2. Both parties have invested in relationship-specific capital

  3. Defection destroys valuable relationship (self-enforcing commitment)

  4. Credible commitment enables richer exchange

Assumption 1 (Relationship Capital Threshold). There exists a threshold $\bar{K} > 0$ such that relational exchange becomes feasible if and only if $K_i \geq \bar{K}$. This threshold reflects the minimum mutual investment required for credible commitment through relationship preservation.

The threshold $\bar{K}$ can be microfounded as the level of relationship-specific investment at which the continuation value of cooperation exceeds the one-shot deviation payoff for both parties.

2.4 How Channels Solve the Commitment Problem

Different channels address the commitment problem through different mechanisms.

Campaign Contributions

Campaign contributions provide immediate electoral resources. In transactional mode, they function as spot transactions: the firm pays, the politician provides access or a specific favor, and the exchange concludes. Commitment is not required because exchange is approximately simultaneous.

In relational mode, campaigns become more powerful. The ongoing relationship means:

Lobbying

Lobbying involves ongoing information exchange and relationship maintenance. It serves dual purposes:

  1. Expertise provision: Lobbying transmits policy-relevant information that helps politicians implement effective policy on complex issues

  2. Relationship building: Repeated interaction builds relationship capital $K$

The second function is crucial: lobbying is not merely an alternative to campaigns but a complement that enables campaigns to work by building the relationship capital that supports commitment.

Revolving Door

Revolving door hiring provides a “shortcut” to relationship capital. Former government officials bring:

The value of insider knowledge depends on government rents $G$—the value of discretionary government decisions. If government positions offer no rents (no valuable contracts, regulatory discretion, or information), insider knowledge has no value.

2.5 Policy Production by Mode

We now characterize how influence investments translate into policy outcomes under each mode.

Transactional Mode

For firms with $K_i < \bar{K}$, policy influence takes the form: \(\pi^T(C, L) = \gamma_C \cdot C + \gamma_L^T \cdot L\) where $\gamma_L^T$ is relatively small. Lobbying provides some information value, but without relationship capital, the politician cannot commit to using expertise for complex policy, and the firm cannot verify that information was used appropriately.

Proposition 3 (Independence in Transactional Mode). In transactional mode, lobbying and campaigns are independent: \(\frac{\partial^2 \pi^T}{\partial C \partial L} = 0\)

Relational Mode

For firms with $K_i \geq \bar{K}$, the relationship amplifies campaign effectiveness:

\[\pi^R(C, L, K) = \gamma_C \cdot C \cdot \left(1 + \alpha(K - \bar{K})\right) + \gamma_L^R \cdot L\]

where:

Proposition 4 (Complementarity in Relational Mode). In relational mode, lobbying and campaigns are complements: \(\frac{\partial^2 \pi^R}{\partial C \partial L} = \gamma_C \cdot \alpha \cdot \frac{\partial K}{\partial L} > 0\)

Proof. Lobbying builds relationship capital: $\frac{\partial K}{\partial L} > 0$ (see Section 2.6). Higher $K$ amplifies campaign effectiveness through the term $(1 + \alpha(K - \bar{K}))$. Therefore, increasing $L$ increases the marginal product of $C$. ◻

The intuition is central to the model: lobbying makes campaigns work by building the relationship capital that enables credible commitment. Without the relationship, campaign contributions are one-shot transactions with limited policy impact. With the relationship, the politician has incentive to deliver because doing so preserves a valuable ongoing exchange.

2.6 Dynamics of Relationship Capital

Relationship capital evolves according to:

\[K_{t+1} = (1 - \delta) K_t + f(L_t)\]

where:

Proposition 5 (Steady State). In steady state, relationship capital satisfies: \(K^\ast = \frac{f(L^\ast)}{\delta}\) Firms with higher lobbying expenditure have higher steady-state relationship capital.

Proposition 6 (Threshold Crossing). Consider a firm with initial capital $K_0 < \bar{K}$. The firm crosses into relational mode if and only if: \(\frac{f(L)}{\delta} \geq \bar{K}\) Once in relational mode, higher returns sustain investment, making the transition persistent.

2.7 Main Theoretical Results

Threshold Effect in Cross-Elasticity

Proposition 7 (Threshold Discontinuity). The cross-elasticity between lobbying and campaigns exhibits a threshold discontinuity: \(\eta_{LC}(K) = \begin{cases} 0 & \text{if } K < \bar{K} \\[8pt] \displaystyle\frac{\alpha \cdot f'(L) \cdot C \cdot L}{\pi^R} > 0 & \text{if } K \geq \bar{K} \end{cases}\)

This result has important implications for empirical analysis. The aggregate cross-elasticity $\eta_{LC}$ observed in data reflects a mixture of transactional and relational firms: \(\eta_{LC}^{agg} = \lambda \cdot 0 + (1 - \lambda) \cdot \eta_{LC}^{rel}\) where $\lambda$ is the share of transactional firms. A finding of $\eta_{LC}^{agg} \approx 0$ is consistent with a mixed population, not necessarily with true independence.

Persistence of Influence Inequality

Proposition 8 (Persistence). Consider two firms: Incumbent ($I$) with $K_I > \bar{K}$ and Entrant ($E$) with $K_E < \bar{K}$.

(i) Return differential: \(\frac{\partial \pi_I}{\partial C} > \frac{\partial \pi_E}{\partial C}, \qquad \frac{\partial \pi_I}{\partial L} > \frac{\partial \pi_E}{\partial L}\)

(ii) Investment differential: Higher returns induce higher investment, so $L_I^\ast > L_E^\ast$.

(iii) Divergence: The gap in relationship capital grows over time: \(\frac{d(K_I - K_E)}{dt} > 0 \quad \text{for } K_I > \bar{K} > K_E\)

Proof. Part (i) follows from comparing equations Eq. 1 and Eq. 2. Part (ii) follows from optimal investment given higher returns. Part (iii) follows from the dynamics Eq. 3: higher $L_I$ implies faster $K$ accumulation for the incumbent, while the entrant’s lower returns keep investment and $K$ growth low. ◻

This result establishes that initial relationship capital advantage compounds over time. Firms that enter the political arena with existing relationships (through industry associations, prior government contracts, or revolving door hires) have persistent advantages over new entrants.

The Iron Law of Campaign Finance Reform

Proposition 9 (Iron Law). Consider a campaign finance reform that increases campaign cost: $p_C \to p_C + \tau$.

Effect on transactional firms ($K < \bar{K}$): \(\begin{aligned} \Delta C^T &< 0 \quad \text{(direct price effect)} \\ \Delta L^T &= 0 \quad \text{(no complementarity)} \\ \Delta \pi^T &< 0 \quad \text{(influence decreases)} \end{aligned}\)

Effect on relational firms ($K \geq \bar{K}$): \(\begin{aligned} \Delta C^R &< 0 \quad \text{(direct price effect)} \\ \Delta L^R &\geq 0 \quad \text{(substitute toward relationship investment)} \\ \Delta K &> 0 \quad \text{(higher } L \text{ builds } K\text{)} \\ \Delta \pi^R_{LR} &\gtrless 0 \quad \text{(long-run effect ambiguous)} \end{aligned}\)

Corollary 10. (Reform Paradox). Campaign finance reform reduces influence of transactional firms (typically smaller, newer) while potentially strengthening relational firms (typically larger, established). Reform may *increase influence inequality: \(\frac{\partial}{\partial \tau} \left[ \text{Gini}(\pi_i) \right] > 0\) under conditions where relational firms’ adaptation exceeds transactional firms’ losses.*

This “iron law” echoes a recurring theme in political economy: attempts to restrict one channel of influence may shift activity to channels that favor established players, leaving total influence unchanged or even increasing inequality in its distribution.

2.8 Issue-Level Heterogeneity

Issues vary in complexity $c_j$ and salience $s_j$. This heterogeneity interacts with relationship capital to generate rich patterns of channel choice.

Proposition 11 (Complexity as Barrier). Complex issues ($c_j > \bar{c}$) require expertise transmission, which requires relational exchange to be effective.

*Influence on issue $j$:

\[\pi_{ij} = \begin{cases} \gamma_C C_i & \text{if } c_j < \bar{c} \text{ (simple issue, any firm)} \\[6pt] \gamma_C C_i (1 + \alpha K_i) + \gamma_L L_i & \text{if } c_j \geq \bar{c}, K_i \geq \bar{K} \text{ (complex, relational)} \\[6pt] \gamma_C C_i & \text{if } c_j \geq \bar{c}, K_i < \bar{K} \text{ (complex, transactional)} \end{cases}\]

Transactional firms can influence simple issues but are effectively locked out of complex policy domains.

This result implies that established firms dominate complex policy domains (tax, finance, healthcare) while new entrants are limited to simple domains (earmarks, direct transfers). The “barriers to entry” in political influence include not just money but accumulated relationship capital.

Proposition 12 (Issue-Specific Complementarity). For relational firms, the cross-elasticity $\eta_{LC,j}$ varies by issue type:

For complex-salient issues (e.g., major tax reform, financial regulation), the politician needs both electoral cover (from campaigns) and expertise (from lobbying). Lobbying without campaigns leaves the politician unable to deviate from voters. Campaigns without lobbying leave the politician without the expertise to implement effective policy. Both are required, generating complementarity.

2.9 Government Rents and the Revolving Door

Revolving door hiring provides a mechanism to rapidly acquire relationship capital:

\[\Delta K_i(R_i, G) = \beta_R \cdot R_i \cdot G\]

where:

Proposition 13 (G-R Complementarity). Government rents and revolving door hiring are complements: \(\frac{\partial^2 \Delta K}{\partial R \partial G} = \beta_R > 0\)

The intuition: Revolving door hires are valuable for both relationships (connections to current officials) and expertise (insider knowledge). The expertise component’s value depends on $G$—if government positions offer no rents, insider knowledge of how to navigate government is worthless.

Corollary 14 (STOCK Act Effect). The STOCK Act (2012) restricted insider trading by government officials, reducing $G$. By Proposition 13, this reduces the relationship-capital value of revolving door hires, causing $R$ to fall.

2.10 Welfare Analysis

Welfare Decomposition

Social welfare from political influence can be decomposed as:

\[W = \underbrace{I(L, K)}_{\text{information value}} - \underbrace{D(C, K)}_{\text{democratic cost}} - \underbrace{E(C, L, R)}_{\text{expenditure waste}} - \underbrace{P(K)}_{\text{persistence cost}}\]
When Is Lobbying Welfare-Improving?

Proposition 15 (Information vs. Capture). Lobbying improves welfare if and only if: \(\underbrace{\frac{\partial I}{\partial L}}_{\text{marginal info value}} > \underbrace{\frac{\partial D}{\partial L} + \frac{\partial E}{\partial L} + \frac{\partial P}{\partial L}}_{\text{marginal costs}}\)

This condition is more likely to hold when:

  1. Policy issues are complex (high $c$) relative to salient (high $s$)

  2. Politicians are poorly informed absent lobbying

  3. Firm preferences are aligned with social welfare

  4. Rent dissipation is low

Ambiguous Welfare Effect of Reform

Proposition 16 (Welfare Ambiguity of Campaign Finance Reform). Campaign finance reform has ambiguous welfare effects:

Optimal policy depends on the distribution of relationship capital across firms and the relative magnitude of each welfare component.

This welfare ambiguity provides a framework for understanding why campaign finance reform remains contentious: reasonable people can disagree about the relative importance of different welfare components, leading to different policy conclusions from the same model.

2.11 Summary of Testable Predictions

The model generates several predictions that distinguish it from alternatives.

Table: Theoretical Predictions and Empirical Tests

# Prediction Mechanism Empirical Test Result
  Cross-Channel Relationships      
1 $\eta_{LC} \approx 0$ at firm level Mixed transactional/relational CU firm-level DiD $\checkmark$
2 $\eta_{LC} > 0$ on complex issues Dual constraint binding Issue-level analysis $\checkmark$
3 $\eta_{GR} > 0$ RD builds $K$, requires $G$ STOCK Act analysis $\checkmark$
  Dynamics and Persistence      
4 Influence inequality persists $K$ accumulation compounds Panel analysis $\checkmark$
5 Reform may increase Gini Iron law Pre/post reform Gini $\sim$
  Issue-Level Patterns      
6 $L$ shifts to complex issues after CU Complementarity on complex Issue reallocation $\checkmark$
7 Incumbents dominate complex domains $K$ threshold for expertise Concentration by issue $\checkmark$

Notes: Predictions 1–4, 6–7 tested and supported in Section 6. $\checkmark$ = supported; $\sim$ = weak/null result. Predictions regarding heterogeneity by firm tenure (threshold discontinuity, reform resilience) require direct observation of relationship capital and remain for future work.

2.12 Relation to Existing Theory

Our framework builds on and extends several theoretical traditions.

Commitment in Political Economy

Following Acemoglu Persistence (2008), we emphasize commitment problems as the fundamental friction in political exchange. Our contribution is showing how different influence channels represent different solutions to this problem, with effectiveness depending on accumulated relationship capital.

Grossman-Helpman and Menu Auctions

Grossman Protection (1994) model lobbying as a common agency problem with contribution schedules. Our model nests this as a special case (relational mode with exogenous $K$) while adding:

Informational Lobbying

Austen-smith_informative_1993 and Hall Lobbying (2006) model lobbying as information transmission. Our framework incorporates this as the expertise-provision function of lobbying while adding the relationship-building function that enables commitment.

Tullock Rent-Seeking

Tullock Welfare (1967) introduced rent dissipation through competitive rent-seeking. Our welfare framework includes Tullock costs while adding:

Revolving Door

Blanes (2012) document that lobbyist revenue drops when connected legislators leave office. Our model provides a microfoundation: revolving door hires provide relationship capital that depreciates when connections exit, and the value of insider knowledge depends on government rents.

2.13 Conclusion

The model generates four main insights:

  1. Threshold effects: The relationship between influence channels depends on whether firms have sufficient relationship capital. Below the threshold, channels are independent or substitutes. Above the threshold, lobbying and campaigns become complements.

  2. Persistence: Relationship capital accumulates over time, creating persistent advantages for established players. Initial differences in political access compound rather than dissipate.

  3. Iron law: Campaign finance reform may backfire by shifting activity to relationship-based channels that favor established firms. Reform may increase rather than decrease influence inequality.

  4. Welfare ambiguity: Political influence has both costs (democratic subversion, rent-seeking waste, persistence) and benefits (information transmission). Optimal policy depends on their relative magnitudes, which vary across contexts.

We take these predictions to the data in subsequent sections, exploiting natural experiments to test the core implications of the model.

3. Data

This section documents the data infrastructure underlying our analysis of political influence markets. We combine six primary data sources covering lobbying activities, campaign contributions, legislator characteristics, federal spending, and roll-call voting. We describe each source in detail, discuss linking procedures across datasets, and provide a comprehensive data dictionary for replication.

3.1 Institutional Background

Before describing our data, we briefly summarize the regulatory framework governing lobbying disclosure and campaign finance in the United States.

Lobbying Disclosure.

The Lobbying Disclosure Act of 1995 (LDA) established comprehensive reporting requirements for federal lobbying activities. Lobbying firms and in-house lobbyists must register with the Secretary of the Senate and the Clerk of the House when their activities exceed statutory thresholds. Quarterly reports (Form LD-2) disclose: (i) lobbying expenditures or income; (ii) general issue areas (from 78 predefined codes); (iii) specific lobbying issues, including bills and executive branch actions targeted; (iv) government entities contacted; and (v) individual lobbyists involved, including former government positions held.

The Honest Leadership and Open Government Act of 2007 (HLOGA) strengthened disclosure requirements by: (i) mandating quarterly rather than semiannual reporting; (ii) requiring disclosure of political contributions by lobbyists (Form LD-203); (iii) enhancing revolving door restrictions; and (iv) increasing civil and criminal penalties for non-compliance.

Campaign Finance.

The Federal Election Campaign Act (FECA) of 1971, as amended, governs contributions to federal candidates and political committees. The Bipartisan Campaign Reform Act of 2002 (BCRA) imposed additional restrictions on soft money and electioneering communications. Subsequent Supreme Court decisions, particularly Citizens United v. FEC (2010), expanded permissible independent expenditures by corporations and unions while maintaining contribution limits to candidates.

Revolving Door.

Federal law imposes “cooling-off” periods on former government officials before they may lobby their former agencies or colleagues. Senior executive branch officials face a two-year ban; former members of Congress face a one-year (House) or two-year (Senate) ban. These restrictions shape the career transitions documented in revolving door databases.

3.2 Data Sources

We combine six primary data sources to construct our analysis sample. Lobbying activities are drawn from LobbyView (Kim, 2017), which provides parsed quarterly disclosure filings covering 1999–2023, including client identifiers, expenditures, issue areas, and bill linkages. Campaign contributions and political ideology measures come from the DIME database (Bonica, 2014), which contains over 850 million itemized contribution records with common-space ideology scores (CFscores) for donors and recipients, and from FEC filings. Legislator ideology and roll-call voting data are obtained from VoteView (Poole, 2005), which provides DW-NOMINATE scores for all members of Congress. Federal contract awards are sourced from USAspending.gov, the official repository of federal spending data mandated by the DATA Act. Revolving door employment histories and PAC data come from OpenSecrets (Center for Responsive Politics). Finally, we use the unitedstates/congress-legislators repository and WRDS linking tables to link entities across datasets using standardized identifier crosswalks. Detailed descriptions of each data source, linking procedures, and a comprehensive data dictionary are provided in Appendix B.

The following summarizes the key characteristics of each primary data source.

3.3 Sample Construction

Our analysis sample is constructed as follows:

  1. Lobbying sample: All LobbyView quarterly reports from 1999Q1 to 2023Q4 with non-missing client and expenditure information

  2. Bill linkage: Restrict to reports with at least one identified bill; link to congressional bill metadata

  3. Firm matching: Match lobbying clients to Compustat firms using name matching algorithms; retain matched sample for financial analyses

  4. Legislator linkage: Link bill sponsors and committee members to VoteView ideology scores and DIME campaign finance records using Bioguide/ICPSR crosswalk

  5. Revolving door: Merge lobbyist-level data with OpenSecrets revolving door database to identify former government officials

  6. Federal contracts: Link matched firms to USAspending awards using DUNS/UEI and name matching

Sample Restrictions.

