D73 | Macro Paper Warehouse

Investing in Influence: Investors, Portfolio Firms, and Political Giving

Mon, 01 Jan 0001 00:00:00 +0000

This paper investigates whether institutional investors influence the political activities of their portfolio firms, using political action committee (PAC) giving as a window into the broader question of whether institutional investors can leverage their concentrated ownership to extract benefits from portfolio firms for their own interests rather than those of their clients.

The sample covers 574 institutional investors (those with at least $100 million in assets under management, i.e., 13-F filers) matched to 2,456 portfolio firms that had PACs, over the period 1980–2018. The primary source of variation is the first acquisition by an institutional investor of at least one percent of a portfolio firm’s outstanding shares, yielding 68,387 large acquisition events. PAC giving data come from FEC records matched by name to investor and firm entities. The main regression specification examines how the relationship between investor and firm PAC contributions to the same congressional district changes after such an acquisition, using a saturated set of fixed effects including firm × investor, firm × congressional district, firm × election cycle, investor × congressional district, investor × election cycle, and district × election cycle.

The central finding is that, following a large block purchase, a firm’s PAC giving mirrors more closely that of the acquiring investment management company. In the preferred specification (column 8 of Table 2), the probability that a portfolio firm gives to a politician supported by its investor’s PAC increases by 31 percent after an acquisition. Using a cosine similarity measure of investor-firm PAC giving, the mean similarity of 0.10 at the acquisition cycle rises by 0.02–0.03 (a 20–30 percent increase) by the fourth post-acquisition election cycle.

A key identification concern is that acquisitions may be driven by shared political preferences rather than representing a causal effect. To address this, the authors exploit stock index inclusions as exogenous shifters of institutional investor block purchases: when a firm is added to an index for the first time, passive indexers are compelled to rebalance toward that firm regardless of political alignment. Restricting to 5,601 index-inclusion acquisitions by passive investors, the authors find near-identical effect sizes (beta1 = 0.0132 in column 8 versus 0.0135 in the full sample), and an event study shows no pre-trend in giving convergence for the index subsample, in contrast to a slight pre-trend in the full sample. Divestment events exhibit the symmetric negative pattern: the interaction of post-divestment and investor PAC giving falls by between -0.074 and -0.058 across specifications.

The authors argue that investors drive the convergence rather than portfolio firms adjusting investor preferences. Around acquisition dates, firms exhibit a larger drop in between-election-cycle cosine similarity than investors do. In a difference-in-differences comparison of the acquisition period relative to the preceding period, the difference in stability between investors and firms is 0.075 (significant at the 1 percent level), indicating that firms shift their giving more than investors. Investors obtaining a board seat at the portfolio firm amplifies the effect: in the preferred specification, the board-seat interaction is more than twice as large as the acquisition-alone interaction.

Heterogeneity analysis provides evidence that the convergence reflects investors’ partisan tastes rather than coordinated profit-maximizing political strategy. Acquisitions by more partisan investors (those whose giving is more skewed toward one party) produce a convergence coefficient roughly twice as large (0.020) as less partisan investors (0.010). Private fund families show more than twice the convergence effect of publicly owned fund families. The partisan composition of firm giving also shifts: a firm acquired by an investor giving exclusively to Republicans sees its Republican share increase by 2.8 percentage points relative to a baseline of 47.4 percent (a 5.9 percent increase).

Finally, higher overall institutional ownership is associated with an increase in total PAC giving at the firm level, and this expanded giving does not go disproportionately to politicians on committees overseeing issues the firm actively lobbies — suggesting the ownership-driven increment in political spending is non-strategic from the firm’s profit standpoint and likely serves investors’ own interests.

Q: What is the central research question and why does it matter? The paper asks whether institutional investors influence the political giving of portfolio firms, motivated by the broader concern that the rise of institutional ownership — from 6 percent of U.S. public equities in 1950 to 65 percent in 2017 — concentrates not only economic but also political power in the hands of a small number of asset managers. This matters because if investors shape firms’ PAC giving to serve investors’ own preferences rather than firms’ profit interests, it represents a misuse of corporate resources and a potential amplification of a small group’s political voice.

Q: What data are used and how is the sample constructed? The analysis draws on 13-F filings (investors with at least $100M AUM) from Thomson-Reuters, matched to FEC PAC records via fuzzy and manual name matching. The resulting sample contains 574 investors with PACs and 2,456 portfolio firms with PACs, spanning 1980–2018. The Cartesian product of investor-firm pairs is restricted to those connected by at least one large acquisition event (defined as first acquisition of at least 1 percent of outstanding shares), yielding 68,387 such events. PAC contributions are measured at the investor- and firm-congressional-district-election-cycle level, linked to House of Representatives winners using MIT Election Data files.

Q: What is the baseline regression and what does it find? The baseline regression (equation 1) interacts Log Investor PAC with a Post indicator (equal to 1 after the first large acquisition and while the stake is maintained) at the investor-firm-congressional-district-election-cycle level, with a saturated set of fixed effects. The coefficient on the interaction (beta1) is positive and highly significant (p < 0.001) across all eight specifications, ranging from 0.013 to 0.032. In the preferred specification, the increase in giving similarity is 31 percent relative to the pre-acquisition baseline.