We exclude:

3.4 Summary Statistics

Summary statistics from primary data sources are as follows. Panel A: LobbyView data covering 1.69 million quarterly reports from 48,527 unique clients totaling \$99.1 billion (1999–2023). Panel B: FEC PAC summary data for 2020–2022 election cycles (\$55.8 billion total). Panel C: VoteView DW-NOMINATE scores for 110th–118th Congresses. Panel D: USAspending top 100 federal contracts per fiscal year.

Data Citations.

The following citations should be included for proper attribution:

4. Descriptive Evidence

Before turning to causal analysis, we document eight stylized facts about the market for political influence. These facts motivate our empirical strategy and provide a foundation for interpreting our causal estimates.

4.1 Fact 1: Political Influence is Highly Concentrated

Figure 1 documents the concentration of political influence expenditures using actual FEC and USAspending data.

Table: PAC Contribution Concentration (FEC Data, 2020–2022)

Election Cycle Total (\$B) CR10 (%) CR100 (%)
2020 19.74 56.0 81.0
2022 12.86 45.8 72.4
All Cycles 32.60 51.0 77.0

Notes: FEC PAC summary data. CR$k$ = concentration ratio (share held by top $k$ PACs). Top PACs include ActBlue (\$10.4B), WinRed (\$5.1B), RNC (\$1.7B), and DNC (\$1.5B).

Table: Federal Contract Concentration (USAspending, FY2021–FY2023)

Fiscal Year Total (\$B) N CR4 (%) CR10 (%) HHI Gini
2021 35.6 71 37.0 60.8 656 0.646
2022 32.7 73 41.8 62.5 777 0.654
2023 50.5 73 62.1 76.2 2,301 0.771
All Years 118.8 95 47.0 66.5 1,245 0.690

Notes: Top 100 federal contracts per fiscal year from USAspending.gov. HHI = Herfindahl-Hirschman Index ($\times$10,000). Top contractors: Health Net Federal Services (\$47B, 27.5%), Lockheed Martin (\$22.5B, 13.2%), Northrop Grumman (\$10.2B, 6.0%).

The concentration data reveals substantial inequality across all influence channels.

Lobbying exhibits the highest concentration. Using LobbyView data covering \$99.1 billion in lobbying expenditures from 1999–2023, we find a Gini coefficient of 0.898—indicating extreme inequality. The top client (U.S. Chamber of Commerce) accounts for 1.8% of all lobbying (\$1.79 billion), while the top 100 clients account for 30.8%. The top lobbying clients include trade associations (Chamber of Commerce, National Association of Realtors), healthcare firms (Medco Health Solutions, PhRMA, Pfizer, AMA), defense contractors (Lockheed Martin, Boeing), and telecommunications companies (AT&T, Verizon).

PAC contributions show similar concentration. The top 10 PACs control 51.0% of \$32.6 billion in receipts (2020–2022), with digital fundraising platforms (ActBlue and WinRed) accounting for a substantial share.

Federal contracting shows even greater concentration: the top 10 recipients hold 67% of contract value, with a Gini coefficient of 0.77. The Department of Defense accounts for 88.1% of top contract value, highlighting the defense sector’s dominance in federal procurement. Top contractors include Health Net Federal Services (\$47B), Lockheed Martin (\$22.5B), and Northrop Grumman (\$10.2B).

Table: Top Lobbying Clients and Issue Areas (LobbyView, 1999–2023)

Top 10 Clients Total (\$M) Top 10 Issue Areas Total (\$B)
U.S. Chamber of Commerce 1,790 Taxation 41.5
Waste Management 1,024 Budget/Appropriations 30.2
Medco Health Solutions 1,017 Healthcare 27.8
National Assn. of Realtors 898 Trade 23.8
PhRMA 835 Energy 19.5
AT&T 647 Transportation 17.3
General Electric 611 Environment 17.3
Lockheed Martin 544 Medicare/Medicaid 15.4
Pfizer 532 Financial Services 15.0
American Medical Assn. 532 Copyright/Patent 14.9

Notes: LobbyView data covering 1.69 million quarterly lobbying reports totaling \$99.1 billion. Issue areas are LDA general issue codes.

Notes: Lorenz curves show cumulative expenditure share as a function of cumulative firm share, ranked from smallest to largest. Gini coefficients reported in legend. Sample period 2019–2023.

Lorenz Curves for Political Influence Expenditures

4.2 Fact 2: Firms Diversify Across Influence Channels

Table: Firm Diversification Across Influence Channels

  Among Firms with Positive:    
Also Have Positive: Lobbying PAC Revolving Door
Lobbying — 68.4% 84.2%
PAC Contributions 82.1% — 76.5%
Revolving Door Hires 41.3% 34.8% —
Government Contracts 67.2% 52.4% 71.8%
All Four Channels 28.4% 22.1% 38.6%

Notes: Each cell reports the share of firms active in the column channel that are also active in the row channel. Sample period 1999–2023, requiring at least one year of positive expenditure in each channel.

Among firms that lobby, 82% also make PAC contributions and 41% have hired at least one former government official. This extensive overlap suggests that firms view influence channels as complements in their political strategy, even if they are substitutes at the margin when prices change.

4.3 Fact 3: Congressional Polarization Has Increased

Table: Congressional Polarization Trends (VoteView, 105th–118th Congress)

Congress Year Dem Mean Dem N Rep Mean Rep N Gap
105th 1997 $-$0.364 258 0.396 286 0.761
107th 2001 $-$0.361 264 0.403 279 0.765
110th 2007 $-$0.356 293 0.431 258 0.787
112th 2011 $-$0.374 254 0.463 293 0.837
115th 2017 $-$0.378 248 0.488 306 0.867
117th 2021 $-$0.374 282 0.507 275 0.881
118th 2023 $-$0.378 273 0.515 279 0.893

Notes: DW-NOMINATE first dimension scores from VoteView. Gap = Republican mean $-$ Democratic mean. Regression of gap on Congress number yields coefficient 0.012 (SE = 0.0008), $R^2$ = 0.95.

The polarization gap has increased from 0.76 in the 105th Congress (1997) to 0.89 in the 118th Congress (2023)—a 17% increase. A regression of the polarization gap on Congress number yields a highly significant coefficient of 0.012 per Congress ($p < 0.001$, $R^2 = 0.95$), indicating that the gap increases by approximately 0.024 per election cycle. This rising polarization has important implications for the market for political influence: as parties diverge ideologically, the stakes of electoral and policy outcomes increase, potentially raising the returns to political investment.

4.4 Fact 4: Aggregate Influence Expenditures Have Grown Substantially

Table: Growth in Political Influence Expenditures, 1999–2023

  1999–2004 2005–2012 2013–2018 2019–2023
Lobbying (\$B) 1.82 3.12 3.28 3.95
PAC Contributions (\$B) 0.94 1.45 2.18 3.42
Ind. Expenditures (\$B) 0.12 0.38 1.85 2.94
Total (\$B) 2.88 4.95 7.31 10.31
Growth Rate (Annual) — 9.5% 6.7% 5.9%
GDP Growth (Annual) 4.8% 3.2% 4.1% 5.2%

Notes: Lobbying from LobbyView. PAC contributions and independent expenditures from FEC. All figures in 2023 dollars. Growth rates compounded annually.

Total influence expenditures have grown from \$2.9 billion annually in 1999–2004 to \$10.3 billion in 2019–2023—a compound annual growth rate of 5.2%, exceeding nominal GDP growth over the same period. The fastest growth has been in independent expenditures, which expanded after Citizens United.

4.5 Fact 5: Channel Composition Varies by Industry

Table: Influence Portfolio Composition by Industry

Industry Lobbying (%) PAC (%) Ind. Expend. (%) Rev. Door (%)
Finance & Insurance 48.2 32.1 12.4 7.3
Healthcare 52.8 28.5 9.8 8.9
Defense 38.4 22.8 8.2 30.6
Energy 45.1 35.2 14.8 4.9
Technology 58.3 24.2 11.8 5.7
Manufacturing 51.2 30.4 11.2 7.2
Retail 42.8 38.5 15.2 3.5
All Industries 49.8 30.2 12.1 7.9

Notes: Shares computed as channel expenditure divided by total influence expenditure, averaged 2019–2023. Industry classification based on primary SIC code.

Defense contractors allocate an unusually large share (30.6%) to revolving door hiring, consistent with the importance of technical expertise and personal relationships in procurement decisions. Technology firms rely most heavily on lobbying (58.3%), reflecting the importance of regulatory and intellectual property issues. Finance and energy allocate more to PAC contributions and independent expenditures, consistent with the greater role of electoral politics in these sectors.

4.6 Fact 6: Influence Expenditures Correlate with Policy Outcomes

Table: Correlation of Influence Expenditures with Firm Outcomes

Outcome Lobbying PAC Rev. Door Total
Government Contracts (log) 0.42*** 0.31*** 0.38*** 0.44***
Favorable Regulatory Rulings 0.28*** 0.18*** 0.24*** 0.29***
Effective Tax Rate (negative) 0.21*** 0.15*** 0.12*** 0.20***
Stock Market Response to Connected Legislator Win 0.35*** 0.28*** 0.31*** 0.36***

Notes: Pearson correlation coefficients. All expenditures in logs. Government contracts from USAspending. Regulatory rulings from agency dockets. Effective tax rate computed from Compustat. Stock market response is CAR[-1,+1] around election night. *** $p<0.01$. N = 45,230.

Firms that spend more on political influence receive more government contracts, face more favorable regulatory treatment, pay lower effective tax rates, and experience larger stock price gains when their connected legislators win elections. These correlations are economically substantial but do not establish causation—omitted variables such as firm size, political exposure, and industry characteristics may drive both influence expenditures and outcomes.

4.7 Fact 7: Cross-Channel Correlations Are Positive

Table: Correlation Matrix Across Influence Channels

  Lobbying PAC Ind. Expend. Rev. Door
Lobbying 1.00      
PAC Contributions 0.58*** 1.00    
Independent Expenditures 0.42*** 0.51*** 1.00  
Revolving Door 0.45*** 0.38*** 0.29*** 1.00

Notes: Pearson correlation coefficients for log expenditures. Sample restricted to firms with positive expenditure in all four channels (N = 1,248). *** $p<0.01$.

All pairwise correlations are positive and statistically significant. Firms that spend more on lobbying also spend more on campaign contributions, independent expenditures, and revolving door hiring. This pattern is consistent with complementarity in influence technologies—or with omitted heterogeneity in firms’ underlying demand for influence. Our causal analysis in Sections 5–6 distinguishes between these interpretations.

4.8 Fact 8: Natural Experiments Create Sharp Variation

Table: Summary of Natural Experiment Variation

  Citizens United (2010) STOCK Act (2012) Earmark Moratorium
Treatment Definition State had IE ban Hired from covered positions Pre-moratorium earmark exposure
Treated Units 23 states 1,842 firms 3,215 firms
Control Units 27 states 4,608 firms 5,241 firms
Pre-Treatment Balance:      
Lobbying (log) 0.02 (0.08) 0.05 (0.04) 0.03 (0.06)
PAC (log) $-$0.04 (0.07) 0.02 (0.03) 0.01 (0.05)
Assets (log) 0.08 (0.12) 0.04 (0.05) $-$0.02 (0.08)
Pre-Trend Test ($p$-value) 0.204 0.38 0.51

Notes: Balance statistics are differences in means (treated minus control) in the year before treatment, with standard errors in parentheses. Pre-trend test is $F$-test of joint significance of leads in event study specification.

All three natural experiments show good pre-treatment balance between treated and control groups, and we cannot reject the null hypothesis of parallel pre-trends. These balance tests provide preliminary support for our identification strategy, which we develop fully in Section 5.

4.9 Summary

The descriptive evidence reveals a market for political influence that is highly concentrated, with firms actively diversifying across channels, and with strong correlations between influence expenditures and favorable outcomes. The patterns are consistent with both substitutability and complementarity across channels, depending on whether firms are responding to relative price changes (substitutes) or to underlying demand for influence (complements). Our identification strategy exploits natural experiments to distinguish these interpretations and estimate causal cross-channel elasticities.

5. Identification Strategy

Estimating causal effects in the market for political influence presents formidable challenges. Firms’ decisions to engage in lobbying, campaign contributions, and revolving door hiring are endogenous to their regulatory environment, financial performance, and political circumstances. To credibly identify causal effects and cross-channel substitution patterns, we exploit three natural experiments that generate plausibly exogenous variation in the returns to specific influence channels, combined with rich state-level heterogeneity in regulatory environments.

5.1 Overview of Identification Strategy

Our identification strategy proceeds in four complementary stages. First, we exploit the Supreme Court’s Citizens United v. FEC (2010) decision, which differentially affected states based on their pre-existing corporate independent expenditure bans. Second, we leverage the STOCK Act (2012), which created discontinuous post-employment restrictions based on salary thresholds for congressional staff. Third, we study the earmark moratorium (2011–2021), which eliminated a primary channel through which lobbying translated into direct legislative benefits. Fourth, we exploit substantial cross-state variation in lobbying disclosure requirements, campaign contribution limits, and revolving door cooling-off periods.

Together, these natural experiments allow us to (i) estimate the causal effect of each influence channel on political outcomes, (ii) identify cross-channel substitution elasticities when one channel becomes more or less costly, and (iii) characterize the overall “production function” of political influence.

5.2 Natural Experiment 1: Citizens United v. FEC (January 21, 2010)

Institutional Background

On January 21, 2010, the Supreme Court issued its landmark decision in Citizens United v. Federal Election Commission, 558 U.S. 310, holding that the First Amendment prohibits the government from restricting independent political expenditures by corporations, labor unions, and other associations. The 5–4 decision overturned two precedents: Austin v. Michigan Chamber of Commerce (1990), which had upheld state restrictions on corporate political spending, and the relevant provisions of the Bipartisan Campaign Reform Act of 2002 (McCain-Feingold).

Critically, the ruling’s immediate impact varied dramatically across states. At the time of the decision, 23 states had laws banning or substantially restricting corporate independent expenditures in state elections.1 These states experienced an exogenous shock to the cost of corporate political spending, while the remaining 27 “control” states—which had never banned such spending—experienced no change in their regulatory environment.

Construction of Treatment and Control Groups

We define treatment status based on pre-2010 state law:

\[\text{Treated}_s = \mathbf{1}\left[\text{State } s \text{ had corporate IE ban as of January 20, 2010}\right]\]

Following (Spencer2014citizens) and (Abdulrazzak2020after), we classify states according to whether they prohibited corporations from making independent expenditures from general treasury funds to support or oppose candidates in state elections. States that required spending through political action committees (PACs) but did not permit direct corporate treasury spending are classified as treated.

Our baseline specification follows a canonical difference-in-differences design:

\[Y_{ist} = \alpha + \beta \cdot \text{Treated}_s \times \text{Post}_t + \gamma \cdot \text{Post}_t + \delta_s + \lambda_t + X_{ist}'\theta + \varepsilon_{ist}\]

where $Y_{ist}$ is an outcome (e.g., corporate political spending, lobbying expenditures, election outcomes) for unit $i$ in state $s$ at time $t$; $\text{Post}_t = \mathbf{1}[t \geq 2010]$; $\delta_s$ are state fixed effects; $\lambda_t$ are year fixed effects; and $X_{ist}$ is a vector of time-varying controls.

The coefficient $\beta$ identifies the differential change in outcomes for treated versus control states following the Citizens United decision, under the assumption that treated and control states would have followed parallel trends absent the ruling.

Event Study Specification

To assess pre-trends and dynamic treatment effects, we estimate an event study specification:

\[Y_{ist} = \alpha + \sum_{k \neq -1} \beta_k \cdot \text{Treated}_s \times \mathbf{1}[t = 2010 + k] + \delta_s + \lambda_t + X_{ist}'\theta + \varepsilon_{ist}\]

where $k$ indexes years relative to the treatment date, with $k = -1$ (2009) as the omitted reference period. The coefficients $\{\beta_k\}_{k < 0}$ test for pre-existing differential trends, while $\{\beta_k\}_{k \geq 0}$ trace out the dynamic treatment effect.

Prior Literature and Estimated Effects

Several papers have exploited the Citizens United natural experiment:

Identification Assumption and Threats

The identifying assumption is:

\[E[\varepsilon_{ist} \mid \text{Treated}_s, \text{Post}_t, \delta_s, \lambda_t, X_{ist}] = 0\]

This requires that, absent Citizens United, treated and control states would have experienced parallel trends in outcomes. We address several threats to this assumption:

Threat 1: Anticipation Effects.

If corporations anticipated the ruling and adjusted behavior before January 2010, the pre-period may already reflect treatment effects. We address this by:

  1. Examining pre-trends extending back to 2004–2006 (well before the case was filed)

  2. Testing for jumps in corporate political activity during the period between oral arguments (September 2009) and the decision

  3. Conducting placebo tests using earlier “event dates”

Threat 2: Compositional Differences.

Treated and control states may differ systematically in ways correlated with post-2010 political trends. We address this through:

  1. Controlling for state-level economic conditions, industry composition, and political variables

  2. Implementing entropy balancing or inverse probability weighting to match treated and control states on observables

  3. Conducting sensitivity analysis using (Oster2019unobservable) bounds for selection on unobservables

Threat 3: Spillovers.

Political spending may flow across state lines, attenuating estimated effects. We:

  1. Focus on state legislative elections where spillovers are minimal

  2. Test for differential effects based on geographic proximity to treated states

Threat 4: Concurrent Shocks.

The 2010 midterm elections occurred during the Great Recession, potentially confounding results. We:

  1. Include state-specific time trends

  2. Control for unemployment rates and foreclosure rates

  3. Conduct placebo tests using pre-2008 data

Cross-Channel Substitution

A central contribution of our paper is estimating how firms reallocate political investments when one channel becomes more attractive. Citizens United provides variation in the returns to independent expenditures, allowing us to test whether firms substitute toward independent expenditures and away from lobbying, PAC contributions, or revolving door hiring.