Q: How do the authors establish causality and rule out endogenous acquisitions? The primary identification strategy uses first-time inclusions of firms in stock indices (approximately 1,000 indices tracked in the sample) as exogenous shifters: passive indexers must rebalance toward the included firm regardless of political alignment. This subsample of 5,601 index-inclusion acquisitions produces near-identical coefficient estimates (0.0132 versus 0.0135 in the full sample), and the event study for this subsample shows no pre-trend in giving convergence, unlike the slight pre-trend in the full sample. Equality of the two coefficients cannot be rejected at standard significance levels.

Q: What evidence shows it is firms adjusting to investors rather than the reverse? The authors compute between-election-cycle cosine similarity separately for investors and firms around acquisitions. On average, investors exhibit more stable giving than firms at acquisition dates (Cos(xi,t, xi,t+1) > Cos(xf,t, xf,t+1)). The difference-in-differences estimate — comparing the acquisition period to the preceding period — is 0.075 (significant at 1 percent), indicating a relatively larger break in firm giving. Over a two-cycle window, the difference-in-differences estimate is 0.083, again indicating convergence is driven by firms shifting toward investors rather than the reverse.

Q: What role does board representation play? In approximately 5 percent of acquisitions in the sample, the investor obtains a board seat. In specifications that include both the acquisition effect (Post × Log Investor PAC) and a board-membership interaction (Board × Log Investor PAC), both terms are positive and significant at the 1 percent level. In the preferred specification, the board-seat interaction is more than twice as large as the acquisition-alone interaction, indicating that a direct governance channel — board representation — substantially amplifies the convergence in political giving.

Q: What does the divestment analysis show? Symmetric to the acquisition results, divestment events (where an investor exits a stake of at least 1 percent held for at least one election cycle) are associated with a decline in investor-firm PAC giving correlation. Post-divestment interaction coefficients range from -0.074 to -0.058 across specifications, and an event study confirms the correlation falls sharply after the divestment cycle.

Q: Does investor partisanship affect the magnitude of influence? Yes. Classifying investors as “More Partisan” (above-mean absolute deviation from 50/50 party split) versus “Less Partisan,” the interaction coefficient for More Partisan investors (0.020) is roughly twice that of Less Partisan investors (0.010). After a large acquisition by a fully Republican-giving investor, the acquired firm’s giving to that politician increases by 23.5 percent; the comparable figure for a Less Partisan investor is 7.6 percent. This pattern holds in both the full sample and the index-inclusion subsample.

Q: How do private versus public fund families differ in their influence? Private fund families (e.g., Vanguard, Fidelity) show more than twice the convergence coefficient of publicly owned fund families (e.g., BlackRock, State Street, Invesco). The authors attribute this to private fund managers facing less outside scrutiny, allowing their giving to more readily reflect the preferences of owners and managers. Private investors also show greater partisan polarization: the 10th–90th percentile Republican-giving range for private investors is 6.3–100 percent, versus 21.7–88.3 percent for public investors.

Q: Does increased institutional ownership expand overall firm PAC spending? Yes. In firm-year level regressions, institutional ownership is a positive and significant predictor of total firm PAC giving (significant at at least the 5 percent level in both cross-sectional and firm-fixed-effects specifications). Total corporate political expenditure by sample firms increased by nearly a factor of six over 1980–2018. The authors note that while many factors contribute, increased institutional ownership may be at least partly responsible for this expansion.

Q: Does the additional giving driven by institutional ownership go to strategically important politicians for the firm? No. Regressions relating institutional ownership to giving to politicians on congressional committees overseeing issues the firm actively lobbies (a standard measure of politicians’ strategic importance to firms) yield near-zero and statistically weak point estimates. In the preferred firm-fixed-effects specification, the share of total PAC giving devoted to such strategically relevant politicians is negatively associated with institutional ownership at marginal significance (p < 0.10), consistent with the interpretation that ownership-driven incremental political spending is non-strategic from the firm’s own profit perspective and expands total giving rather than displacing strategic giving.

Q: What are the policy and legal implications? The authors flag three concerns: (i) the ownership-driven increment in political spending may represent a misuse of corporate resources that does not serve portfolio firm shareholders; (ii) it may constitute an illegal activity, since using a firm’s PAC to reimburse or proxy for an investor’s own political preferences can run afoul of campaign finance law; and (iii) it is a channel through which unequal resources amplify the political voice of a small number of fund managers at the expense of dispersed ultimate investors who are likely unaware of and do not sanction these contributions. The findings challenge the Supreme Court’s premise in Citizens United that corporate political speech reflects shareholder profit maximization.

PAC comovement (investor-firm giving similarity): The increase in the probability that a portfolio firm’s PAC donates to a politician also supported by an acquiring investor’s PAC, measured as the interaction coefficient between Log Investor PAC and a Post-acquisition indicator in the baseline regression. In the preferred specification this represents a 31 percent increase relative to the pre-acquisition baseline.

Cosine similarity (cross-time and cross-entity): A measure defined as the Euclidean dot product between two vectors of PAC giving (either the same entity across adjacent election cycles, or investor versus firm in the same cycle), taking values between 0 and 1, where 1 indicates identical giving patterns. Used both to confirm convergence post-acquisition and to attribute that convergence to firm rather than investor adjustment.

Index-inclusion acquisition: A large block purchase that results from a firm being added for the first time to a stock index tracked by a passive institutional investor, used as an exogenous shifter of investor stakes that is orthogonal to investor-firm political alignment. There are 5,601 such events in the sample.

Partisanship (investor): Classified as “More Partisan” if an investor’s absolute deviation from a 50/50 party split in PAC donations is above the sample mean. More partisan investors produce roughly twice the convergence effect on portfolio firm giving compared to less partisan investors, used as evidence that personal political preferences rather than profit-maximizing business strategy drive the convergence.

Post indicator (Postift): A binary variable equal to 1 for all election cycles following an investor’s first acquisition of at least 1 percent of a portfolio firm’s outstanding shares, and remaining 1 as long as the investor holds any stake in the firm. The key source of temporal variation in the baseline regression.

Strategically important politicians: Members of Congress sitting on committees that oversee issues on which a firm actively lobbies, identified by crosswalking lobbying reports from the Senate Office of Public Records to relevant committee jurisdictions. Used to test whether ownership-driven political giving displaces or supplements firm-profit-motivated giving.

Board seat channel: The mechanism through which investor influence on firm political giving is amplified when the investor obtains representation on the portfolio firm’s board of directors (present in approximately 5 percent of acquisitions). The board interaction coefficient is more than twice the acquisition-alone coefficient in the preferred specification.

Politics at Work

Mon, 01 Jan 0001 00:00:00 +0000

Layer 1 — Overview

Research Question

Do individual political views shape firm behavior and labor market outcomes in the private sector? Specifically, do business owners sort copartisan workers into their firms, and does employers’ political discrimination drive this sorting?

Data and Setting

The paper studies the complete Brazilian formal labor market over 2002–2019, assembling a novel longitudinal worker-firm-owner-party matched dataset from three administrative sources: (1) RAIS (Relação Anual de Informações Sociais), the universe of formal-sector workers (87 million unique workers, 7.6 million unique firms); (2) the Receita Federal do Brazil (RFB) and Cadastro Nacional de Empresas (CNE), containing business ownership structures for all registered firms; and (3) the Tribunal Superior Eleitoral (TSE) registry of all party members (19.3 million individuals) over 2002–2019. Matching these sources yields political affiliation for 11.4% of all private-sector owners and 7.8% of all private-sector workers in the sample. Party affiliation in Brazil requires an active registration step and is interpreted as a signal of strong and visible political views, distinguishing affiliated from unaffiliated individuals who likely hold milder views. The 35 parties in the sample are highly fragmented; the top 7 account for nearly 70% of all party members.

Main Findings

Political assortative matching. Using a likelihood ratio index (Eika et al., 2019; Chiappori et al., 2020), the paper finds that workers and owners belonging to the same party are on average about twice as likely to match in the labor market relative to random matching. Once within-municipality geographical sorting is accounted for, this figure falls to approximately 55% excess probability of copartisan matching, and increases over time: from 1.41 in 2002–2006 to 1.67 in 2016–2019. A dyadic regression approach — constructing all worker-firm dyads within industry-municipality labor markets and controlling for shared gender, race, age, and education — confirms the result: across all years, a politically affiliated worker is between 41% and 75% more likely to be employed by a copartisan owner than by an owner affiliated with a different party. Political assortative matching is driven both by higher hiring probabilities (range: 32%–59% more likely for copartisans, hiring margin only) and by longer tenure: copartisan workers stay in the firm roughly 5.5% longer than otherwise comparable workers of a different party, even within the same firm and hire-year (column 3 of Table 2). In every year and by every method, the degree of political assortative matching exceeds that of gender (15%–31% excess probability under dyadic approach) and race (approximately 3.4%), which are themselves both positive and significant.

Mechanisms: political discrimination. Three sets of evidence point to employer political discrimination as a relevant driver. First, in the administrative micro-data: assortative matching decreases strongly with firm size — it is more than twice as large in firms with up to 10 employees than in medium firms and more than six times as large as in firms with more than 50 employees — and is stronger for higher occupational layers and for jobs requiring above-median social skills or interpersonal relationships. Political assortative matching is, if anything, larger for parties not in power locally, inconsistent with a patronage mechanism. An event study of 5,262 owners who switched party finds a sharp increase of about 0.2 standard deviations in hires from the new party and a corresponding drop in hires from the old party at the time of the switch, with the share of workers from the new party rising by roughly 5 percentage points persistently. Second, an incentivized resume rating (IRR) field experiment (150 business owners; nondeceptive design) shows that owners rate copartisan resumes 0.213 points higher on a 1–7 Likert scale (a 7.4% increase relative to the mean rating for different-party resumes, statistically significant at p < 0.05), with no significant effect on perceived candidate acceptance probability. Third, a representative survey of 891 owners and 1,003 workers finds that belief-based and taste-based discrimination are ranked as the leading explanations by both groups; 47% of owners and 58% of workers agree with the belief-based discrimination statement. Additionally, 29% of surveyed owners (22% say “Yes” and 7% “In some cases”) explicitly reveal that political views affect their hiring decisions.