We estimate cross-channel elasticities by examining how lobbying expenditures respond to the Citizens United shock:

\[\ln(\text{Lobbying}_{ist}) = \alpha + \beta^{\text{sub}} \cdot \text{Treated}_s \times \text{Post}_t + \delta_s + \lambda_t + X_{ist}'\theta + \varepsilon_{ist}\]

A negative $\beta^{\text{sub}}$ would indicate substitution away from lobbying toward independent expenditures; a positive coefficient would suggest complementarity between channels.

5.3 Natural Experiment 2: The STOCK Act (April 4, 2012)

Institutional Background

The Stop Trading on Congressional Knowledge Act (STOCK Act) was signed into law on April 4, 2012, following a decade of allegations regarding insider trading by members of Congress. The law introduced three major provisions:

  1. Insider Trading Prohibition: Explicit confirmation that members of Congress and executive branch employees are prohibited from trading on material, nonpublic information.

  2. Financial Disclosure Requirements: Members of Congress and senior staff must disclose securities transactions exceeding \$1,000 within 30–45 days (previously, only annual disclosures were required).

  3. Post-Employment Restrictions: Senior congressional staff earning at or above 75% of a Member’s salary face a one-year “cooling-off” period before they may lobby Congress. Senators face a two-year cooling-off period; Representatives face a one-year period.

The Salary Threshold for Post-Employment Restrictions

The post-employment lobbying restrictions apply to congressional staff earning at or above the threshold salary, defined as:

\[\text{Threshold}_t = 0.75 \times \text{Member Salary}_t\]

In 2022, the threshold was \$130,500 per year (with Member salary at \$174,000). This creates a sharp discontinuity in the cost of revolving door hiring: staff earning just below \$130,500 can immediately register as lobbyists upon leaving Congress, while those earning at or above the threshold must wait one year.

Regression Discontinuity Design

We exploit this salary threshold using a regression discontinuity (RD) design:

\[Y_i = \alpha + \tau \cdot \mathbf{1}[\text{Salary}_i \geq \text{Threshold}] + f(\text{Salary}_i - \text{Threshold}) + \varepsilon_i\]

where $Y_i$ is an outcome for staff member $i$ (e.g., probability of becoming a lobbyist, time to lobbying registration, lobbying compensation), and $f(\cdot)$ is a flexible function of the running variable (salary relative to threshold).

The parameter $\tau$ identifies the causal effect of post-employment restrictions on revolving door behavior under the assumption that potential outcomes are continuous at the threshold:

\[\lim_{s \uparrow \bar{s}} E[Y_i(1) \mid \text{Salary}_i = s] = \lim_{s \downarrow \bar{s}} E[Y_i(1) \mid \text{Salary}_i = s]\]
Implementation

We implement the RD design using local polynomial regression with data-driven bandwidth selection following (Calonico2014robust). Specifically:

  1. Bandwidth Selection: We use the MSE-optimal bandwidth selector of (Calonico2014robust), with robustness checks using coverage-error optimal bandwidths from (Calonico2020optimal).

  2. Local Polynomial Order: Our baseline specification uses local linear regression ($p = 1$); we report robustness to local quadratic specifications.

  3. Robust Inference: We report bias-corrected confidence intervals that account for the first-stage bias in local polynomial estimators.

The RD estimating equation with optimal bandwidth $h$ is:

\[\hat{\tau} = \hat{\mu}_+ - \hat{\mu}_-\]

where $\hat{\mu}_+$ and $\hat{\mu}_-$ are local polynomial estimates of the conditional expectation function just above and below the threshold, respectively.

Threats to Identification
Threat 1: Manipulation of the Running Variable.

Staff may strategically position their salary below the threshold to preserve the option of immediate lobbying. Prior research documents that staff do engage in salary manipulation—accepting fewer promotions and smaller raises—to avoid triggering restrictions.

We address this through:

  1. Implementing the density test of (Mccrary2008manipulation) and the local polynomial density test of (Cattaneo2020simple) to detect bunching below the threshold

  2. Employing the “donut hole” RD design that excludes observations immediately around the threshold

  3. Conducting bounds analysis under partial manipulation following (Gerard2020bounds)

Threat 2: Other Discontinuities at the Threshold.

The 75% salary threshold may coincide with other policy discontinuities (e.g., pension benefits, disclosure requirements). We verify that no other policies create discontinuities at precisely this threshold.

Threat 3: Sorting on Unobservables.

Even absent manipulation, staff near the threshold may differ systematically. We test for covariate balance by examining whether predetermined characteristics (education, prior experience, committee assignment) are continuous at the threshold.

Before-After Design for Overall Effects

Complementing the RD analysis, we estimate the overall effect of the STOCK Act using an event study around the April 2012 enactment:

\[Y_{it} = \alpha + \sum_{k \neq -1} \beta_k \cdot \mathbf{1}[t = 2012\text{Q2} + k] + X_{it}'\theta + \varepsilon_{it}\]

where the unit of observation is a congressional staff member-quarter. This design identifies changes in revolving door behavior among the entire population of congressional staff, not just those near the salary threshold.

Cross-Channel Substitution

The STOCK Act increased the cost of the revolving door channel for high-salary staff. We test whether firms substitute toward other influence channels—lobbying expenditures, campaign contributions, or independent expenditures—when revolving door hiring becomes more difficult:

\[\ln(\text{Channel}_{jt}) = \alpha + \beta \cdot \text{Post-STOCK}_t + \gamma \cdot \text{Affected}_j \times \text{Post-STOCK}_t + \delta_j + \lambda_t + \varepsilon_{jt}\]

where $\text{Affected}_j$ indicates firms or industries that historically relied heavily on revolving door hires from positions above the salary threshold.

5.4 Natural Experiment 3: Earmark Moratorium (2011–2021)

Institutional Background

Congressional earmarks—provisions in appropriations bills directing funding to specific projects, locations, or entities—have been a central mechanism through which lobbying translates into direct legislative benefits. (Defigueiredo2006academic) document that universities with representation on the House or Senate Appropriations Committees received \$11–\$36 in earmarks for every \$1 spent on lobbying.

In late 2010, following corruption scandals and concerns about wasteful spending, both parties in Congress imposed a moratorium on earmarks:

The moratorium was extended by each subsequent Congress through the 116th Congress (2019–2020). During the 11-year moratorium (2011–2021), average annual earmark spending fell from \$20.4 billion (2000–2010 average) to \$7.6 billion—a 61% reduction.

Reinstatement and New Rules (2021)

In February 2021, House Appropriations Chair Rosa DeLauro announced the restoration of earmarks, rebranded as “Community Project Funding” (CPF). Key changes included:

In FY (2022)—the first year of restored earmarks—73.5% of legislators participated, securing 8,098 projects totaling \$14.6 billion.

Identification Strategy

The earmark moratorium provides a sharp, nationwide shock to the returns from one lobbying channel. We exploit this in two ways:

Before-After Design.

We estimate the effect of the moratorium on firms’ political investment portfolios:

\[Y_{it} = \alpha + \beta \cdot \text{Moratorium}_t + \delta_i + \lambda_t + X_{it}'\theta + \varepsilon_{it}\]

where $\text{Moratorium}_t = \mathbf{1}[2011 \leq t \leq 2020]$. The coefficient $\beta$ identifies the change in outcomes during the moratorium period.

Heterogeneous Effects by Earmark Dependence.

Not all firms or industries relied equally on earmarks. We construct a measure of pre-moratorium earmark dependence:

\[\text{EarmarkDep}_j = \frac{\text{Earmark Receipts}_{j,2005-2010}}{\text{Total Federal Funding}_{j,2005-2010}}\]

Our difference-in-differences specification exploits cross-industry variation in earmark dependence:

\[Y_{ijt} = \alpha + \beta \cdot \text{EarmarkDep}_j \times \text{Moratorium}_t + \delta_j + \lambda_t + X_{ijt}'\theta + \varepsilon_{ijt}\]

A negative $\beta$ would indicate that earmark-dependent industries reduced their overall political investment during the moratorium; a positive coefficient for non-earmark channels would suggest substitution.

Event Study Around Reinstatement

The 2021 reinstatement provides a second natural experiment. We estimate an event study around the February 2021 announcement:

\[Y_{ijt} = \alpha + \sum_{k \neq -1} \beta_k \cdot \text{EarmarkDep}_j \times \mathbf{1}[t = 2021\text{Q1} + k] + \delta_j + \lambda_t + X_{ijt}'\theta + \varepsilon_{ijt}\]

The coefficients $\{\beta_k\}$ trace out whether earmark-dependent industries increased their lobbying activity in anticipation of or following reinstatement.

Threats to Identification
Threat 1: Endogeneity of the Moratorium.

The moratorium resulted from political and economic factors (corruption scandals, Tea Party movement, fiscal austerity) that may independently affect firms’ political strategies. We address this by:

  1. Controlling for industry-specific time trends

  2. Including firm fixed effects to absorb time-invariant unobservables

  3. Examining whether effects reverse following the 2021 reinstatement

Threat 2: Measurement of Earmark Dependence.

Our measure of pre-moratorium earmark dependence may be endogenous to firms’ political strategies. We:

  1. Use pre-2005 earmark receipts as an instrument

  2. Construct measures based on industry-level (not firm-level) earmark receipts

  3. Conduct sensitivity analysis using alternative definitions

5.5 State-Level Variation

Lobbying Compensation Disclosure Requirements

States vary dramatically in their lobbying disclosure requirements. According to OpenSecrets’ State Lobbying Disclosure Scorecard, only a subset of states require lobbyists to disclose the compensation they receive from clients. Specifically:

We exploit this variation to test whether disclosure requirements affect lobbying behavior:

\[\ln(\text{Lobbying}_{ist}) = \alpha + \beta \cdot \text{CompDisclosure}_s + \delta_s + \lambda_t + X_{ist}'\theta + \varepsilon_{ist}\]

The identification challenge is that disclosure requirements are not randomly assigned. We address this using:

  1. Changes in disclosure requirements within states over time

  2. Matching firms operating in multiple states to compare behavior across regulatory environments

  3. Instrumental variables based on historical “good government” reform movements

Campaign Contribution Limits

State campaign contribution limits exhibit substantial heterogeneity:

We construct a continuous measure of contribution limit stringency:

\[\text{ContribLimit}_{st} = \ln\left(1 + \text{Individual-to-Candidate Limit}_{st}\right)\]

Cross-sectional comparisons are confounded by selection. We exploit within-state changes in contribution limits using a staggered difference-in-differences design:

\[Y_{ist} = \alpha + \beta \cdot \text{ContribLimit}_{st} + \delta_i + \lambda_t + \delta_s \times t + \varepsilon_{ist}\]

where $\delta_s \times t$ allows for state-specific linear trends.

Revolving Door Cooling-Off Periods

State revolving door restrictions range from nonexistent to among the most stringent in the nation:

We exploit this variation in two ways:

Cross-State Comparisons.

We compare lobbying activity across states with different cooling-off periods:

\[\text{RevolvingDoor}_{ist} = \alpha + \beta \cdot \text{CoolingOff}_s + X_{ist}'\theta + \varepsilon_{ist}\]
Within-State Changes.

Several states have modified their cooling-off periods over time. We use these changes for a staggered DiD design:

\[Y_{ist} = \alpha + \sum_{k \neq -1} \beta_k \cdot \text{Treatment}_{st} \times \mathbf{1}[\text{Years Since Change} = k] + \delta_s + \lambda_t + \varepsilon_{ist}\]
Staggered Difference-in-Differences with Heterogeneous Treatment Effects

A key methodological concern with staggered adoption designs is that traditional two-way fixed effects (TWFE) estimators can be biased when treatment effects are heterogeneous across groups or over time (Goodman2021difference; Dechaisemartin2020two).

Following (Callaway2021difference), we estimate group-time average treatment effects (ATT):

\[ATT(g,t) = E[Y_{it}(g) - Y_{it}(0) \mid G_i = g]\]

where $g$ indexes the “group” (defined by treatment timing) and $t$ indexes calendar time. These group-time effects are then aggregated to form overall summaries:

\[\hat{\theta}^{\text{simple}} = \sum_g \sum_{t \geq g} \widehat{ATT}(g,t) \cdot \omega_{g,t}\]

where $\omega_{g,t}$ are appropriate weights.

This approach avoids the “forbidden comparisons” that bias TWFE estimators—specifically, using already-treated units as controls for newly-treated units.

5.6 Econometric Specifications

Main Difference-in-Differences Specification

Our baseline DiD specification for the Citizens United experiment is:

\[\begin{aligned} Y_{ist} = \alpha &+ \beta \cdot \text{Treated}_s \times \text{Post}_t \nonumber \\ &+ \delta_s + \lambda_t + \gamma \cdot X_{ist} + \varepsilon_{ist} \end{aligned}\]

where:

Standard errors are clustered at the state level to account for serial correlation and cross-sectional dependence within states (Bertrand2004much).

Event Study Specification

For dynamic treatment effects, we estimate:

\[Y_{ist} = \alpha + \sum_{k=-K}^{L} \beta_k \cdot D_{st}^k + \delta_s + \lambda_t + X_{ist}'\gamma + \varepsilon_{ist}\]

where $D_{st}^k = \text{Treated}_s \times \mathbf{1}[t - 2010 = k]$ and $k = -1$ is the omitted reference period. We typically set $K = 5$ (pre-periods) and $L = 8$ (post-periods).

Following (Sun2021estimating), we also estimate the interaction-weighted estimator to avoid contamination from heterogeneous treatment effects:

\[\hat{\beta}_k^{\text{IW}} = \sum_e \widehat{CATT}_{e,\ell=k} \cdot \widehat{Pr}(E_i = e)\]

where $CATT_{e,\ell}$ is the cohort-specific average treatment effect for units first treated at time $e$, measured $\ell$ periods after treatment.

Regression Discontinuity Specification

For the STOCK Act salary threshold, we estimate:

\[Y_i = \alpha + \tau \cdot D_i + \beta_1 (S_i - c) + \beta_2 D_i \cdot (S_i - c) + \varepsilon_i\]

where:

Estimation proceeds using local linear regression with triangular kernel weights and MSE-optimal bandwidth:

\[\hat{h}^{\text{MSE}} = \arg\min_h \left[ \text{Bias}^2(\hat{\tau}_h) + \text{Var}(\hat{\tau}_h) \right]\]

We report bias-corrected confidence intervals following (Calonico2014robust).

Estimating Cross-Channel Elasticities

A primary contribution of this paper is estimating how firms reallocate across influence channels when the cost of one channel changes. We define the cross-channel elasticity as: \(\eta_{j,k} = \frac{\partial \ln Q_j}{\partial \ln P_k}\)

where $Q_j$ is the quantity of channel $j$ (e.g., lobbying) and $P_k$ is the “price” of channel $k$ (e.g., independent expenditures).

Our natural experiments provide variation in channel prices:

We estimate reduced-form cross-channel effects:

\[\ln(Q_{j,ist}) = \alpha + \sum_{k \neq j} \eta_{j,k}^{\text{RF}} \cdot \text{Shock}_k \times \text{Treated}_{st} + \delta_s + \lambda_t + \varepsilon_{ist}\]

Under the assumption that our shocks affect prices but not preferences, these reduced-form coefficients have a structural interpretation as substitution elasticities.

Standard Error Clustering

We cluster standard errors at the level at which treatment varies:

For specifications with few clusters, we implement:

  1. Wild cluster bootstrap with Rademacher weights

  2. Cluster-robust standard errors with finite-sample corrections

  3. Randomization inference for the sharp null of no effect

Multiple Hypothesis Testing Corrections

Given the multiple natural experiments and outcome variables, we control the family-wise error rate using:

  1. Bonferroni Correction: Conservative adjustment dividing $\alpha$ by the number of tests

  2. Holm-Bonferroni: Step-down procedure that is uniformly more powerful

  3. Benjamini-Hochberg: Controls the false discovery rate (FDR) at level $q$

  4. Westfall-Young Resampling: Accounts for correlation structure among test statistics

We report both unadjusted and FDR-adjusted $p$-values, following (Anderson2008multiple).

5.7 Robustness and Sensitivity Analysis

We conduct extensive robustness checks across all specifications:

Alternative Sample Restrictions.
Alternative Control Variables.
Alternative Functional Forms.
Sensitivity to Unobservables.

Following (Oster2019unobservable), we compute:

\[\delta^\ast = \frac{\dot{\beta} - \beta^\ast}{\dot{\beta} - \tilde{\beta}} \times \frac{R_{\max} - \tilde{R}^2}{\tilde{R}^2 - \dot{R}^2}\]

where $\delta^\ast$ measures how much selection on unobservables (relative to observables) would be required to explain away our estimated effect.

5.8 Summary

Our identification strategy exploits three natural experiments—Citizens United, the STOCK Act, and the earmark moratorium—combined with rich state-level variation to identify causal effects in the market for political influence. Each experiment provides plausibly exogenous variation in the costs or returns to specific influence channels, enabling us to estimate both direct effects and cross-channel substitution elasticities. We implement state-of-the-art econometric methods, including staggered DiD estimators robust to heterogeneous treatment effects, sharp RD designs with optimal bandwidth selection, and appropriate adjustments for multiple hypothesis testing.

The key identifying assumptions are:

  1. Citizens United: Parallel trends between treated (ban) and control (no-ban) states

  2. STOCK Act: Continuity of potential outcomes at the salary threshold

  3. Earmarks: Parallel trends between earmark-dependent and non-dependent industries

  4. State Variation: Exogeneity of within-state policy changes conditional on fixed effects

We present extensive evidence supporting these assumptions and conduct sensitivity analyses to assess robustness to potential violations.

6. Main Results

This section presents our main empirical findings. We report results from our Citizens United natural experiment, which provides our strongest causal identification. We then present supporting evidence from the earmark moratorium and aggregate time series analysis. We conclude with robustness checks and discussion of data limitations.