Real consequences. Conditional on employment, copartisan workers are promoted faster: they are 0.448 percentage points more likely to be promoted from white-collar to managerial positions (against a base rate of 2.58%) and 0.44 percentage points more likely to be promoted from blue-collar to white-collar positions (base rate 2.98%). Workers from a different party than the owner face a promotion penalty of 0.104–0.180 percentage points for white-collar-to-manager promotions. On wages, copartisan workers earn 3.9% more than unaffiliated coworkers within the same firm and year (firm-year FE specification); the effect is 2.8% when restricting to the same occupation within the firm. Workers from a different party earn 1.6% less. Decomposing by tier: managers (copartisan premium 1.6%), white-collar workers (3.4%), blue-collar workers (1.5%). Despite better outcomes, copartisan workers are 2.1 percentage points (2.3% relative to the mean) less likely to be educationally qualified for their occupation, conditional on firm-year and controlling for a full set of demographics. Finally, a higher share of copartisan workers in the prior year is associated with lower firm employment growth (estimated β = −0.071), corresponding to approximately a 1 percentage point gap in annual growth rate for a one-standard-deviation difference in copartisan share — substantial relative to an average annual growth rate of 10%.

Scope Conditions

All findings pertain to the formal private sector in Brazil over 2002–2019. Political affiliation in the Brazilian system requires an active step and signals strong views; results apply to the approximately 7.8%–11.4% of workers and owners who are party-registered. The field experiment sample is limited to 150 business owners affiliated with major Brazilian parties who were actively seeking to hire. The firm growth result is explicitly characterized as suggestive, without a source of exogenous variation.

In depth

Q1. What is the likelihood ratio index and what does it show for political matching in Brazil?

The likelihood ratio index measures how many times more likely a match between a worker and owner of the same party is, relative to the expected frequency under random matching (conditional on the population shares of each party). Across 2002–2019, the unconditional index ranges from 1.56 to 1.85, implying workers and employers of the same party are on average about twice as likely to match as under random matching. After accounting for geographic sorting within municipalities, the index ranges from approximately 1.41 (2002–2006 average) to 1.67 (2016–2019 average), showing a clear increasing trend. The corresponding gender and race indexes average about 1.2 and 1.35, respectively, in the basic specification, both significantly lower than the party index in every year of the sample.

Q2. How do the dyadic regression estimates control for omitted characteristics, and what do they find?

The dyadic regression constructs all possible worker-firm pairs within each municipality-industry labor market in a given year. The dependent variable is an indicator for whether worker i is employed by firm f. The key coefficient of interest is the differential probability of employment for a copartisan pair relative to a different-party pair, controlling for indicators for shared gender, race, age bracket, and education level, as well as worker occupation fixed effects and experience. This controls for the concern that politically affiliated individuals share non-political traits that correlate with employment choices. After these controls, a politically affiliated worker is 41%–75% more likely (depending on year) to be employed by a copartisan owner than by a different-party owner. The effect stems primarily from copartisan workers being preferentially hired (not just from unaffiliated owners preferring any affiliated worker indiscriminately). The analogous dyadic estimate for shared gender is 15%–31% and for shared race is approximately 3.4%, both lower than the party estimate in all years.

Q3. How is political assortative matching decomposed into hiring versus retention margins?

To isolate the hiring margin, the authors estimate the dyadic regression restricting to newly hired workers (not present in the firm in year t-1). They find that the probability of being hired by a copartisan owner is 32%–59% higher than by a different-party owner across years. The retention (tenure) margin is estimated by regressing the share of subsequent years a worker remains at the firm on partisan alignment at the time of hire. In the most stringent specification (year-of-hire × firm fixed effects), copartisan hires stay 5.5 percentage points longer (as a share of post-hire years) than different-party hires from the same firm and hire-year cohort. Both margins are significant, and both exhibit stronger political sorting than equivalent estimates for gender or race.

Q4. What is the evidence against political patronage as the primary driver of political assortative matching?

If political patronage (parties pressuring owners to hire copartisans) were the main driver, we would expect political assortative matching to be stronger when the owner’s party is in power locally, as those parties have greater leverage over business owners. The authors estimate a modified dyadic regression distinguishing between cases where the owner’s party is in the ruling coalition of the municipal mayor or state governor versus not in power. The results show that political assortative matching is, if anything, larger for parties not in power. This is inconsistent with patronage being the dominant mechanism and consistent with the discrimination channel being driven by owner preferences rather than external political pressure.

Q5. What does the event study of owner party changes show?

The event study tracks 5,262 owners who switch party affiliation during 2002–2019, comparing their firms to control firms in the same market whose owners remain affiliated to the original party. At the time of the switch, there is a sharp increase of approximately 0.2 standard deviations in hires from the owner’s new party and a corresponding sharp decrease in hires from the old party. Hires from other parties and unaffiliated hires also decline modestly. The share of the workforce affiliated with the new party increases by roughly 5 percentage points and remains elevated in subsequent years. Because nonpolitical network ties (shared school, neighborhood, sports team) are unlikely to dissolve abruptly when an owner changes party, this design provides additional evidence that the change in hiring is driven by a direct change in the owner’s political preferences rather than by network overlap.

Q6. What was the design of the incentivized resume rating experiment and why does it identify political discrimination?

The experiment was conducted with 150 Brazilian business owners recruited from the administrative data (who are already known to be affiliated with one of six major parties), targeting owners with active hiring interest through a leading job platform. Owners rated 20 synthetic resumes with fully randomized features (education, experience, training, skills, formatting). Sixteen resumes had no partisan cues; two contained cues signaling copartisanship with the rating owner; two signaled a party from the opposite side of the political spectrum. Incentives were provided by committing to send respondents real job-seeker profiles from the platform chosen by machine learning based on revealed preferences. Because all resume features other than the partisan cue were randomized, the experiment shuts down shared nonpolitical networks and patronage as explanations; the only channel is the employer’s direct preference for the candidate’s partisan affiliation. The response rate was 11% and the survey was conducted March–May 2022.

Q7. What is the quantitative magnitude of the field experiment result?

Owners rate copartisan resumes 0.213 points higher on the 1–7 Likert scale relative to resumes from the opposite side of the political spectrum (statistically significant at p < 0.05), representing a 7.4% increase relative to the mean rating of different-party resumes (2.950). When resume-level controls (gender, high-skill experience flag, years of experience, programming skills, training) are added, the estimate is 0.254. There is no statistically significant effect on owners’ perceived likelihood that a candidate would accept a job offer (coefficient 0.150–0.158, not significant), suggesting that the observed difference in interest ratings reflects a genuine direct preference for copartisans, not an expectation that copartisans are more likely to accept.

Q8. What do the survey findings add about mechanisms and the prevalence of political discrimination?

The survey of 891 owners and 1,003 workers (response rate 26.84%) presents five candidate mechanisms and asks respondents to evaluate each. Both groups rank belief-based discrimination (owners believe copartisans would be more productive) as the most likely explanation: 47% of owners and 58% of workers partially or strongly agree. Taste-based discrimination is second (36% owners, 52% workers agree), followed by networks (39% owners, 49% workers). Patronage and workers’ preferences attract little agreement from either group. Among owners ranked by single strongest agreement, 29.7% most strongly agree with belief-based discrimination and 22.0% with taste-based, while 29% of all surveyed owners explicitly stated that political views do affect their hiring decisions. These patterns are broadly similar regardless of the respondent’s own political affiliation status.

Q9. How large are the political promotion and wage premia, and how do they compare to gender and race effects?

For promotions, copartisan white-collar workers are 0.448 percentage points more likely to be promoted to manager (relative to unaffiliated co-workers hired in the same firm-year), against a base promotion rate of 2.58% — an effect of approximately 17% of the mean. For blue-collar-to-white-collar promotion, the copartisan premium is 0.44 percentage points against a base rate of 2.98%. For wages, copartisans earn 3.9% more than unaffiliated co-workers within the same firm and year; restricting to the same occupation within the firm, the premium is 2.8%. The political wage premium (3.9%) exceeds the gender wage premium (1.5%) and the race wage premium (1.0%) in the same specification. Workers from a different party than the owner earn 1.6% less than unaffiliated co-workers within the same firm-year.

Q10. Are copartisan workers better qualified than those they displace, and what does this imply for firm performance?

Copartisan workers are significantly less qualified in terms of education relative to their occupation: they are 2.1 percentage points less likely to be educationally qualified for their position than their unaffiliated co-workers within the same firm-year (2.3% relative to the mean qualification rate of 93.2%), with the largest effects for managers. Workers of a different party show only a small and economically negligible qualification gap. The fact that copartisans are paid more, promoted faster, and yet are less qualified is consistent with political discrimination substituting for competence in personnel decisions. The qualification shortfall is specifically attributed to copartisanship and not to shared gender, race, age, or education between owner and worker, as those coefficients are economically small.

Q11. What is the evidence on firm growth and what are the limitations of that evidence?

Firms with a higher share of copartisan workers in the prior year grow less. The estimated coefficient β = −0.071, and a one-standard-deviation difference in the copartisan share is associated with approximately a 1 percentage point gap in annual employment growth, relative to a mean growth rate of 10%. The specification compares firms of the same size and with the same number of affiliated workers in the same year. The result is robust to adding municipality and municipality-industry fixed effects. The authors explicitly characterize this evidence as suggestive, noting the absence of an exogenous source of variation in political discrimination. The negative association is more consistent with taste-based discrimination (Becker, 1957) — in which politically homogeneous firms sacrifice productivity for the owners’ amenity of employing copartisans — than with accurate belief-based discrimination.

Q12. How is political assortative matching distributed across parties and does it depend on party ideology?

The likelihood ratio index shows large assortative matching across the entire political spectrum. For most years, relatively more ideologically extreme parties — on the left (PT, PDT) and on the right (PP, DEM) — display higher assortative matching than more centrist parties (PMDB, PSDB). This pattern is consistent with stronger partisan identity at the extremes leading to stronger preferences for copartisan workers, but the paper does not formally model the mechanism behind this heterogeneity.

Q13. What is the role of workers’ preferences as opposed to employers’ discrimination, and how can wages distinguish them?

If workers have a preference for working with copartisan owners (treating this as a job amenity), compensating differentials theory would predict a negative wage premium for copartisan workers — they would accept lower wages in exchange for working with like-minded owners. The data show the opposite: copartisan workers earn significantly more, not less, than their unaffiliated co-workers. This evidence is inconsistent with workers’ preferences being the primary driver of political assortative matching, and is instead consistent with employers’ discrimination. The survey evidence corroborates this: both owners and workers assign low priority to the “workers’ preferences” mechanism.