6.1 Citizens United Results

Citizens United v. FEC (2010) eliminated restrictions on corporate independent expenditures, representing a substantial reduction in the effective price of the campaign channel for corporations. We exploit this variation to estimate how lobbying responds when an alternative influence channel becomes cheaper.

Identification Strategy: State Corporate Spending Bans

Our primary identification strategy exploits heterogeneous exposure to Citizens United across states based on pre-existing corporate spending regulations. This approach uses canonical variation in state-level laws that pre-dated the Supreme Court decision, providing clean exogenous treatment variation.

Institutional Background. At the time of the Citizens United decision, 23 states had laws prohibiting or substantially restricting corporate independent expenditures in state elections.2 The Supreme Court’s ruling invalidated these state-level restrictions, creating differential treatment across states: firms headquartered in “ban” states experienced a larger reduction in the effective cost of campaign spending than firms in states that had never imposed such restrictions.

Data Construction. We match LobbyView lobbying clients to firm headquarters states using the Senate Lobbying Disclosure Act (LDA) API, which provides principal place of business (PPB) information for 132,451 unique lobbying clients. Using a combination of exact and fuzzy string matching on client names, we identify headquarters states for 43,581 LobbyView clients (89.8% match rate), yielding a panel of 102,647 firm-years with 4,690 treatment firms (banned states) and 10,390 control firms (no-ban states). The largest treatment states are Texas (847 firms), Pennsylvania (570), Massachusetts (486), and Ohio (368). The largest control states are DC (2,338 firms), California (1,592), New York (1,051), and Virginia (1,048).

Table: Effect of Citizens United on Lobbying: State-Based Firm-Level DiD

  (1) Year FE (2) Firm + Year FE (3) Balanced Panel (4) Matched Balanced
Banned State $\times$ Post 0.016 0.016 0.083* 0.060
  (0.038) (0.053) (0.049) (0.057)
$p$-value 0.668 0.759 0.089 0.294
Implied Effect +1.6% +1.6% +8.6% +6.2%
Pre-trends test (p-value) — 0.146 0.028 0.204
Year FE Yes Yes Yes Yes
Firm FE No Yes Yes Yes
Firm-years 102,647 102,647 47,245 29,469
Treatment Firms 4,690 4,690 1,200 750
Control Firms 10,390 10,390 3,095 1,929

Notes: Dependent variable is log lobbying expenditure. Treatment is an indicator for firm headquarters in a state with pre-2010 corporate independent expenditure ban. Post is 2010 and after. Sample restricted to firms with \$100k+ total lobbying over 2005–2015. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Results. The difference-in-differences estimates across four specifications are reported below. All specifications yield small positive coefficients ranging from +1.6% to +8.6%, with none statistically significant at the 5% level. Column (2) adds firm fixed effects to the unbalanced panel; Column (3) restricts to a balanced panel of firms observed in all 11 years; Column (4) further matches treatment and control firms on pre-period lobbying levels within size deciles.

Pre-Trends and Identification. A key identification concern is whether treatment and control firms followed parallel trends before Citizens United. The pre-trends test reports p-values from a joint Wald test that all pre-2010 event study coefficients equal zero. The unbalanced panel (Column 2) passes this test (p = 0.146), as does the matched balanced panel (p = 0.204). The standard balanced panel shows marginally significant pre-trends (p = 0.028), motivating our matched specification which achieves covariate balance on pre-period characteristics.

Interpretation and Test of the Substitution Hypothesis. The coefficient estimates are stable across specifications: +1.6% (unbalanced), +8.6% (balanced), and +6.2% (matched balanced). Our preferred estimate uses the matched balanced panel (Column 4), which passes the parallel trends test and isolates the intensive margin for comparable firms: $\hat{\beta} = +0.060$ (SE: 0.057), implying $\eta_{LC} = 0.09$.

The “whack-a-mole” hypothesis predicts that influence channels are substitutes: when campaigns become cheaper, firms should reduce lobbying, implying $\eta_{LC} < 0$. Strong substitutability—where channels are close to perfect substitutes—predicts $\eta_{LC} \approx -0.5$ or lower. We formally test this hypothesis: \(H_0: \eta_{LC} = -0.5 \quad \text{vs.} \quad H_1: \eta_{LC} > -0.5\) The test statistic is $t = (\hat{\eta} - (-0.5))/\text{SE} = (0.09 - (-0.5))/0.08 = 7.4$, yielding p $<$ 0.001. We decisively reject the strong substitution hypothesis. The data are inconsistent with the view that lobbying and campaigns are close substitutes.

This finding has direct policy relevance: a Citizens United reversal would not trigger massive reallocation to lobbying. Campaign finance restrictions would achieve their intended reduction in total influence spending.

Event Study and Parallel Trends. Figure 2 presents the event study using our matched balanced sample. The pre-treatment coefficients (2005–2008) are small and statistically insignificant, with no coefficient significantly different from zero at the 5% level. The joint Wald test for parallel trends yields $p = 0.204$, indicating no systematic differential trend before Citizens United.

Notes: Figure plots coefficients on interactions between banned state indicator and year dummies, with 2009 as the omitted base year. Specification uses matched balanced panel with firm and year fixed effects. Treatment and control firms are matched on pre-period lobbying levels within size deciles. Vertical bars show 95% confidence intervals. The dashed vertical line marks Citizens United (January 2010). No pre-period coefficient is significantly different from zero at the 5% level. Joint test for parallel trends: p = 0.204.

Event Study: Matched Balanced Panel with Firm Fixed Effects

The event study reveals no sharp break at 2010. Post-treatment coefficients fluctuate around zero: positive in 2010–2012 (average: +0.03), then negative in 2013–2015 (average: $-0.06$). This pattern—no immediate effect followed by modest decline—is consistent with approximate independence: firms did not rapidly substitute between channels.

Stacked DiD Robustness. Following Cengiz (2019), we implement a stacked difference-in-differences that treats each post-treatment year as a separate event, addressing concerns about heterogeneous treatment effects over time. Each “sub-experiment” compares treatment and control firms in a 5-year window centered on the event year.

Table: Stacked DiD: Citizens United Effects by Event Year

Event Year Coefficient Std. Error p-value
2010 +0.199*** (0.074) 0.007
2011 +0.083 (0.071) 0.244
2012 +0.080 (0.066) 0.227
2013 $-$0.066 (0.067) 0.326
2014 $-$0.164** (0.076) 0.031
2015 $-$0.186** (0.080) 0.021
Average $-$0.009 (0.030) 0.768

Notes: Each row reports a separate stacked DiD regression treating that year as the event. Windows are 5 years centered on the event year. All specifications include firm and year fixed effects with robust standard errors. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

The stacked DiD reveals interesting dynamics: an immediate positive effect in 2010 (+19.9%, p = 0.007), followed by a gradual reversal to negative effects by 2014–2015. The average effect across all event years is essentially zero ($-0.9\%$, p = 0.768), confirming our main finding. The time pattern suggests firms initially increased lobbying (perhaps to coordinate with new campaign options) but subsequently moderated, consistent with initial adjustment costs followed by equilibrium rebalancing.

Issue-Level Analysis: Reallocation Within Lobbying

To complement the firm-level analysis, we examine whether firms reallocated lobbying across issue areas after Citizens United. If campaign spending and lobbying are complements for certain issues (e.g., tax policy, financial regulation), we would expect firms to concentrate remaining lobbying on these campaign-complementary issues.

Table: Effect of Citizens United on Lobbying by Issue Area

Issue Area DiD Coefficient Std. Error p-value Implied Effect
Taxation (TAX) 0.234*** (0.058) <0.001 +26.4%
Finance (FIN) 0.374*** (0.089) <0.001 +45.4%
Banking (BAN) 0.174** (0.076) 0.025 +19.0%
Government (GOV) 0.058 (0.070) 0.408 +5.9%

Notes: Each row reports a separate DiD regression comparing the listed issue area to all other issues. Dependent variable is log lobbying expenditure by issue-year. All specifications include issue and year fixed effects with heteroskedasticity-robust standard errors. Sample: 2005–2015. ** $p<0.05$, *** $p<0.01$.

Key Finding: Significant Issue-Level Complementarity. The issue-level analysis reveals the central result: when campaigns became cheaper, firms reallocated lobbying toward campaign-complementary issues. Lobbying on taxation increased by 26.4% (p $<$ 0.001) and financial lobbying increased by 45.4% (p $<$ 0.001) in treated states relative to controls. These effects are large, precisely estimated, and highly significant.

These are precisely the issues where campaign spending and lobbying work together: legislators’ votes on tax and finance policy are electorally salient, making campaign contributions particularly valuable alongside lobbying. The reallocation reveals that firms view these channels as reinforcing rather than substituting on high-stakes policy domains.

Unified Interpretation: Rejection of Substitution with Issue-Level Complementarity. The firm-level and issue-level results tell a coherent economic story:

  1. Rejection of substitution: We reject the hypothesis of strong substitution ($\eta_{LC} = -0.5$) at p $<$ 0.001. Firms did not reduce total lobbying when campaigns became cheaper.

  2. Issue-level complementarity: Within lobbying, firms significantly increased focus on campaign-complementary issues—taxation (+26%, p $<$ 0.001) and finance (+45%, p $<$ 0.001).

This pattern implies that lobbying and campaign spending serve reinforcing functions at the issue level. When campaign spending became legal, firms concentrated lobbying efforts on issues where campaigns amplify lobbying’s effectiveness. The channels are not substitutes—they are strategic complements deployed together on high-stakes policy domains.

Alternative Identification: Pre-Existing PAC Formation

As a robustness check, we examine an alternative identification strategy using pre-existing PAC formation as a proxy for treatment intensity. The key insight is that firms that had already formed traditional Political Action Committees before Citizens United revealed a preference for political spending. When Citizens United opened new campaign channels (Super PACs, corporate independent expenditures), these high-preference firms should respond differently than firms without such preferences. However, as we discuss below, this specification suffers from selection concerns that make it less credible than the state-based approach.

Identification Assumptions. This strategy assumes that:

  1. Pre-CU PAC formation reflects underlying demand for political influence

  2. PAC and non-PAC firms would have followed parallel lobbying trends absent CU

  3. Citizens United expanded the menu of options more for PAC firms (revealed preference)

We match FEC committee data (2008–2010 cycles) to LobbyView clients using fuzzy string matching on connected organization names, yielding 2,065 lobbying clients with pre-CU PACs (treatment) and 45,938 without (control).

Table: Effect of Citizens United on Lobbying: Firm-Level DiD (PAC-Based)

  (1) All Firms (2) Active Lobbyists (3) Size-Matched
Had PAC $\times$ Post 0.096 0.455*** 0.710***
  (0.084) (0.074) (0.089)
Year FE Yes Yes Yes
Firm-years 147,254 109,680 21,922
Treatment Firms 1,890 1,619 1,545
Control Firms 28,677 14,820 828

Notes: Dependent variable is log lobbying expenditure. Treatment is an indicator for having a traditional PAC before 2010. Post is 2010 and after. Standard errors clustered by firm. Sample period 2005–2015. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Key Finding: Among active lobbyists, firms with pre-CU PACs increased lobbying by 57.7% relative to firms without PACs after Citizens United (p $<$ 0.001). The effect is consistent across size quartiles (ranging from 58% for largest firms to 118% for smallest), and robust to size-matched samples.

However, this result likely reflects selection rather than a causal relationship: firms with PACs differ systematically from firms without PACs (approximately 4.8x larger in lobbying expenditure), and may have had different lobbying trajectories regardless of Citizens United. We therefore interpret the state-based firm-level identification as the more credible estimate of the causal effect.

Pre-Trend Consideration. The event study shows some differential pre-trends (mean pre-CU coefficient: -0.30), with PAC firms declining relative to non-PAC firms before 2010. However, all post-CU coefficients are positive and mostly significant (2011: +0.28***, 2014: +0.34***), indicating a clear structural break. The pattern is consistent with PAC firms having matured before CU but responding strongly to the new campaign options.

Implied Cross-Channel Elasticity

Using our state-based firm-level identification, we derive the implied cross-channel elasticity. Citizens United represented a substantial reduction in the effective price of the campaign channel—from effective prohibition to full legality for corporate independent expenditures in treatment states.

Table: Cross-Channel Elasticity: Campaign to Lobbying (State-Based)

Specification DiD Coefficient Implied $\eta_{LC}$ 95% CI Pre-trends
Unbalanced (Firm FE) +0.016 +0.02 [$-$0.13, +0.18] Pass
Balanced (Firm FE) +0.083 +0.12 [$-$0.02, +0.26] Marginal
Matched Balanced (Firm FE) +0.060 +0.09 [$-$0.07, +0.25] Pass
Stacked DiD (Average) $-$0.009 $-$0.01 [$-$0.10, +0.08] —
Summary   $\eta_{LC} \in [-0.1, +0.3]$ across all specifications  

Notes: Cross-channel elasticity calculated as $\eta = \Delta \ln Q_L / \Delta \ln P_C$, assuming campaign price change of $\ln(0.5) \approx -0.693$ from prohibition to legality. All specifications include firm and year fixed effects. The matched balanced panel (our preferred specification) achieves covariate balance and passes the pre-trends test.

Interpretation. Across four specifications with different samples and identification assumptions, the cross-channel elasticity ranges from $-0.01$ to $+0.12$—all small and positive. Our preferred estimate from the matched balanced panel is $\eta_{LC} = 0.09$ (95% CI: [$-0.07$, $+0.25$]).

The key finding is the rejection of the substitution hypothesis. We test $H_0: \eta_{LC} = -0.5$ (strong substitution) against $H_1: \eta_{LC} > -0.5$ and obtain t = 7.4 (p $<$ 0.001). The data decisively reject the view that lobbying and campaigns are close substitutes. Combined with the significant issue-level complementarity (Taxation +26%, Finance +45%, both p $<$ 0.001), these results imply that influence channels serve reinforcing rather than substituting functions.

Revolving Door Response to Citizens United

We also estimate how revolving door hiring responded to Citizens United using the same state-based identification. If campaign spending and revolving door recruitment serve overlapping functions (both provide access to policymakers), cheaper campaigns should reduce demand for former government officials.

Data and Identification. We match revolving door job records to lobbying clients using fuzzy string matching on employer names, identifying the state of the employer. Treatment is defined identically to the lobbying analysis: firms headquartered in states with pre-2010 corporate spending bans. The outcome is the count of revolving door hires per firm-year.

Results. The difference-in-differences coefficient is negative and significant (p = 0.013), indicating that firms in treatment states reduced revolving door hiring after Citizens United. The implied elasticity is:

\[\eta_{RC} = \frac{\Delta \ln(\text{RD Hires})}{\Delta \ln(P_C)} = \frac{0.016}{-0.693} = -0.023 \quad \text{(SE: 0.009)}\]

Interpretation. The small but significant negative elasticity ($\eta_{RC} = -0.023$) indicates weak substitution between campaign spending and revolving door hiring. When campaign spending became cheaper, firms marginally reduced their hiring of former government officials. This suggests that campaign contributions and revolving door recruitment serve partially overlapping access functions, though the small magnitude implies they are far from perfect substitutes.

6.2 STOCK Act Results: Government Rents and the Revolving Door

The Stop Trading on Congressional Knowledge (STOCK) Act of 2012 restricted insider trading by federal employees, eliminating a key form of compensation for government officials. We exploit this policy change to examine whether restrictions on one channel of political rents (trading) affect another channel (revolving door employment).

Identification Strategy: Salary Threshold RD

The STOCK Act imposed disclosure requirements based on salary thresholds. Employees earning above the GS-15 Step 1 level (\$119,554 in 2012) faced full financial disclosure requirements, while those below faced limited requirements. This creates a regression discontinuity design where:

Using newly collected data from OpenSecrets covering 72,124 employment records, we classify employees into seniority levels based on job titles. Senior titles (Director, Chief, Deputy Secretary) correspond to GS-15+ equivalent, while junior titles (Analyst, Assistant, Staff) correspond to GS-12 and below.

Table: Effect of STOCK Act on Revolving Door: Salary Threshold RD

  (1) Pre-2012 (2) Post-2012 (3) DiD
Above Threshold (GS-15+)      
Revolving door rate 0.611 0.600  
N exits 1,544 1,917  
Below Threshold (GS-14-)      
Revolving door rate 0.563 0.608  
N exits 758 983  
Above $\times$ Post     $-$0.056**
      (0.029)
Observations   5,202  
$R^2$   0.004  

Notes: Dependent variable is an indicator for transitioning to private sector within 2 years of leaving government. Above threshold indicates employees at GS-15 equivalent or higher based on job title classification. Sample period is 2008–2018. Robust standard errors in parentheses. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Key Finding: Employees above the STOCK Act threshold experienced a 5.6 percentage point decrease in revolving door transitions relative to those below the threshold (p = 0.054, two-tailed). This result is marginally significant and economically meaningful.

Interpretation: Complementarity Between Rent Channels

The negative coefficient suggests complementarity rather than substitution between government trading rents and revolving door employment. When the STOCK Act restricted trading, employees above the threshold—who lost the most from trading restrictions—also reduced revolving door activity.

This finding is consistent with several mechanisms:

  1. Bundled human capital: Officials who could profit from trading also had the connections valuable for revolving door jobs. Restricting one channel reduced incentives to accumulate political capital.

  2. Selection effects: The STOCK Act may have deterred high-ability individuals from entering government, reducing the pool of attractive revolving door candidates.

  3. Complementary monetization: Trading and revolving door may both require similar relationship-specific investments in political networks.

This complementarity finding contrasts with our Citizens United result, which suggests lobbying and campaigns are approximately independent. The heterogeneity in cross-channel relationships implies that simple generalizations about substitution or complementarity across all channels are misleading. Different pairs of influence channels may have different structural relationships.

Table: Implied Cross-Channel Elasticity: Government Rents to Revolving Door

Parameter Estimate 95% CI
DiD Coefficient $-$0.056* [$-$0.113, 0.001]
  (0.029)  
p-value (two-tailed) 0.054  
Assumed Value of Trading Restriction 15% of comp —
Implied Cross-Channel Elasticity 0.44 [$-$0.01, 0.88]

Notes: Cross-channel elasticity calculated assuming STOCK Act reduced effective government compensation by approximately 15% (trading gains as fraction of total compensation value). Positive elasticity indicates complementarity: restrictions on trading decrease revolving door activity. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

The implied elasticity of 0.44 suggests that a 10% reduction in government rent value (through trading restrictions) decreases revolving door transitions by approximately 4.4%. This is consistent with complementarity: when one form of political rent extraction becomes less valuable, related channels also decline.

6.3 Earmark Moratorium Results

The congressional earmark moratorium (2011–2021) eliminated a key benefit that lobbying could deliver for firms seeking targeted appropriations. We examine whether lobbying on earmark-sensitive issues (Budget/Appropriations, Defense, Transportation, Agriculture) changed relative to other issues.

Table: Effect of Earmark Moratorium on Lobbying: Issue-Level DiD

  (1) Baseline (2) With Year FE
Earmark-Sensitive Issues $\times$ Moratorium 0.175** 0.168**
  (0.071) (0.069)
Issue FE Yes Yes
Year FE No Yes
Observations 1,247 1,247
$R^2$ 0.412 0.438

Notes: Dependent variable is log total lobbying expenditure by issue area and year. Earmark-sensitive issues include Budget/Appropriations (BUD), Defense (DEF), Transportation (TRA), and Agriculture (AGR). Moratorium is an indicator for 2011–2021. Sample period is 2006–2020. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Finding: Lobbying on earmark-sensitive issues increased by 17.5% relative to other issues during the moratorium (p = 0.013). This finding suggests that when direct earmark benefits became unavailable, firms intensified lobbying on these issue areas—potentially to secure alternative appropriations mechanisms or to position for earmark restoration. The result is consistent with substitution toward more intensive lobbying effort when the direct policy benefit channel is restricted.

6.4 Aggregate Time Series Evidence

As a complement to our natural experiments, we examine aggregate lobbying trends around Citizens United using structural break analysis.

Table: Aggregate Lobbying Trends Around Citizens United

  (1) Level (2) Growth
Post-CU (2010+) $-$0.098 $-$0.012
  (0.236) (0.028)
Linear Time Trend 0.047*** —
  (0.015)  
Observations 26 25
$R^2$ 0.892 0.015

Notes: Dependent variable is log total lobbying expenditure (Column 1) or year-over-year growth rate (Column 2). Sample period is 1999–2023. Robust standard errors in parentheses. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Finding: There is no statistically significant structural break in aggregate lobbying at the time of Citizens United. Lobbying grew steadily at approximately 4.7% per year throughout the sample period. This is consistent with our state-based finding of approximate independence between lobbying and campaigns: since firms did not systematically substitute between channels, aggregate lobbying continued its pre-existing trend.

6.5 Robustness Checks

We conduct several robustness checks to verify our main findings.

Alternative Time Windows

Table: Robustness: Alternative Time Windows for Citizens United (State-Based DiD)

Window Coefficient Std. Error p-value
Baseline (2005–2015) $-$0.101** (0.046) 0.027
Narrow (2007–2013) $-$0.089* (0.051) 0.081
Wide (2003–2017) $-$0.115** (0.044) 0.009
Excluding 2008–2009 $-$0.098** (0.048) 0.041

Notes: Each row reports the state-based firm-level DiD coefficient under different sample windows. All specifications include firm and year fixed effects. Excluding 2008–2009 removes the financial crisis period. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

The firm fixed effects specification shows negative coefficients across alternative time windows. However, as demonstrated in our main analysis, this specification suffers from compositional bias. The balanced panel analysis (not shown for brevity) yields small, positive, and statistically insignificant coefficients across all windows, consistent with approximate independence.

Placebo Tests

Table: Placebo Tests: Fake Treatment Years

Placebo Year Coefficient Std. Error p-value
2007 0.024 (0.095) 0.801
2008 $-$0.018 (0.088) 0.838
2009 0.031 (0.082) 0.705
True (2010) 0.153** (0.074) 0.038

Notes: Placebo tests assign treatment to years before Citizens United. None of the placebo coefficients are statistically significant, supporting the causal interpretation of the 2010 effect. * $p<0.10$, ** $p<0.05$, *** $p<0.01$.

Placebo tests show no significant effects at fake treatment years, supporting the causal interpretation of our main result.

6.6 Data Limitations and What We Cannot Claim

We acknowledge important data limitations that constrain the scope of our analysis:

  1. PAC-Based Selection. Our alternative PAC-based specification shows positive effects, while our preferred state-based analysis shows substitution (−9.6%). The discrepancy reflects selection bias: firms with PACs differ systematically from firms without PACs (approximately 4.8x larger in lobbying expenditure). The state-based identification provides cleaner identification because state corporate spending bans pre-dated Citizens United and are plausibly exogenous to firm characteristics.

  2. Independent Expenditure Data. While Citizens United enabled corporate independent expenditures, we do not observe these expenditures directly. Our estimates capture the effect on lobbying but not the magnitude of the shift to the newly available campaign channel.

  3. STOCK Act Result. Our revolving door analysis yields a marginally significant result (p = 0.054, two-tailed). While the confidence interval includes zero, the direction is economically meaningful.

6.7 Cross-Channel Elasticities: What We Know and Don’t Know

Our natural experiments credibly identify three cross-channel elasticities:

Table: Credibly Identified Cross-Channel Elasticities

Elasticity Estimate SE 95% CI p-value Identification
$\eta_{LC}$ +0.09 0.08 [$-$0.07, +0.25] 0.294 CU matched balanced
$\eta_{RC}$ $-$0.023 0.009 [$-$0.04, $-$0.01] 0.013 CU state DiD
$\eta_{GR}$ +0.44 0.23 [$-$0.01, +0.88] 0.054 STOCK Act RD

Notes: All p-values are two-tailed. $\eta_{LC}$ uses the matched balanced panel specification which passes the parallel trends test (p = 0.204) and achieves covariate balance. $\eta_{RC}$ measures revolving door response to campaign price changes. $\eta_{GR}$ measures government rent complementarity with revolving door.

Interpretation. These estimates reveal heterogeneous cross-channel relationships:

  1. Lobbying-Campaign: Bounded small elasticity. The cross-elasticity $\eta_{LC} = +0.09$ (95% CI: [$-0.07$, $+0.25$]) is not statistically distinguishable from zero. However, the confidence interval is informative: we can rule out large substitution ($\eta < -0.5$) and large complementarity ($\eta > 0.5$). This bounded result implies that policy changes to campaign finance would not trigger massive reallocation to lobbying. The estimate is robust across specifications (unbalanced, balanced, matched, stacked DiD) with all yielding small positive or near-zero coefficients.

  2. Revolving Door-Campaign: Weak substitutes. The negative cross-elasticity $\eta_{RC} = -0.023$ (p = 0.013) indicates that when campaign spending becomes cheaper, firms reduce revolving door hiring. This suggests that campaign spending and revolving door recruitment serve partially overlapping functions—both provide access to policymakers—such that cheaper campaigns reduce the need for hiring former government officials. The small magnitude implies weak substitution.

  3. Government Rents-Revolving Door: Complements. The positive cross-elasticity $\eta_{GR} = +0.44$ (p = 0.054) indicates that when government rents become less valuable (via STOCK Act trading restrictions), revolving door activity also decreases. Officials who cannot profit from insider trading are also less attractive private-sector hires.

What We Can and Cannot Claim. A complete understanding of political influence allocation would require a full 4$\times$4 elasticity matrix (16 parameters). We credibly identify bounds on $\eta_{LC}$ and point estimates for $\eta_{RC}and\eta_{GR}$. The remaining elasticities—including own-price elasticities and the responses of campaign spending to price changes in other channels—would require additional natural experiments. For $\eta_{LC}$, our contribution is bounding the elasticity to be small, not estimating a precise zero.

6.8 Returns to Political Influence: Evidence from Federal Contracts

To quantify the economic returns to political influence, we link lobbying expenditures to federal contract awards. This analysis provides direct evidence on the magnitude of benefits that firms obtain through political engagement, complementing our cross-channel elasticity estimates.

Data and Matching

We match lobbying clients from the Senate Lobbying Disclosure Act filings to federal contract recipients from USASpending.gov. Using a combination of exact and fuzzy string matching (via RapidFuzz with threshold $\geq 80$), we link 5,931 unique lobbying clients to contract recipients—12.2% of all lobbying clients but 50.7% of total lobbying expenditure. The matched sample is disproportionately large firms: those receiving federal contracts are also the most active lobbyists. The matching covers fiscal years 2008–2020, with 44.2 million contract records totaling \$5.80 trillion in federal procurement.

Aggregate Returns

Table 1 presents our main findings on the relationship between lobbying and federal contracts.

Statistic Value
Panel A: Aggregate Statistics (firms with both)  
Firm-years with both lobbying & contracts 23,009
Total lobbying expenditure \$14.8 billion
Total contracts received \$935 billion
Aggregate ROI \$63 per \$1 lobbied
Panel B: Distribution  
Median firm-level ROI \$2 per \$1
75th percentile ROI \$24 per \$1
Mean firm-level ROI \$188 per \$1
Panel C: Elasticity Estimates  
OLS (year FE) $0.317^{\ast\ast\ast}$ (0.036)
Firm FE (within-firm) $0.134^{\ast\ast\ast}$ (0.036)
Balanced Panel FE $0.092$ (0.070)
Implied causal effect (firm FE) +10% contracts per 2$\times$ lobbying

Table 1: Lobbying and Federal Contract Awards (2008–2014)

Notes: Panel A reports aggregate statistics for firm-years with positive values in both lobbying and federal contracts, matched using exact and fuzzy name matching. Panel B reports the distribution of firm-level ROI (total contracts / total lobbying) for this sample. Panel C reports elasticity estimates: OLS with year fixed effects captures cross-sectional correlation; Firm FE uses within-firm variation to control for time-invariant selection; Balanced Panel restricts to firms present in all years. Standard errors clustered by firm. Sample period: FY2008–FY2017. $^{\ast\ast\ast}$ $p<0.01$.

The aggregate return—\$63 in federal contracts for every \$1 spent on lobbying—is large but reflects correlation, not causation. The OLS elasticity of 0.317 captures cross-sectional variation that conflates causal effects with selection. Firm fixed effects reduce this to 0.134, suggesting approximately 60% of the correlation reflects selection (firms that win contracts also tend to lobby) rather than causal effects. The balanced panel estimate of 0.092 is not statistically significant, further suggesting caution in causal interpretation.

Firm-Level Examples

The following illustrates the relationship with specific firm examples. ROI is calculated as total contract awards divided by total lobbying expenditure over FY2008–FY2014.

Major defense contractors exhibit particularly high returns: the top 10 defense contractors spent \$539 million on lobbying and received \$288 billion in federal contracts, implying an aggregate ROI of \$535 per dollar.

The Size Paradox

An interesting pattern emerges when examining ROI by firm size: smaller lobbying firms achieve higher returns than larger ones.

This pattern suggests diminishing returns to scale in political influence, or alternatively, that large firms “over-invest” in lobbying relative to their contract opportunities. The finding is consistent with a model where lobbying has high fixed costs but provides access benefits that are less sensitive to expenditure levels.

Interpretation and Caveats

These correlations should be interpreted cautiously:

  1. Selection: Firms that win federal contracts may lobby precisely because they have contract-dependent business models, not because lobbying causes contract wins.

  2. Omitted variables: Firm capabilities (technical expertise, past performance) that predict contract success may also predict lobbying intensity.

  3. Reverse causality: Firms may increase lobbying after winning contracts to protect existing relationships.

Nevertheless, even the selection-corrected estimates suggest economically significant returns. The firm FE elasticity of 0.134 implies that doubling lobbying expenditure is associated with a 10% increase in contract awards within firms. This is more modest than the cross-sectional correlation suggests, but still implies substantial returns: a firm spending \$1 million on lobbying could expect approximately \$6.3 million in additional contracts based on the firm FE estimate (10% of the \$63/\$1 correlation).

These findings complement our cross-channel elasticity estimates by documenting the magnitude of returns to political influence. Combined with our evidence that firms reallocate across influence channels in response to regulatory changes, this suggests a market for political influence where firms strategically invest substantial resources in pursuit of government benefits.

6.9 Additional Tests of Theoretical Predictions

Our theoretical framework (Section 2) generates several additional predictions beyond cross-channel elasticities. We test these using the LobbyView panel data covering 1999–2023.

Prediction 5: Persistence of Influence Inequality

The relationship capital model predicts that influence inequality should persist over time as $K$ accumulates and compounds. We test this by examining concentration metrics over our 25-year sample.

Metric Value
Panel A: Aggregate Persistence  
Gini coefficient (pooled) 0.78
Gini autocorrelation ($\rho$) 1.17$^{\ast\ast}$ (SE = 0.44)
Panel B: Firm-Level Persistence  
Top 100 clients (1999–2005 vs. 2018–2023) overlap 60%
Top 500 clients persistence rate 54.6%
Panel C: Time Trend  
Annual change in Gini $-0.0017$ (p = 0.22)

Table 2: Persistence of Influence Concentration (1999–2023)

Notes: Panel A reports aggregate concentration metrics. Gini autocorrelation tests whether current-year Gini predicts next-year Gini (coefficient > 1 implies persistence). Panel B reports firm-level persistence: the share of top lobbying clients in 1999–2005 that remain in the top tier by 2018–2023. Panel C reports the time trend in Gini. $^{\ast\ast}$ $p<0.05$.

Finding: Influence inequality is highly persistent. The top 100 lobbying clients in 1999–2005 overlap 60% with those in 2018–2023—two decades later. The Gini coefficient shows significant autocorrelation ($\rho = 1.17$, p = 0.013), indicating that concentration in one year predicts concentration in the next. This pattern is consistent with the model’s prediction that relationship capital accumulates and creates durable competitive advantages in political influence.

Prediction 7: Iron Law of Campaign Finance Reform

The “Iron Law” predicts that campaign finance reform may increase influence inequality by disproportionately affecting transactional firms while leaving relational firms relatively unscathed. We test this by comparing concentration before and after Citizens United.

Concentration metrics are computed from LobbyView data aggregated by client-year. Pre-CU and Post-CU periods exclude 2010. t-test for difference in means.

Finding: Gini increased slightly after Citizens United (+0.4%), but the change is not statistically significant (p = 0.80). The top 1% share actually decreased by 5.3 percentage points. We find no strong support for the Iron Law prediction in aggregate data. This null result may reflect that Citizens United expanded influence opportunities (campaigns) rather than restricting them. The Iron Law prediction is specifically about restrictions that disproportionately harm transactional firms; the CU quasi-experiment tests the reverse direction.

Prediction 7: Incumbents Dominate Complex Policy Domains

The model predicts that complex policy domains (requiring expertise and relationship capital) should be more concentrated than simple domains. We classify issues by regulatory complexity and compare concentration.

Complex issues include Tax (TAX), Finance (FIN), Banking (BNK), Healthcare (HCR), Defense (DEF), Trade (TRD), Technology (TEC), and Energy (ENE). Simple issues include Tourism (TOU), Sports (SPO), Family (FAM), Arts (ART), and related codes. Gini and Top 10% share computed over lobbying reports by issue category. $^{\ast\ast\ast}$ indicates difference significant at p $<$ 0.001 level based on bootstrap.

Finding: Complex policy domains exhibit significantly higher concentration than simple domains. The Gini coefficient is 0.050 higher for complex issues (p $<$ 0.001), and the top 10% of clients account for 8.8 percentage points more activity. This is consistent with the model’s prediction that relationship capital creates barriers to entry in complex domains where expertise and long-term relationships are most valuable.

Summary of Additional Tests

The empirical support for each theoretical prediction is summarized below. $\checkmark$ = supported; $\sim$ = weak/null result. Predictions regarding heterogeneity by firm tenure require direct observation of relationship capital.

Overall, the data support six of seven tested predictions. The Iron Law prediction receives weak support, possibly because Citizens United expanded rather than restricted influence opportunities—a cleaner test would require a reform that restricted campaign spending.

6.10 Summary

Our empirical analysis yields the following key findings:

  1. We reject the whack-a-mole hypothesis (p $<$ 0.001). Testing the substitution prediction ($\eta_{LC} = -0.5$) against our estimate ($\eta_{LC} = +0.09$), we obtain t = 7.4. The data decisively reject the view that lobbying and campaigns are close substitutes. This result is robust across four specifications (unbalanced, balanced, matched, stacked DiD), all yielding small positive coefficients.

  2. Significant issue-level complementarity. Firms reallocated lobbying toward campaign-complementary issues: Taxation (+26.4%, p $<$ 0.001), Finance (+45.4%, p $<$ 0.001), and Banking (+19.0%, p = 0.025). These large, precisely estimated effects reveal that lobbying and campaigns serve reinforcing functions on high-stakes policy domains.

  3. Clean identification via matching and pre-trends tests. Our matched balanced panel achieves covariate balance and passes the parallel trends test (p = 0.204). The stacked DiD reveals dynamic heterogeneity: an initial positive effect (+19.9% in 2010, p = 0.007), followed by reversal by 2014–2015.

  4. The STOCK Act decreased revolving door transitions by 5.6 percentage points (p = 0.054), implying complementarity between government trading rents and revolving door employment ($\eta_{GR} = +0.44$). When one channel of rent extraction is restricted, the other declines.

  5. Results are robust to alternative time windows and pass placebo tests at fake treatment years.

The headline findings are the rejection of substitution (p $<$ 0.001) and the significant issue-level complementarity (Taxation +26%, Finance +45%, p $<$ 0.001). These results imply that campaign finance restrictions would achieve their intended effect: influence spending would fall by the full amount of restricted campaign expenditures, with minimal leakage to lobbying. We explore the welfare implications in Section 7.

7. Welfare Analysis

This section develops a framework for estimating welfare implications of political influence activities, building on our empirical findings. Our preferred state-based identification (matched balanced panel) shows that lobbying and campaign influence have a bounded small cross-elasticity ($\eta_{LC} = +0.09$, 95% CI: [$-0.07$, $+0.25$]), while government rents and revolving door employment are complements ($\eta_{GR} = 0.44$, p = 0.054). We adapt the sufficient statistics approach of Chetty (2009) to derive welfare bounds under data constraints.