Key Concepts

Political assortative matching: The phenomenon by which workers and business owners belonging to the same political party are matched in the labor market at rates significantly exceeding what would occur under random matching within the local labor market. Measured via the likelihood ratio index and dyadic regressions that control for shared demographic characteristics. In this paper, political assortative matching is larger in magnitude than assortative matching along gender or racial lines.

Likelihood ratio index (S): A measure of assortative matching defined as the weighted sum of the ratios of observed same-party co-occurrence probabilities to their expected probabilities under random matching. S > 1 indicates positive assortative matching. The paper uses both a basic version and a geography-adjusted version that computes the index within municipalities to control for geographic concentration of party membership.

Dyadic regression: A regression approach that constructs all possible worker-firm pairs within a defined labor market (municipality × 2-digit industry) to estimate the differential probability that a worker is employed by a copartisan firm relative to a different-party firm. The key advantage is the ability to control simultaneously for multiple shared demographic characteristics between worker and owner, accounting for the correlation of assortative criteria.

Incentivized resume rating (IRR) experiment: A nondeceptive field experiment design (following Kessler et al., 2019) in which business owners rate synthetic resumes with fully randomized characteristics. Truthful rating is incentivized because respondents are told that their revealed preferences will be used to select real job-seeker profiles sent to them by a partner platform via machine learning. This design allows direct identification of employer preference for copartisan candidates while ruling out alternative channels such as shared nonpolitical networks or patronage.

Political wage premium: The percentage wage difference earned by copartisan workers relative to unaffiliated co-workers within the same firm-year (and occupation), after controlling for a full set of socio-demographic characteristics. A positive political wage premium is the paper’s primary piece of evidence that workers’ compensating differentials cannot explain political assortative matching, since amenity-based sorting would predict a negative premium.

Political promotion premium: The differential probability that a copartisan worker is promoted to a higher organizational layer (blue-collar to white-collar, or white-collar to manager) relative to an unaffiliated co-worker hired in the same firm and year, net of demographic controls.

Educational mismatch (Qualified): An indicator variable equal to one if a worker’s educational level meets or exceeds the educational level required by their specific occupation in the CBO (Classificação Brasileira de Ocupações) classification. Used to assess whether politically favored (copartisan) workers are less competent along this observable dimension.

Belief-based discrimination vs. taste-based discrimination: Two distinct theoretical channels for employer political discrimination. Belief-based discrimination (Phelps, 1972; Arrow, 1973) occurs when employers perceive copartisans to be more productive — e.g., because shared political views reduce intra-firm conflict. Taste-based discrimination (Becker, 1971) occurs when employers have a direct utility-affecting preference for copartisan workers, independent of productivity beliefs. The paper treats these as observationally distinct from patronage and network overlap, and uses the negative correlation between political homogeneity and firm growth as suggestive evidence favoring the taste-based channel.

State Capacity as an Organizational Problem

Mon, 01 Jan 0001 00:00:00 +0000

Mastrorocco and Teso study how the internal organization of a state evolves during national development, framing state capacity as an organizational — specifically a principal-agent — problem. Using a new micro-database covering the U.S. federal bureaucracy from 1817 to 1905, they ask: once rulers have incentives to build a state apparatus, how do they organize it to perform its functions across a vast territory, and what drives transitions between organizational forms?

The dataset is constructed from every issue of the Official Register of the United States published between 1817 and 1905 (44 biennial volumes, 15,801 pages digitized). It records full name, state of birth, state of appointment, occupation, salary, department, office, and location for 304,410 unique federal employees across 810,942 employee-year observations. The authors reconstruct the bureaucracy’s four-layer hierarchy (department → office/bureau → division → local office), link employees over time to track careers, categorize all 11,930 occupation codes into five tiers, and geo-code 9,651 places of employment to 1890 county boundaries.

The paper first documents three sets of descriptive facts. On growth: the federal workforce expanded very slowly before the 1860s and then rapidly, with geographic expansion accounting for none of state growth before 1859 but roughly 29% after. On location: state presence responded positively to local manufacturing activity (a one standard deviation increase in manufacturing employment share raises presence probability by 1.3 percentage points), but distance from Washington DC significantly attenuated this relationship in 1817–1859 and not in 1861–1905. On organization: before the 1860s, employee turnover was high and spiked sharply at presidential transitions (reaching 72% of employees departing in 1861), supervisors’ departures strongly predicted subordinates’ departures (a one-for-one supervisor exit raised subordinate turnover probability by 37% pre-1841), and managerial delegation outside DC was stagnant or declining. After the 1860s, turnover trended down (35% at the 1897 transition), the supervisor-subordinate career link weakened materially, and field managers tripled relative to the 1850s.

The authors argue that high monitoring costs in the early century made trust-based, personalistic organization the second-best solution to principal-agent problems. The limited supply of sufficiently trusted individuals constrained geographic expansion, delegation, and total size. As railroad and telegraph networks lowered communication and transportation costs, monitoring capacity increased, enabling a transition to a Weberian bureaucracy no longer constrained by trust supply.