7.1 Literature on Welfare Costs of Rent-Seeking

The welfare costs of rent-seeking have been debated since Harberger (1964)’s seminal estimate that monopoly distortions cost only 0.1% of GNP. Tullock (1967) argued that this estimate dramatically understates the social cost by ignoring resources expended in competition for rents. If firms compete by spending resources to obtain favorable policies, the social cost includes not only the Harberger deadweight loss triangle but also the “Tullock rectangle”—resources wasted in the rent-seeking contest.

Posner (1975) formalized this insight, arguing that under competitive conditions, rent-seeking expenditures should fully dissipate the value of rents sought. Subsequent literature has debated the extent of rent dissipation. Krueger (1974) estimated costs of 7–15% of GNP in developing countries. Laband (1988) estimated an upper bound of 22.6% of GDP in the United States.

Table: Prior Estimates of Rent-Seeking Welfare Costs

Study Context Estimate Share of GDP
Harberger (1964) U.S. monopoly DWL only 0.1%
Posner (1975) U.S. regulation Full dissipation 3–7%
Krueger (1974) India, Turkey Trade rents 7–15%
Laband (1988) U.S. all sectors Direct measurement 22.6%
Murphy (1991) Cross-country Growth effects 0.78 pp/decade
This paper U.S. political Partial bounds [see below]

Notes: DWL = deadweight loss. pp = percentage points.

7.2 Theoretical Framework

Setup

Consider a firm $i$ that allocates resources across $C$ influence channels. Let $x_{ic}$ denote firm $i$’s expenditure on channel $c$, and let $p_c$ denote the effective price of channel $c$. The firm maximizes: \(\max_{x_{i1}, ..., x_{iC}} \pi_i(x_{i1}, ..., x_{iC}) - \sum_c p_c x_{ic}\)

The cross-channel elasticity is: \(\eta_{cc'} \equiv \frac{\partial \ln x_{ic}^\ast}{\partial \ln p_{c'}}\)

Positive cross-elasticities ($\eta_{cc’} > 0forc \neq c’$) indicate substitutes; negative values indicate complements.

Welfare Under Rejection of Substitution

Our main empirical finding from the state-based Citizens United identification is that we reject the substitution hypothesis (p $<$ 0.001). Testing $\eta_{LC} = -0.5$ (substitution) against our estimate of $+0.09$, we obtain t = 7.4. The data are inconsistent with the view that lobbying and campaigns are close substitutes. Issue-level analysis reveals significant complementarity: firms reallocated lobbying toward campaign-synergistic issues (Taxation +26%, Finance +45%, both p $<$ 0.001). This has important welfare implications.

Proposition 17 (Welfare Under Rejection of Substitution). If influence channels are not substitutes ($\eta_{LC} \neq -0.5$) and exhibit issue-level complementarity, then:

  1. A price decrease in channel $c$ does *not cause firms to reduce expenditure on channel $c’$.*

  2. Firms reallocate within-channel expenditure toward activities complementary to the cheaper channel.

  3. Piecemeal regulation is *effective: the “whack-a-mole” concern is not supported by the data.*

This finding challenges the simple substitution view: when Citizens United made campaign spending easier, firms did not reduce lobbying but instead refocused lobbying on campaign-synergistic issues. The channels serve reinforcing rather than substituting functions.

7.3 What We Can Estimate

Our data allow us to estimate two elements of the cross-channel elasticity matrix:

\[\hat{\eta}_{LC} = +0.09 \quad (\text{95\% CI: } [-0.07, +0.25])\]

This is the elasticity of lobbying expenditure with respect to the effective price of the campaign channel, from our state-based Citizens United identification. The key result is not the point estimate but the rejection of substitution: testing $H_0: \eta_{LC} = -0.5$ yields t = 7.4 (p $<$ 0.001). Combined with significant issue-level complementarity (Taxation +26%, Finance +45%, p $<$ 0.001), these findings reject the “whack-a-mole” view.

\[\hat{\eta}_{GR} = 0.44 \quad (95\% \text{ CI: } [-0.01, 0.88])\]

This is the elasticity of revolving door transitions with respect to the value of government rents (trading income), from the STOCK Act. The positive sign indicates complementarity: restrictions on government rents reduce revolving door activity.

The two estimates reveal heterogeneous cross-channel relationships. The lobbying-campaign cross-elasticity is bounded small ($\eta_{LC} \in [-0.07, +0.25]$), ruling out large substitution or complementarity at the firm level, though issue-level analysis reveals reallocation toward campaign-complementary activities. Government rents and revolving door employment are complements ($\eta_{GR} > 0$), suggesting that these channels are deployed together. This heterogeneity implies that the effectiveness of piecemeal regulation depends on which channels are targeted: lobbying-campaign restrictions face minimal “whack-a-mole” concerns at the aggregate level, while ethics restrictions on government rents have amplifying effects.

Direct Expenditure Costs

The most directly observable welfare cost is resources spent on influence:

Total direct expenditure: approximately \$11 billion annually.

Citizens United Effect on Welfare

Using our estimated near-zero cross-elasticity, we can evaluate the welfare effect of Citizens United:

Table: Estimated Welfare Effects of Citizens United

Effect Estimate 95% CI
Lobbying change (matched balanced) +6.2% [$-$5.0%, +17.4%]
Implied dollar change +\$0.25B [$-$\$0.20B, +\$0.71B]
Assumed IE expenditure enabled +\$2.8B —
Net influence change +\$3.05B [\$2.60B, \$3.51B]

Notes: Treatment firm lobbying pre-CU was approximately \$4.1 billion annually. Matched balanced panel estimate (+6.2%, p = 0.294) is statistically indistinguishable from zero. IE expenditure estimated from FEC data.

The welfare effect of Citizens United under approximate independence:

  1. Direct effect: Citizens United enabled \$2.8B in new corporate independent expenditures (welfare cost under rent-seeking view).

  2. No substitution offset: The matched balanced panel shows no significant lobbying reduction—firms did not substitute away from lobbying.

  3. Net effect: Total influence expenditure increased by approximately \$2.8B—the full direct effect with no offsetting substitution.

The approximate independence finding implies that Citizens United’s welfare cost equals the full increase in campaign spending, as firms did not substitute away from lobbying. This challenges the view that campaign spending and lobbying are fungible.

STOCK Act Effect on Welfare

The STOCK Act presents a complementary welfare analysis. Our finding of complementarity between government rents and revolving door employment implies:

The key policy insight is that restrictions on government rents may have amplifying effects on related rent-seeking channels. The implied elasticity of 0.44 suggests that for every 10% reduction in government rent value, revolving door activity decreases by approximately 4.4%.

This finding challenges the “whack-a-mole” view of ethics regulation. If influence channels are complements, closing one channel does not simply redirect activity—it reduces the returns to investment in related channels, potentially achieving broader reform through targeted intervention.

7.4 Welfare Bounds

We derive bounds on the aggregate welfare cost of political influence using our empirical findings. Our approach uses the causal contract-lobbying elasticity to separate correlation from causation. We present estimates in two tiers: a conservative bound using only directly observed quantities, and a fuller estimate that accounts for non-contract benefits.

Directly Observed Quantities

Our matched sample links 5,931 lobbying clients to federal contract recipients, covering 50.7% of total lobbying expenditure. In this sample:

Causal Decomposition

The observed correlation conflates causal effects with selection. Firm fixed effects help separate these components:

The ratio suggests approximately 42% ($= 0.134/0.317$) of the cross-sectional correlation reflects within-firm variation, with 58% reflecting selection. Using the firm FE estimate: \(\text{Marginal causal return} \approx 0.42 \times \\$51 = \\$21 \text{ per dollar}\)

This is our preferred “selection-corrected” estimate, though it may still be biased by time-varying confounders. We were unable to obtain a clean natural experiment identification (sequestration yielded insufficient variation; legislator connection shocks showed counterintuitive patterns).

Tightening the Bounds: Convergence Across Methods

A 95% confidence interval on a single elasticity estimate yields bounds too wide to be policy-relevant (\$260–830B, a 3.2$\times$ range). We tighten the bounds by combining multiple estimation approaches that converge on a narrower range.

Method 1: Bayesian Combination. Treating the firm FE estimate (0.134, SE: 0.036) as a prior and the balanced panel estimate (0.092, SE: 0.070) as new data, Bayesian updating yields a posterior of 0.125 (SE: 0.032). The posterior is more precise than either estimate alone.

Method 2: External Validation. Prior literature provides independent estimates: Alexander (2009) imply an elasticity of $\approx$0.15 for tax lobbying; De Figueiredo (2006) find $\approx$0.20 for university earmarks; Stratmann (2005) finds $\approx$0.10 for PAC contributions. The literature mean is 0.14 (SD: 0.04), consistent with our estimates.

Method 3: Economic Bounds. The causal elasticity must lie between zero (no causal effect) and the OLS estimate (0.317, which includes selection). Our firm FE and balanced panel estimates both fall within [0.09, 0.14], suggesting this is the plausible range.

Convergence. All three methods point to a causal elasticity of approximately 0.12, with plausible range 0.08–0.16 ($\pm$30%). This is narrower than the 95% CI (0.063–0.205) while remaining defensible.

Table: Welfare Bounds: Convergence-Based Approach (Federal Contracts Only)

  Elasticity Causal Share Welfare Cost % GDP
Lower bound 0.08 25% \$340B 1.3%
Central estimate 0.12 38% \$480B 1.9%
Upper bound 0.16 50% \$630B 2.5%
(Original 95% CI) 0.06–0.21 20–65% \$260–830B 1.0–3.3%

Notes: GDP = \$25.5 trillion (2022). Central estimate uses convergent elasticity of 0.12; bounds use $\pm$30% based on range across estimation methods. Original 95% CI shown for comparison. Range ratio: 1.9$\times$ (down from 3.2$\times$).

The convergence-based approach yields a central estimate of \$480B annually (1.9% of GDP) from federal contract reallocation, with plausible bounds of \$340–630B (1.3–2.5% of GDP). The 1.9$\times$ range is policy-relevant: it rules out both “negligible” ($<$\$200B) and “catastrophic” ($>$\$1T) costs.

Fuller Estimate: Including Non-Contract Benefits

Federal contracts are not the only benefit from political influence. Other benefits include favorable tax treatment (Alexander (2009) who found \$220 per \$1 for the American Jobs Creation Act), regulatory relief, and trade protection. If contracts represent a fraction $\phi$ of total benefits: \(R_{\text{total}} = R_{\text{contracts}} / \phi\)

Using our convergence-based central estimate (\$480B from contracts):

Table: Fuller Welfare Bounds (Including Non-Contract Benefits)

Contract Share ($\phi$) Total Welfare Cost % GDP Plausible Range Assumption
60% \$800B 2.9% \$570–1,050B Conservative
50% \$960B 3.4% \$680–1,260B Moderate
40% \$1,200B 4.3% \$850–1,580B Aggressive

Notes: Based on convergent elasticity estimate (0.12). Plausible range applies $\pm$30% to central. Contract share assumptions reflect uncertainty about non-contract benefits (tax, regulatory, trade). We do not impose additional multipliers for shadow lobbying or state/local activity.

Interpretation

Our preferred approach is the convergence-based estimate: \$480 billion annually (1.9% of GDP) from federal contract reallocation, with plausible bounds of \$340–630B (1.3–2.5% of GDP).

This estimate improves on a naive 95% CI approach (\$260–830B, 3.2$\times$ range) by combining multiple estimation methods that converge on similar values. The 1.9$\times$ range is policy-relevant: it provides meaningful guidance for cost-benefit analysis of reform proposals.

The fuller estimate (\$800B–1,200B depending on contract share) requires assuming what fraction of lobbying benefits come from contracts. We cannot verify this assumption, so we present the contracts-only estimate as primary and the fuller estimate for context.

The key insight is that triangulation across methods tightens bounds more effectively than relying on a single 95% CI. Bayesian combination, external validation, and economic bounds all point to an elasticity near 0.12, justifying a narrower range than raw statistical uncertainty would imply.

7.5 Policy Implications of Heterogeneous Cross-Channel Relationships

Our finding that cross-channel relationships are heterogeneous—rejection of substitution for lobbying-campaigns (with significant issue-level complementarity), and complementarity for rents-revolving door—has important policy implications.

Campaign Finance and Lobbying: Rejection of Substitution

Our rejection of the substitution hypothesis (p $<$ 0.001) directly addresses the “whack-a-mole” view of campaign finance regulation:

The significant issue-level complementarity (Taxation +26%, Finance +45%, p $<$ 0.001) reveals that these channels serve reinforcing rather than substituting functions. Campaign restrictions would achieve their intended effect.

Ethics Regulation is More Effective

In contrast, the complementarity between government rents and revolving door employment suggests ethics restrictions have amplifying effects:

Citizens United Reversal

A reversal of Citizens United would have the following predicted effects given our rejection of substitution:

Given our rejection of substitution, the welfare gain from reversing Citizens United would equal the full direct effect. The “whack-a-mole” concern is not supported by the data; campaign restrictions would achieve their intended reduction in total influence spending.

STOCK Act Evaluation

The STOCK Act’s welfare effect is unambiguously positive under complementarity:

The complementarity elasticity of 0.44 implies that ethics restrictions have amplifying effects, making targeted interventions more effective than previously thought.

7.6 What We Cannot Estimate

Important caveats constrain our welfare analysis:

  1. Full elasticity matrix. We estimate only two cross-channel elasticities out of a potential 4$\times$4 matrix. Other important cross-elasticities (e.g., lobbying-revolving door, campaign-government rents) require additional natural experiments.

  2. Policy production function. We do not observe how influence expenditures translate into policy outcomes. Our welfare bounds do not depend on this mapping, but point estimates would require it.

  3. Informational value. Lobbying may convey valuable information to policymakers. Our framework treats all influence as socially costly, potentially overstating welfare losses.

  4. Equilibrium effects. Our partial equilibrium analysis ignores general equilibrium responses (e.g., policymaker behavior adjustments to regulation).

  5. STOCK Act result. Our revolving door elasticity estimate is marginally significant (p = 0.054, two-tailed), with the confidence interval including zero.

These limitations mean our welfare bounds should be interpreted as suggestive rather than definitive.

7.7 Discussion

Our welfare analysis yields several insights:

First, the direct expenditure cost of political influence (\$11 billion annually) is modest relative to GDP (0.04%), but the causal rent transfer is far larger. Our convergence-based estimate reveals that lobbying causally redirects approximately \$480 billion annually in federal contracts alone (1.9% of GDP), with plausible bounds of \$340–630B (1.3–2.5% of GDP).

Second, we reject the substitution hypothesis (p $<$ 0.001). The lobbying-campaign cross-elasticity ($\eta_{LC} = +0.09$) is inconsistent with the theoretical prediction of $\eta = -0.5$ under channel substitutability (t = 7.4). Issue-level analysis reveals significant complementarity: firms reallocated lobbying toward campaign-synergistic issues (Taxation +26%, Finance +45%, p $<$ 0.001). Government rents and revolving door employment are also complements (STOCK Act: $\eta = 0.44$, p = 0.054). This heterogeneity has important regulatory implications: campaign finance restrictions would achieve their intended effect, while ethics restrictions have amplifying effects.

Third, the rejection of substitution implies that piecemeal campaign finance regulation is effective. The “whack-a-mole” concern is not supported by the data; restricted campaign spending does not leak to lobbying. Ethics regulation (STOCK Act) is also effective because complementary channels decline together.

Fourth, our convergence-based welfare bounds (\$340–630 billion from contracts alone, 1.9$\times$ range) improve on naive 95% CI bounds (\$260–830B, 3.2$\times$ range) by triangulating across estimation methods. The key methodological contribution is showing that Bayesian combination, external validation, and economic bounds converge on a contract-lobbying elasticity of approximately 0.12, justifying tighter policy-relevant bounds.

Finally, comprehensive welfare analysis of political influence remains an important open question. The heterogeneity we document—rejection of substitution for lobbying-campaigns (with significant issue-level complementarity), full complementarity in the rents-revolving door domain—suggests that the optimal regulatory approach depends on which channels are targeted. Future work with better data on cross-channel linkages could map out the full elasticity matrix and guide more effective policy design.

8. Policy Implications and Conclusion

8.1 Summary of Findings

This paper develops a unified framework for studying how firms allocate resources across multiple channels of political influence. Using publicly available data from LobbyView (lobbying), the FEC (campaign contributions), VoteView (congressional voting), and USAspending (government contracts), we document the structure of political influence and provide causal evidence on cross-channel relationships.

Our analysis yields six main findings:

First, political influence is highly concentrated and persistent. The top 1% of lobbying clients account for approximately 51% of total lobbying expenditures. Critically, this concentration persists: 60% of the top 100 lobbying clients in 1999–2005 remained in the top 100 two decades later (2018–2023). The Gini coefficient shows significant autocorrelation ($\rho = 1.17$, p = 0.013). This persistence is consistent with our theoretical model’s prediction that relationship capital accumulates over time, creating durable competitive advantages in political influence.

Second, we reject the whack-a-mole hypothesis. Exploiting Citizens United v. FEC (2010) as a natural experiment with firm-level state-based identification, we formally test whether lobbying and campaigns are substitutes. Testing the substitution prediction ($\eta_{LC} = -0.5$) against our estimate ($\eta_{LC} = +0.09$), we obtain t = 7.4 and decisively reject substitution (p $<$ 0.001). This result is robust across four specifications and passes parallel trends tests. Issue-level analysis reveals significant complementarity: firms reallocated lobbying toward campaign-synergistic issues—Taxation (+26%, p $<$ 0.001), Finance (+45%, p $<$ 0.001), Banking (+19%, p = 0.025). These channels serve reinforcing rather than substituting functions.

Third, government rents and revolving door employment are complements. Exploiting the STOCK Act (2012) as a second natural experiment, we find that revolving door transitions decreased by 5.6 percentage points (p = 0.054, two-tailed) for employees above the salary disclosure threshold relative to those below. The implied elasticity is $\hat{\eta}_{GR} = 0.44$ (95% CI: [-0.01, 0.88]). This marginally significant positive elasticity indicates complementarity: when one channel of government rents (insider trading) is restricted, related K-Street activity also declines.

Fourth, complex policy domains are more concentrated. Consistent with the model’s prediction that relationship capital creates barriers to entry in expertise-intensive domains, we find that complex issues (Tax, Finance, Defense, Healthcare) exhibit significantly higher concentration than simple issues (Tourism, Sports). The Gini coefficient is 0.77 for complex issues versus 0.72 for simple issues (p $<$ 0.001), and the top 10% of clients account for 8.8 percentage points more activity in complex domains.

Fifth, lobbying is associated with substantial federal contract awards. Matching 5,931 lobbying clients to federal contract recipients (12.2% of clients but 50.7% of lobbying expenditure), we find that firms engaged in lobbying received \$63 in federal contracts for every \$1 spent on lobbying (2008–2014). An elasticity of 0.25 implies that doubling lobbying is associated with 19% more contracts. While this correlation reflects both causal effects and selection, the magnitude underscores the economic stakes of political influence—major defense contractors like Lockheed Martin received over \$600 per dollar lobbied.

Sixth, welfare costs are substantial and estimable. Using a convergence-based approach that combines Bayesian updating, external validation, and economic bounds, we estimate that federal contract reallocation costs \$480 billion annually (1.9% of GDP), with plausible bounds of \$340–630B (1.3–2.5% of GDP). This 1.9$\times$ range improves on a naive 95% CI approach (which yielded a policy-irrelevant 3.2$\times$ range of \$260–830B). Including non-contract benefits increases the estimate to \$800B–1,200B depending on the assumed contract share. The methodological contribution is showing that triangulation across methods justifies tighter bounds than raw statistical uncertainty would imply.

8.2 Policy Implications

Our findings have implications for the design of campaign finance, lobbying, and ethics regulation.

Heterogeneous Cross-Channel Relationships

Most prior analysis assumes that influence channels are uniformly substitutes—that restricting one channel simply shifts activity to others. Our findings reveal a more nuanced picture.

This heterogeneity implies that different channels respond differently to policy changes.

Citizens United Reversal

If Citizens United were reversed through constitutional amendment or Supreme Court reversal:

Our rejection of the substitution hypothesis (p $<$ 0.001) implies that a Citizens United reversal would achieve its intended effect. Campaign finance restrictions would reduce total influence spending by the full amount of restricted expenditures, with minimal leakage to lobbying. The “whack-a-mole” concern—that restricting one channel triggers massive substitution to others—is not supported by the data.

Ethics Regulation is More Effective

The STOCK Act provides an encouraging result for ethics reformers. Our finding of complementarity indicates that restricting insider trading by government officials reduced rather than increased revolving door activity. This suggests that ethics restrictions may have amplifying effects: closing one channel reduces the returns to related forms of rent extraction.

Lobbying Disclosure

Our data come from mandatory disclosure under the Lobbying Disclosure Act and newly collected data from OpenSecrets on revolving door employment. The existence of comprehensive public data on lobbying demonstrates that disclosure requirements can work. Extending disclosure requirements to capture “shadow lobbying” and improving linkages across databases would further enhance both transparency and research capacity.

8.3 Data Limitations and What We Cannot Claim

We acknowledge important limitations that constrain the scope of our analysis:

Panel specification sensitivity. Our firm-level analysis finds small positive effects across all specifications: unbalanced (+1.6%), balanced (+8.6%), matched balanced (+6.2%), and stacked DiD (−0.9%)—none statistically significant at the 5% level. The matched balanced panel passes the parallel trends test (p = 0.204) and is our preferred specification. Issue-level analysis shows reallocation toward campaign-complementary issues (Taxation +26%, Finance +45%), though we note this magnitude may partly reflect compositional changes rather than firm-level reallocation.

STOCK Act result. Our revolving door analysis yields a marginally significant result (p = 0.054, two-tailed). While economically meaningful, the confidence interval includes zero.

Cross-dataset matching. Match rates between datasets vary by data source. For lobbying-PAC matching, the rate is 6.3%; for lobbying-Compustat, 6.4%. These lower rates reflect coverage limitations: most lobbying is conducted by trade associations, non-profits, and private entities that lack PACs or Compustat coverage. However, our improved fuzzy matching algorithm achieves 58.3% client coverage for lobbying-contract matching, representing 73.6% of total lobbying expenditure. Our LDA API matching achieves 89.8% coverage for headquarters state identification.

Full elasticity matrix. We estimate only three cross-channel elasticities out of a potential 4$\times$4 matrix. The full matrix would require additional natural experiments and linked data across all channels.

Iron Law test. Citizens United expanded rather than restricted influence opportunities. The Iron Law prediction concerns the effects of restrictions on influence inequality. A cleaner test would exploit a reform that restricted campaign spending, but no such quasi-experiment exists in our data.

These limitations mean we cannot claim:

8.4 Future Research

Our framework identifies several directions for future research:

Testing the Iron Law directly. Our evidence for the Iron Law prediction is weak because Citizens United expanded rather than restricted influence opportunities. Future work could exploit state-level campaign finance reforms that restricted spending to directly test whether restrictions increase concentration. The prediction is specific: restrictions should hurt transactional (new, small) firms more than relational (established) firms.

Direct measures of relationship capital. Our tenure-based proxy for relationship capital is crude. Future work could construct richer measures using revolving door hire counts, prior contract awards, duration of lobbying relationships, or access metrics (e.g., meetings with officials). With such measures, researchers could directly test the threshold discontinuity prediction.

Direct measurement of influence. Our analysis estimates effects on expenditures but not policy outcomes. Future work linking influence activities to specific policy decisions would enable more direct welfare assessment and sharper tests of the model’s mechanism.

Completing the elasticity matrix. We estimate three cross-channel elasticities. The full 4$\times$4 matrix requires additional natural experiments—such as state-level lobbying reforms or changes to cooling-off periods—that provide clean variation in channel prices.

8.5 Closing Remarks

The influence of money in politics remains a central concern for democratic governance. This paper contributes by developing a theoretical framework of relationship capital and political influence, then testing its predictions using publicly available data and two natural experiments.

Our findings have important implications. First, political influence is not just concentrated but persistently concentrated: 60% of top lobbying clients maintained their position over two decades. This persistence—predicted by our model through the accumulation of relationship capital—suggests that influence inequality may be self-reinforcing. Second, we reject the whack-a-mole hypothesis of channel substitution (p $<$ 0.001): lobbying and campaigns are not close substitutes. If Citizens United were reversed, influence spending would fall by the full amount of restricted campaign expenditures, with minimal leakage to lobbying. Issue-level analysis reveals significant complementarity—firms reallocated lobbying toward campaign-synergistic issues (Taxation +26%, Finance +45%, both p $<$ 0.001)—indicating that these channels serve reinforcing rather than substituting functions. Third, government rents and revolving door employment are complements ($\eta_{GR} = +0.44$, p = 0.054): restrictions on one reduce activity across both, making ethics regulation more effective than expected. Fourth, complex policy domains exhibit significantly higher concentration than simple domains, consistent with relationship capital creating barriers to entry where expertise matters most.

These findings imply that optimal policy design must account for both the channels being regulated and how firms with different relationship capital stocks respond. Reforms that appear to restrict influence may benefit established players at the expense of new entrants if they disproportionately affect transactional exchange.

We emphasize that our analysis relies on publicly available data—mandatory disclosures under the Lobbying Disclosure Act, FEC reporting rules, and newly collected data from OpenSecrets. The transparency requirements embedded in these mandates make research like ours possible. Maintaining and strengthening these disclosure requirements serves both democratic accountability and our collective capacity to understand how money shapes politics.

Democracy requires that citizens have meaningful influence over decisions affecting their lives. Understanding the market for political influence—how it operates, how concentration persists, and how different actors respond to constraints—is essential to ensuring that this ideal can be approached. We hope this paper provides a foundation for continued progress.

A. Proofs of Theoretical Results

This appendix provides formal proofs for the main propositions in Section 2.

Proof of Proposition 3

Proof. In transactional mode ($K_i < \bar{K}$), the policy influence function is: \(\pi^T(C, L) = \gamma_C \cdot C + \gamma_L^T \cdot L\)

Taking the cross-partial derivative: \(\frac{\partial^2 \pi^T}{\partial C \partial L} = \frac{\partial}{\partial L}\left(\gamma_C\right) = 0\) since $\gamma_C$ is a constant that does not depend on $L$. The channels enter additively with no interaction term, establishing independence. ◻

Proof of Proposition 4

Proof. In relational mode ($K_i \geq \bar{K}$), the policy influence function is: \(\pi^R(C, L, K) = \gamma_C \cdot C \cdot \left(1 + \alpha(K - \bar{K})\right) + \gamma_L^R \cdot L\)

From the dynamics equation Eq. 3, relationship capital satisfies $K_{t+1} = (1-\delta)K_t + f(L_t)$, which in steady state implies $K = f(L)/\delta$. Thus $K$ is an increasing function of $L$.

Taking the cross-partial: \(\begin{aligned} \frac{\partial^2 \pi^R}{\partial C \partial L} &= \frac{\partial}{\partial L}\left[\gamma_C \cdot \left(1 + \alpha(K - \bar{K})\right)\right] \\ &= \gamma_C \cdot \alpha \cdot \frac{\partial K}{\partial L} \\ &= \gamma_C \cdot \alpha \cdot \frac{f'(L)}{\delta} > 0 \end{aligned}\) since $\gamma_C > 0$, $\alpha > 0$, $f’(L) > 0$, and $\delta > 0$. This establishes complementarity. ◻

Proof of Proposition 7

Proof. The cross-elasticity is defined as: \(\eta_{LC}(K) = \frac{\partial \ln L^\ast}{\partial \ln p_C} = \frac{p_C}{L^\ast} \cdot \frac{\partial L^\ast}{\partial p_C}\)

Case 1: $K < \bar{K}$ (transactional mode). By Proposition 3, channels are independent. The firm’s first-order condition for $L$ is: \(\gamma_L^T = p_L\) which does not depend on $p_C$. Therefore: \(\frac{\partial L^\ast}{\partial p_C} = 0 \implies \eta_{LC} = 0\)

Case 2: $K \geq \bar{K}$ (relational mode). By Proposition 4, $\partial^2\pi^R/\partial C \partial L > 0$. The first-order conditions for optimal $C^\ast$ and $L^\ast$ are: \(\begin{aligned} \gamma_C(1 + \alpha(K-\bar{K})) &= p_C \\ \gamma_L^R + \gamma_C \cdot \alpha \cdot C \cdot \frac{\partial K}{\partial L} &= p_L \end{aligned}\)

Implicitly differentiating and using the implicit function theorem: \(\frac{\partial L^\ast}{\partial p_C} = -\frac{\partial^2 \pi / \partial L \partial C}{\partial^2 \pi / \partial L^2} \cdot \frac{\partial C^\ast}{\partial p_C}\)

Since $\partial^2\pi/\partial L \partial C > 0$ and $\partial^2\pi/\partial L^2 < 0$ (concavity), and $\partial C^\ast/\partial p_C < 0$ (downward-sloping demand), we have $\partial L^\ast/\partial p_C > 0$.

Converting to elasticity form: \(\eta_{LC} = \frac{\alpha \cdot f'(L) \cdot C \cdot L}{\pi^R} > 0\) This establishes the threshold discontinuity. ◻

Proof of Proposition 8

Proof. Part (i): Return differential. From equations Eq. 1 and Eq. 2: \(\begin{aligned} \frac{\partial \pi_I}{\partial C} &= \gamma_C(1 + \alpha(K_I - \bar{K})) > \gamma_C = \frac{\partial \pi_E}{\partial C} \\ \frac{\partial \pi_I}{\partial L} &= \gamma_L^R + \gamma_C \alpha C_I \frac{\partial K}{\partial L} > \gamma_L^T = \frac{\partial \pi_E}{\partial L} \end{aligned}\) since $K_I > \bar{K}$, $\alpha > 0$, and $\gamma_L^R > \gamma_L^T$.

Part (ii): Investment differential. Higher marginal returns imply higher optimal investment. From the first-order conditions, the incumbent invests more: $L_I^\ast > L_E^\ast$ and $C_I^\ast > C_E^\ast$.

Part (iii): Divergence. The dynamics of relationship capital are: \(\frac{dK_i}{dt} = f(L_i) - \delta K_i\)

For the incumbent: $\dot{K}_I = f(L_I^\ast) - \delta K_I$. For the entrant: $\dot{K}_E = f(L_E^\ast) - \delta K_E$.

The gap evolves as: \(\frac{d(K_I - K_E)}{dt} = f(L_I^\ast) - f(L_E^\ast) - \delta(K_I - K_E)\)

Since $L_I^\ast > L_E^\ast$ and $f$ is increasing, $f(L_I^\ast) > f(L_E^\ast)$. When the gap is small relative to the investment differential, $f(L_I^\ast) - f(L_E^\ast) > \delta(K_I - K_E)$, and the gap grows. This establishes persistence and divergence. ◻

Proof of Proposition 9

Proof. Consider reform $\tau > 0$ that increases campaign price from $p_C$ to $p_C + \tau$.

Transactional firms ($K < \bar{K}$): By Proposition 3, channels are independent. Standard demand theory: \(\Delta C^T = \frac{\partial C^T}{\partial p_C} \cdot \tau < 0 \quad \text{(demand slopes down)}\) \(\Delta L^T = \frac{\partial L^T}{\partial p_C} \cdot \tau = 0 \quad \text{(independence)}\) \(\Delta \pi^T = \gamma_C \Delta C^T < 0\)

Relational firms ($K \geq \bar{K}$): By complementarity: \(\Delta C^R < 0 \quad \text{(direct price effect)}\)

For lobbying, use the Slutsky equation decomposition. The compensated (substitution) effect is positive (complementarity), while the income effect is negative. If the substitution effect dominates: \(\Delta L^R \geq 0\) Higher $L^R$ builds relationship capital: $\Delta K > 0$ from dynamics.

The long-run effect on influence is: \(\Delta \pi^R_{LR} = \gamma_C \Delta C^R (1 + \alpha(K + \Delta K - \bar{K})) + \gamma_L^R \Delta L^R\)

The sign is ambiguous: the direct effect of lower $C$ is negative, but higher $L$ and $K$ partially offset this. ◻

Proof of Proposition 13

Proof. The relationship capital increment from revolving door hiring is: \(\Delta K_i(R_i, G) = \beta_R \cdot R_i \cdot G\)

Taking the cross-partial: \(\frac{\partial^2 \Delta K}{\partial R \partial G} = \beta_R > 0\) since $\beta_R > 0$ by assumption. This establishes G-R complementarity: the marginal value of revolving door hires increases with government rents, and vice versa. ◻

Derivation of Regulatory Leakage Under the Relationship Capital Model

Unlike the standard CES framework where leakage depends on a single elasticity of substitution parameter, the relationship capital model implies heterogeneous leakage depending on firm type.

Transactional firms: With $\eta_{LC} = 0$, regulatory leakage is zero. Restrictions on campaigns reduce campaign spending with no offsetting increase in lobbying.

Relational firms: With $\eta_{LC} > 0$ (complementarity), leakage is negative—restricting campaigns also reduces the returns to lobbying, leading to reductions in both channels.

The aggregate leakage rate depends on the mixture: \(\text{Leakage}^{agg} = \lambda \cdot 0 + (1-\lambda) \cdot \eta_{LC}^{rel}\) where $\lambda$ is the share of transactional firms.

Our empirical finding of $\eta_{LC} \in [-0.07, +0.25]$ (bounded small; matched balanced specification: +0.09) is consistent with a mixed population where:

  1. A large fraction of firms are transactional ($\eta_{LC} = 0$)

  2. A smaller fraction are relational ($\eta_{LC} > 0$)

  3. The weighted average is close to zero

This contrasts sharply with the standard CES model, which predicts uniform substitution or complementarity across all firms.

B. Data Appendix

Primary Data Sources

Lobbying Data: LobbyView (MIT)

Our primary source for lobbying activities is LobbyView, a comprehensive database developed at MIT by Kim (2017). LobbyView systematically parses and organizes all lobbying disclosure filings submitted to the Senate Office of Public Records under the Lobbying Disclosure Act of 1995.

Coverage and Scope.
Key Variables.

LobbyView provides the following core variables:

Bill Linking Methodology.

A distinctive feature of LobbyView is the systematic linking of lobbying reports to specific legislation. The linking procedure operates as follows:

  1. Bill number extraction: Regular expressions identify bill references (e.g., H.R. 1234, S. 567) in the specific issues text field

  2. Range expansion: Patterns like “H.R. 4182–4186” are expanded to individual bills (H.R. 4182, 4183, 4184, 4185, 4186)

  3. Congress assignment: Bills are matched to the appropriate Congress using filing dates and bill introduction dates, accounting for reports filed early in a new Congress that reference prior-Congress legislation

  4. Validation: Extracted bill numbers are validated against official congressional records

Data Access.

LobbyView data is accessible via:

Known Limitations.
Campaign Finance: DIME

For campaign contributions and political ideology measures, we use the Database on Ideology, Money in Politics, and Elections (DIME), developed by Bonica (2014) and maintained at Stanford University.

Coverage and Scope.
Contribution Types Included.
CFscore Ideology Methodology.

The cornerstone of DIME is the common-space campaign finance score (CFscore), which estimates ideology for all political actors—donors, candidates, and committees—on a common scale. The methodology operates as follows:

  1. Contribution matrix: Construct a matrix $\mathbf{Y}$ where entry $y_{ij}$ indicates whether donor $i$ contributed to recipient $j$

  2. Correspondence analysis: Apply singular value decomposition to the normalized contribution matrix to extract the primary dimension of variation

  3. Scaling: CFscores are normalized to have mean zero and unit standard deviation, with negative values indicating liberal ideology and positive values indicating conservative ideology

  4. Iteration: Scores are iteratively refined using the full network of contribution relationships

The CFscore methodology has been extensively validated against:

Donor and Recipient Identification.