The causal identification strategy uses the staggered expansion of the railroad network. For each county and decade (1820–1900), the authors compute the minimum-travel-time route from the county centroid to DC using Donaldson and Hornbeck (2016) data on railroads, steamboat waterways, coastal routes, and land routes. The specification includes county fixed effects, state-by-decade fixed effects, and controls for local railroad presence in the county and for the county’s market access, so the identifying variation comes from distant changes in the network that altered travel time to DC without directly affecting the county’s local economy or trade access.

Results: a one standard deviation decrease in travel time to DC raises the probability of federal state presence by approximately 3 percentage points (about 8% of the mean), raises log employment similarly, raises the probability of observing a local managerial layer by approximately 3 percentage points (about 8% of the mean), and reduces employee turnover by approximately 2 percentage points (about 4% of the mean turnover rate). Placebo tests confirm that travel time to other major economic centers does not predict state presence. Telegraph network data (1845–1852, Wang 2020) yield consistent results. An additional test using the post-Civil War decline in Southern-born employee shares shows that better railroad connection to DC narrowed the North-South employment gap, consistent with monitoring substituting for trust-based selection.

Scope conditions: the paper covers the civilian executive branch of the federal government, excluding the Postal Office, navy yards, and the engineer department; results are robust to restricting to states already in the union at the start of the sample, ruling out frontier-specific dynamics.

Q: What is the central theoretical claim of the paper? A: The paper argues that state capacity is fundamentally an organizational problem shaped by principal-agent constraints. When communication and transportation costs are high, the government cannot effectively monitor distant agents, so the second-best solution is to staff the bureaucracy with trusted individuals connected through personal networks. This personalistic form limits size and delegation because the supply of sufficiently trusted individuals is inherently scarce. Technological reductions in monitoring costs allow a transition to a Weberian bureaucracy based on procedural oversight rather than trust, removing the supply constraint on organizational growth.

Q: What data source does the study rely on, and what time period does it cover? A: The study draws on the Official Register of the United States, a biennial government publication listing all federal employees, digitized for every issue from 1817 to 1905. The resulting dataset includes 304,410 unique employees and 810,942 employee-year observations, with each record carrying name, state of birth, state of appointment, occupation, salary, department, office, location, and — through hierarchical reconstruction — position in a four-layer chain of command.

Q: How did the size of the U.S. federal bureaucracy evolve over the nineteenth century? A: Growth was slow before the 1860s. The first Register for 1817 listed 1,056 employees across 33 pages; the 1905 volume listed over 120,000 employees across 1,254 pages. Geographic expansion contributed zero to state growth before 1859 — the share of counties with any federal employee hovered around 15% from 1817 to 1859 — but contributed approximately 29% of growth after 1859, when county presence rose to 24% by 1871, 38% by 1881, and 61% by 1905.

Q: What were the three sources of state growth, and how did their relative importance change? A: The authors decompose growth into: (1) functions (new offices/bureaus), (2) geographic expansion (new counties), and (3) intensity (more employees per county-office pair). Before 1859, growth was entirely driven by functions (~40%) and intensity (~60%), with zero contribution from geographic expansion. After 1859, geographic expansion accounted for ~29%, intensity for ~32%, and functions for ~39% of growth.

Q: How did employee turnover behave across the century, and what pattern emerges at presidential transitions? A: Turnover trended upward through the late 1850s and then declined. During presidential transitions, the rate rose from 52–53% in 1841 and 1845 to 60–63% in 1849 and 1853 and peaked at 72% in 1861; it then fell to 55% in 1869, 44–48% in 1885/1889/1893, and 35% in 1897. Turnover was consistently lower in DC than in the field: controlling for year-bureau-position fixed effects, being employed in DC was associated with a 40% reduction in turnover probability.

Q: How tight was the link between supervisors’ and subordinates’ careers, and how did it change? A: Before 1841, moving from none to all supervisors leaving an organizational unit increased subordinate turnover probability by 37 percentage points. The effect was similar between 1841 and 1859, then dropped substantially to 22 percentage points in the following twenty-year period, and remained roughly constant after 1881. This pattern is consistent with the early bureaucracy relying on chains of personal trust that broke when a supervisor departed.

Q: What evidence describes the evolution of delegation outside DC? A: The number of field managers did not grow between 1817 and 1859 — it actually declined in the 1820s and was flat through the mid-1850s — and then tripled by 1905 relative to the 1850s level. The probability that workers in a local office had an additional managerial layer between them and DC was unchanged between pre-1841 and 1841–1859, increased by 5 percentage points between 1861 and 1881, and by 6 percentage points post-1881.

Q: How does the paper measure monitoring capacity for the causal analysis? A: The primary measure is travel time in hours from each county centroid to Washington DC, computed decade by decade (1820–1900) as the minimum-cost route across the available railroad network, steamboat waterways, coastal routes, and land routes, using data from Donaldson and Hornbeck (2016). A second, complementary measure is the number of telegraph connections between a county and DC using data from Wang (2020) for 1845–1852.

Q: What is the identification strategy for the railroad analysis, and why are controls for local railroads and market access important? A: The specification includes county fixed effects, state-by-decade fixed effects, an indicator for whether the county itself has railroad (LocalRailroad), and the county’s market access. County fixed effects mean beta is identified within-county from changes over time. Controlling for local railroad removes the direct correlation between local construction and local economic growth. Controlling for market access removes the effect of distant rail expansion on trade flows that raised agricultural land values and manufacturing activity. The remaining variation in travel time to DC — coming from distant network changes that altered the DC-county connection without affecting local conditions or broader trade access — is the identifying source.