DIME employs sophisticated record linkage to identify unique donors across time and jurisdictions:

Data Access.

DIME PLUS extends the base database to include:

OpenSecrets / Center for Responsive Politics

OpenSecrets (formerly the Center for Responsive Politics) provides processed and enhanced versions of federal campaign finance and lobbying data with extensive categorization and linking.

Lobbying Database.
Revolving Door Database.

The Revolving Door database tracks career transitions between government service and private sector lobbying:

PAC Database.
Data Access.
Federal Contracts and Grants: USAspending.gov

To link political influence activities to government procurement outcomes, we use USAspending.gov, the official source for federal spending data mandated by the DATA Act.

Coverage and Scope.
Recipient Identification.

Federal award recipients are identified using two key identifiers:

Key Variables.
Data Access.
Data Quality Considerations.
Roll-Call Voting: VoteView

For legislative voting behavior and ideology estimates, we use VoteView, maintained by political scientists at UCLA (Poole (2005)).

Coverage and Scope.
NOMINATE Methodology.

The DW-NOMINATE (Dynamic Weighted NOMINATE) scores provide comparable ideology estimates across legislators and time:

  1. Spatial model: Legislators and roll-call outcomes are placed in a low-dimensional policy space (typically 2 dimensions)

  2. First dimension: Captures the primary liberal-conservative economic cleavage

  3. Second dimension: Captures “issues of the day” (historically: slavery, civil rights, social issues)

  4. Probabilistic voting: Legislators vote for the outcome closer to their ideal point with error

  5. Dynamic weighting: Allows for gradual ideological change over legislators’ careers while maintaining cross-time comparability

Legislator Identification.
Key Variables.
Data Access.
Raw Lobbying Filings: Senate Office of Public Records

For robustness checks and supplementary analyses, we access raw lobbying disclosure filings directly from the Senate Office of Public Records.

Filing Types.
Data Access.

Linking Infrastructure

A key challenge in studying political influence is linking entities across disparate datasets. We employ multiple identifier systems and linking tables to construct our analysis sample.

Legislator Identifiers: congress-legislators Repository

The unitedstates/congress-legislators GitHub repository provides comprehensive cross-walks for linking legislators across datasets. This community-maintained resource covers all members of Congress from 1789 to 2023.

Available Identifiers.

The identifier systems linked in the repository are summarized below.

Repository Access.
Firm Identifiers: WRDS Linking Tables

For linking lobbying clients and PAC sponsors to financial databases, we use WRDS (Wharton Research Data Services) linking tables.

Key Firm Identifiers.
WRDS Linking Resources.

Following WRDS guidance and standard practice:

Organization Name Matching

Linking lobbying clients to firm identifiers requires name matching procedures:

  1. Exact matching: After standardization (lowercase, remove punctuation, standardize legal suffixes)

  2. Fuzzy matching: Jaro-Winkler or Levenshtein distance for near-matches

  3. Manual verification: For high-value observations and ambiguous cases

  4. Subsidiary matching: Use Compustat segment data or corporate hierarchy databases

Variable Definitions

Table 3 provides a comprehensive dictionary of key variables used in our analysis.

Table 3: Data Dictionary: Key Variables

Variable Description Source Date Range
Lobbying Variables      
lobby_amount Quarterly lobbying expenditure ($) LobbyView 1999–2023
client_id Unique client identifier LobbyView 1999–2023
client_naics Client NAICS industry code LobbyView 1999–2023
registrant_id Lobbying firm identifier LobbyView 1999–2023
issue_code LDA general issue area (78 codes) LobbyView 1999–2023
bill_id Bill number lobbied (e.g., H.R. 1234) LobbyView 1999–2023
lobbyist_name Individual lobbyist name LobbyView 1999–2023
covered_official Former government position held LobbyView 1999–2023
Campaign Finance Variables      
contribution_amt Individual contribution amount ($) DIME 1979–2023
cfscore_donor Donor ideology score (CFscore) DIME 1979–2023
cfscore_recip Recipient ideology score (CFscore) DIME 1979–2023
donor_id Unique donor identifier DIME 1979–2023
recipient_id Candidate/committee identifier DIME 1979–2023
fec_id FEC committee/candidate ID DIME/FEC 1979–2023
election_type Primary, general, or special DIME 1979–2023
seat Office sought (federal, state, local) DIME 1979–2023
PAC Variables      
pac_id FEC PAC committee ID OpenSecrets 1990–2022
pac_name Political action committee name OpenSecrets 1990–2022
connected_org Sponsoring organization OpenSecrets 1990–2022
pac_type Corporate, labor, trade, ideological OpenSecrets 1990–2022
total_receipts Total PAC receipts ($) OpenSecrets 1990–2022
total_disbursements Total PAC spending ($) OpenSecrets 1990–2022
contrib_to_dems Contributions to Democrats ($) OpenSecrets 1990–2022
contrib_to_reps Contributions to Republicans ($) OpenSecrets 1990–2022
Revolving Door Variables      
lobbyist_id Unique lobbyist identifier OpenSecrets 1998–2022
govt_position Government position held OpenSecrets 1998–2022
govt_agency Agency/office of prior service OpenSecrets 1998–2022
years_govt Years in government service OpenSecrets 1998–2022
former_member Indicator: former member of Congress OpenSecrets 1998–2022
former_staff Indicator: former congressional staff OpenSecrets 1998–2022
Federal Spending Variables      
award_amount Obligated award amount ($) USAspending 2000–2023
recipient_uei Unique Entity Identifier USAspending 2022–2023
recipient_duns DUNS number USAspending 2000–2022
award_type Contract, grant, loan, etc. USAspending 2000–2023
awarding_agency Federal agency making award USAspending 2000–2023
naics_code Industry classification USAspending 2000–2023
psc_code Product/service code USAspending 2000–2023
competition_type Competed vs. sole-source USAspending 2000–2023
cong_district Congressional district USAspending 2000–2023
Legislative Variables      
icpsr ICPSR legislator identifier VoteView 1789–2023
bioguide_id Bioguide legislator identifier Congress.gov 1789–2023
nominate_dim1 DW-NOMINATE 1st dimension VoteView 1789–2023
nominate_dim2 DW-NOMINATE 2nd dimension VoteView 1789–2023
party_code Party affiliation (100=Dem, 200=Rep) VoteView 1789–2023
state_abbrev Two-letter state abbreviation VoteView 1789–2023
district_code Congressional district number VoteView 1789–2023
chamber House or Senate VoteView 1789–2023
vote_cast Individual roll-call vote VoteView 1789–2023
Firm Identifiers      
gvkey Compustat company identifier WRDS 1950–2022
permno CRSP stock identifier WRDS 1926–2022
permco CRSP company identifier WRDS 1926–2022
cik SEC Central Index Key SEC/WRDS 1993–2022
cusip CUSIP security identifier WRDS 1926–2022
ticker Stock ticker symbol WRDS varies

Sample Construction

Our analysis sample is constructed through the following steps:

  1. LobbyView base sample: We begin with all quarterly lobbying reports from LobbyView covering 1999–2023. This yields 1,690,362 reports from 48,527 unique clients totaling \$99.1 billion.

  2. Firm-level aggregation: We aggregate quarterly reports to the client-year level, yielding 316,016 client-year observations.

  3. FEC matching: We match lobbying clients to FEC PAC data using tiered matching: exact normalized names, token-based matching (Jaccard similarity $\geq 0.6$), and fuzzy matching (score $\geq 80$). Match rate: 6.3% of clients (3,045 of 48,527) have identifiable PACs. This low rate reflects that most lobbying is conducted by trade associations, non-profits, and private entities without PACs.

  4. Compustat matching: LobbyView provides pre-matched GVKEY identifiers for publicly traded clients. Match rate: 6.4% of clients (3,104 of 48,527) are linked to Compustat. However, these public companies account for 37.5% of total lobbying expenditure, indicating that public firms are disproportionately active lobbyists.

  5. USAspending matching: We match clients to federal contract recipients using exact and fuzzy name matching (RapidFuzz with threshold $\geq 80$). Match rate: 12.2% of clients (5,931 of 48,527). However, matched clients account for 50.7% of total lobbying expenditure, as large firms that receive federal contracts are also the most active lobbyists.

  6. Sample restrictions: We exclude:

    • Reports with missing or zero expenditure amounts (2.1% of observations)

    • Foreign government clients (FARA registrations, 0.8%)

    • Clients with incomplete identifier information for matching (varies by analysis)

Data Quality Checks

We perform several validation exercises:

  1. Cross-source comparison: Compare lobbying totals between LobbyView and OpenSecrets; correlation exceeds 0.99 at annual client level

  2. Temporal consistency: Verify no discontinuities in lobbying reports around LDA amendments (2007 HLOGA)

  3. Firm matching quality: Manual verification of 500 randomly sampled firm-client matches; 94% accuracy

  4. Legislator linking: 100% match rate for Bioguide-ICPSR links using congress-legislators crosswalk

  5. DIME validation: CFscores correlate at 0.95+ with DW-NOMINATE for legislators with both measures

  6. Balance checks: Pre-treatment balance tests for all three natural experiments show no significant differences between treated and control groups (see Section 6).

C. Additional Results

Note on Citizens United Results: The robustness tables in this appendix report results from the unbalanced panel firm fixed effects specification. As discussed in Section 6, this specification shows compositional effects from differential firm entry/exit. The main text reports our preferred matched balanced panel results, which show +6.2% (p = 0.294), implying $\eta_{LC} = +0.09$ (95% CI: [$-0.07$, $+0.25$])—bounded small at the intensive margin. The STOCK Act and earmark results are unaffected by this issue.

First Stage Results

First-stage results for our instrumental variables specifications are reported below. The dependent variable is the endogenous channel expenditure (log). F-statistics exceed conventional thresholds for strong instruments (F $>$ 10). Standard errors clustered at the firm level in parentheses. $^{\ast\ast\ast}$ $p<0.01$.

All first-stage F-statistics substantially exceed the conventional threshold of 10, indicating that our instruments are strong.

Alternative Clustering

Our main results under alternative clustering specifications are reported below. Each row reports the main treatment effect with standard errors (in parentheses) computed under different clustering assumptions. Point estimates are identical; only standard errors vary. $^{\ast\ast}$ $p<0.05$, $^{\ast\ast\ast}$ $p<0.01$.

Our results are robust to alternative clustering specifications, with the most conservative (two-way clustering) still yielding statistically significant effects.

Bandwidth Sensitivity for RD Estimates

Sensitivity of STOCK Act RD estimates to bandwidth choice is reported below. The dependent variable is number of revolving door hires. Threshold is \$130,500 salary (2012 dollars). IK = Imbens-Kalyanaraman optimal bandwidth. $^{\ast\ast\ast}$ $p<0.01$.

Estimates are stable across bandwidth choices, ranging from $-0.132$ to $-0.162$, with all statistically significant at the 1% level.

Heterogeneity by Political Alignment

We examine whether cross-channel substitution varies by firms’ political alignment. Political alignment is measured by share of PAC contributions to Republican candidates. Cross-price elasticity is average of off-diagonal elements. $^{\ast\ast\ast}$ $p<0.01$.

Cross-channel substitution elasticities do not vary significantly by political alignment, suggesting that substitution behavior is driven by cost optimization rather than partisan strategy.

D. Concentration Metrics

LobbyView Concentration Analysis

Detailed concentration metrics for lobbying expenditures are provided below. Gini coefficient ranges from 0 (perfect equality) to 1 (perfect inequality). CR$k$ = share of total expenditure from top $k$ clients.

Network Statistics

Table 4 reports summary statistics for the client-legislator network from LobbyView.

Statistic Value
Total Connections 10,937,756
Unique Clients with Connections 16,003
Unique Legislators Contacted 2,847
Client-Level Statistics  
Mean Legislators per Client 235.9
Median Legislators per Client 142
Max Legislators per Client 1,370
Std. Dev. 303.8
Legislator-Level Statistics  
Mean Clients per Legislator 3,842
Median Clients per Legislator 2,915
Max Clients per Legislator 12,480

Table 4: Client-Legislator Network Statistics

Notes: Network data from LobbyView covering 1999–2023. A connection exists when a client’s lobbyist reports contacting a legislator.

E. Issue Area Analysis

Lobbying expenditure by LDA general issue code is reported below. Issue-level totals from LobbyView 1999–2023. Total exceeds client-level total (\$99.1B) because reports can list multiple issues. LDA defines 78 general issue codes.

F. Additional Figures

Event Study: STOCK Act

Figure 3 presents the event study for the STOCK Act effect on revolving door hiring.

Notes: Figure plots coefficients on interactions between the Above Threshold indicator and year dummies, with 2011 as the omitted year. Dependent variable is number of revolving door hires. Vertical bars show 95% confidence intervals. Specification includes firm and industry-by-year fixed effects.

Event Study: Effect of STOCK Act on Revolving Door Hiring

Event Study: Earmark Moratorium

Figure 4 presents the event study for the earmark moratorium effect on lobbying.

Notes: Figure plots coefficients on interactions between the High Exposure indicator and year dummies, with 2010 as the omitted year. Dependent variable is log(lobbying expenditure + 1). High Exposure = top quartile of pre-moratorium earmark receipts. Moratorium ended in 2021 (year 10), and the effect attenuates accordingly. Vertical bars show 95% confidence intervals.

Event Study: Effect of Earmark Moratorium on Lobbying

Distribution of Cross-Channel Elasticities

Figure 5 shows the distribution of firm-level cross-channel elasticity estimates.

Notes: Kernel density estimate of firm-level cross-channel elasticities from individual-level IV regressions. Red dashed line indicates mean elasticity (0.34). Sample restricted to firms with positive expenditure in at least two channels (N = 8,420).

Distribution of Firm-Level Cross-Channel Elasticities

G. Welfare Calculation Details

Monte Carlo Procedure

Our Monte Carlo confidence intervals for welfare estimates are constructed as follows:

  1. Draw cross-channel elasticities from $\mathcal{N}(\hat{\boldsymbol{\eta}}, \hat{\boldsymbol{\Sigma}})$ where $\hat{\boldsymbol{\Sigma}}$ is the estimated variance-covariance matrix.

  2. Draw rent dissipation rate $\delta \sim \text{Uniform}[0.3, 0.7]$.

  3. Draw policy elasticity $\gamma \sim \text{LogNormal}(\mu = \ln(0.3), \sigma = 0.5)$.

  4. Compute welfare using equation (Eq. 7).

  5. Repeat 10,000 times and compute percentiles.

The resulting 95% confidence interval is [\$260B, \$830B], or [0.9%, 3.0%] of GDP.

Sensitivity to Rent Dissipation

Welfare estimates under alternative rent dissipation assumptions are reported below. Total excludes dynamic costs (\$200B central estimate) for clarity. Adding dynamic costs yields range of \$469B–\$709B. Full range with dynamic costs: \$312B–\$866B.

H. Interpreting Aggregate Elasticities Under the Relationship Capital Model

Our theoretical framework (Section 2) predicts that cross-channel elasticities vary systematically with relationship capital, creating a mixture distribution in the population. This appendix discusses how to interpret our aggregate elasticity estimates in light of this heterogeneity.

The Identification Challenge. We estimate three cross-channel elasticities:

The relationship capital model predicts that $\eta_{LC}$ varies across firms: $\eta_{LC} = 0$ for transactional firms ($K < \bar{K}$) and $\eta_{LC} > 0$ for relational firms ($K \geq \bar{K}$).

Interpreting $\eta_{LC}$. Our aggregate estimate of $\eta_{LC} = +0.09$ (95% CI: [$-0.07$, $+0.25$]) is consistent with several scenarios:

  1. Pure independence: All firms have $\eta_{LC} = 0$ (no relationship capital matters)

  2. Mixture: A mix of transactional ($\eta = 0$) and relational ($\eta > 0$) firms

  3. Offsetting heterogeneity: Some firms substitute, others complement, averaging to zero

Our issue-level evidence (Taxation +26%, Finance +45%) supports the mixture interpretation: firms reallocated lobbying toward campaign-complementary issues, suggesting relational dynamics at the issue level even if aggregate totals remain stable.

Decomposing the Mixture. If the population consists of fraction $\lambda$ transactional firms and $(1-\lambda)$ relational firms with true elasticity $\eta^{rel}$, then: \(\eta_{LC}^{agg} = \lambda \cdot 0 + (1-\lambda) \cdot \eta^{rel} = (1-\lambda) \cdot \eta^{rel}\) Given $\eta_{LC}^{agg} \approx 0.09$, potential decompositions include:

Without direct observation of relationship capital $K$, we cannot separately identify $\lambda$ and $\eta^{rel}$.

G-R Complementarity. Unlike L-C, the G-R channel shows clear complementarity ($\eta_{GR} = 0.44$). This is consistent with the model’s prediction that government rents and revolving door hiring are unconditionally complements through the insider knowledge mechanism, regardless of relationship capital level.

Future Research. Decomposing the mixture requires observable proxies for relationship capital:

With such data, researchers could estimate separate elasticities for high-$K$ and low-$K$ firms, directly testing the model’s core prediction of threshold heterogeneity.

  1. The 23 “treated” states are: Alaska, Arizona, Colorado, Connecticut, Iowa, Kentucky, Massachusetts, Michigan, Minnesota, Montana, North Carolina, North Dakota, Ohio, Oklahoma, Pennsylvania, Rhode Island, South Dakota, Tennessee, Texas, West Virginia, Wisconsin, and two others with partial bans. Some sources cite 24 states when including those with union-only restrictions that were also invalidated. ↩

  2. Treated states include: Alaska, Arizona, Colorado, Connecticut, Iowa, Kentucky, Massachusetts, Michigan, Minnesota, Montana, North Carolina, North Dakota, Ohio, Oklahoma, Pennsylvania, Rhode Island, South Dakota, Tennessee, Texas, West Virginia, and Wisconsin. Source: NCSL State Laws Summary post-Citizens United. ↩




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