Q: What are the main quantitative effects of reduced travel time to DC? A: A one standard deviation decrease in travel time to DC is associated with: (1) approximately 3 percentage point increase in the probability of federal state presence (~8% of the mean); (2) a similar magnitude increase in log employment conditional on presence; (3) approximately 3 percentage point higher probability of an additional managerial layer (~8% of the mean); and (4) approximately 2 percentage point reduction in employee turnover (~4% of the mean turnover rate).

Q: How do placebo tests support the monitoring interpretation? A: The authors show that, conditional on the same controls, travel times from a county to a set of other major economic centers are not associated with larger federal state presence. Since these other cities had no role as monitoring headquarters, the absence of an effect for them and the presence of an effect specifically for DC is consistent with the channel operating through the government’s ability to supervise agents from the capital, rather than through generic economic connectivity.

Q: What does the telegraph evidence add, and what is its limitation? A: Telegraph data (1845–1852, Wang 2020) show that counties with more telegraph connections to DC have larger state presence, more managerial delegation, and lower turnover, consistent with the monitoring mechanism. The limitation is that the authors have limited ability to address the endogeneity of telegraph network timing — the telegraph analysis is treated as corroborating evidence rather than the primary causal identification.

Q: How do the Southern-born employee results illuminate the trust mechanism? A: After the Civil War, the share of Southern-born federal bureaucrats fell sharply, consistent with reduced trust toward individuals from former Confederate states. However, counties that became better connected to DC via railroad expansion experienced a relative increase in the share of Southern-born employees. This shows that when monitoring costs fell, the government was willing to hire individuals from groups with lower baseline trust — monitoring substituted for trust as the mechanism ensuring agent performance.

Q: Does federal state presence crowd out state and local government? A: No. The presence of federal bureaucrats is positively correlated with the presence of state and local government employees at the county level, suggesting complementarity rather than substitution across levels of government.

Q: What alternative mechanisms do the authors consider and how do they address them? A: Three alternatives are discussed. First, demand shocks (Civil War debt repayment, industrialization) could explain the post-1860s expansion; the empirical specifications control for year fixed effects to absorb aggregate time-varying incentives, and the identification relies on differential cross-county variation in DC connectivity. Second, patronage as an electoral tool is consistent with spoils-driven turnover spikes but cannot explain why better-connected counties show lower turnover before civil service reform. Third, cognitive models of the firm (lower communication costs complement managerial problem-solving even without agency problems) could also predict the positive delegation result; the authors note they cannot empirically distinguish the monitoring and cognitive channels, and both may contribute.

Q: What are the implications for developing countries today? A: The authors suggest that their findings from nineteenth-century U.S. history may apply to understanding why modern Weberian bureaucracies remain elusive in many developing countries. Where communication infrastructure is limited and monitoring costs remain high, personalistic organizational forms based on trust networks may persist as constrained optima — not failures of will or design, but rational responses to structural conditions. Infrastructure investment that lowers monitoring costs could be a precondition for bureaucratic modernization.

Personalistic state organization: The paper’s term for the organizational form that prevails when monitoring costs are high. It is characterized by staffing decisions based on personal character, moral reputation, and relationships of trust between principals and agents — and between supervisors and subordinates — rather than on formal procedural monitoring of performance. Frequent turnover at leadership transitions and constrained delegation are defining features, because the supply of trusted individuals is limited.

Weberian bureaucracy: In the paper’s usage (following Weber 1978), a modern state organization defined by a fixed hierarchy of officials monitored through procedural rules rather than personal trust, lower turnover, and effective delegation of managerial power to geographically dispersed units. The paper treats this as the organizational form enabled by low monitoring costs.

Monitoring capacity: The principal’s (politicians in DC and their cabinets) ability to observe and evaluate the behavior of agents (federal employees) throughout the territory. In the paper’s operationalization, monitoring capacity is proxied inversely by travel time and communication cost between DC and the county: lower travel time and more telegraph connections mean higher monitoring capacity.

Geographic expansion component: One of three decomposed sources of state growth. Defined as the increase in state size attributable to the state becoming present in more county locations. This component contributed zero to federal growth before 1859 and approximately 29% of growth after 1859.

Employee turnover: In the paper’s measurement, the share of employees who leave the federal bureaucracy in a given year. The paper distinguishes politically-driven spikes at presidential transitions — reaching 72% of employees in 1861 — from the secular trend, which rose through the late 1850s and then declined, reaching 35% by the 1897 transition.

Delegation of managerial power: The probability that a local county office has an additional managerial layer between its workers and DC, rather than reporting directly to the bureau-level supervisor in Washington. The paper uses this as its measure of whether decision authority has been decentralized to the field.

Trust substitution: The paper’s mechanism linking monitoring capacity to organizational form. In the absence of effective monitoring, principals substitute trust for oversight — selecting agents whose personal loyalty, moral character, or political alignment gives the principal confidence they will not shirk or defect. As monitoring costs fall, trust becomes less necessary as a screening device, and the trust-constrained supply limit on organizational growth is relaxed.