D72 | Macro Paper Warehouse

Ideological Alignment and Evidence-Based Policy Adoption

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

This paper investigates how the ideological alignment between knowledge-disseminating institutions and policymakers affects the adoption of evidence-based policies. The core research question is whether, and through which mechanisms, the ideology of the messenger — rather than the content of the message — determines whether local policymakers act on rigorous research evidence.

The authors conduct a country-wide randomized controlled trial (RCT) across 5,678 touristic Spanish municipalities. The policy recommendation derives from Hinnosaar et al. (2021), an RCT demonstrating that minor improvements to municipalities’ Wikipedia pages (adding photographs, local festival information, touristic landmark details) increased overnight tourist stays by 9%. This policy was chosen because it is ideologically neutral, low cost, within local policymakers’ remit, and its implementation is directly traceable via Wikipedia edit histories.

Municipalities were randomized into five treatment arms and a control group (approximately 950 municipalities each), stratified by ruling party ideology, population, and touristic accommodation count. Three arms received the same policy brief endorsed by: (1) an ideologically aligned think tank (FAES for right-wing municipalities, Fundación Alternativas for left-wing), (2) the ideologically opposite think tank, or (3) an ideologically nonsalient researcher from the London School of Economics. Two further arms received links to newspaper articles covering the same research from either an ideologically aligned outlet (El Mundo for right, Eldiario.es for left) or an ideologically opposite outlet. The control group received no information. The experiment ran from May to December 2022, with multiple reminder emails sent across the period.

The main outcome is a binary indicator for whether a municipality’s Wikipedia page was changed in line with the recommended guidelines during the study period, coded blind to treatment status by two independent coders.

Key findings: Pooled across all treatment arms, information provision increased the probability of policy adoption by approximately 0.98 percentage points (a 38% relative increase over the control group baseline), but this effect is only marginally above conventional significance thresholds (p-value = 0.13). The aggregate effect masks sharp heterogeneity by ideological alignment. When the informing institution’s ideology aligns with the policymaker’s, policy adoption increases by 1.68 percentage points (think tank) and 1.67 percentage points (newspaper) relative to the control group — equivalent to a 66% and 65% relative increase, respectively, both statistically significant at the 5% level. By contrast, information from an ideologically opposite institution produces a coefficient that is negligible and statistically indistinguishable from zero, indicating that misaligned information is no more effective than receiving no information at all. The ideologically nonsalient LSE researcher arm produced an intermediate effect (0.94 percentage points, 37% relative increase), but the p-value (0.27) exceeds conventional thresholds, and the effect is not statistically distinguishable from either the aligned or the control condition. Policy briefs and newspaper articles are equally effective when ideologically aligned (difference of 0.1 percentage points, p-value = 0.82).

To decompose mechanisms, the authors propose a three-stage framework: (1) selective exposure to information, (2) belief updating, and (3) policy implementation. Email click-through rates (access to the full policy brief or article once the informing institution is revealed) do not differ significantly across treatment arms, ruling out selective exposure as the operative mechanism. A post-intervention online survey experiment with 1,600 policymakers from 1,196 municipalities shows that those receiving information from an aligned or nonsalient institution updated their beliefs about policy effectiveness significantly more than those receiving information from an opposite institution, implicating belief updating as one operative channel. However, comparing the survey experiment (where nonsalient and aligned treatments produce similar belief updating) with the main experiment (where the aligned arm adopts at nearly twice the rate of the nonsalient arm, though not statistically distinguishable) suggests that ideological alignment also affects the third stage — policy implementation — beyond mere belief updating.

The estimated monetary cost of ideological misalignment is 2,192 euros per municipality per year, calculated using the impact of Wikipedia changes on touristic revenues from Hinnosaar et al. (2021).

Scope conditions: The context is Spanish local government, a policy that is explicitly non-ideological, low-cost, and easily implemented. Generalizability to ideologically charged or costly policies is not established. Left-wing municipalities show larger responses to aligned information, though this heterogeneity is not statistically significant at conventional levels.

Q: What is the baseline rate of policy adoption in the control group, and what does the aligned-institution treatment achieve in absolute terms?

A: The paper reports that ideologically aligned institutions increase the share of municipalities implementing recommended Wikipedia changes by 1.68 percentage points (think tank) and 1.67 percentage points (newspaper) relative to the control group. Working backward from the stated 66% and 65% relative increases, this implies a control group baseline of approximately 2.5 percentage points. The aligned effects are statistically significant at the 5% level.

Q: Does information from an ideologically opposite institution have any effect on policy adoption?

A: No. The coefficient for opposite-ideology treatment arms is negligible in magnitude, closely resembling the near-zero coefficients from the placebo analysis conducted for the same months in 2019 (pre-intervention). The authors conclude that receiving information from an ideologically opposite institution is statistically indistinguishable from receiving no information at all. This null result is consistent across heterogeneity analyses by mayor ideology, municipality population, Wikipedia page length, and party type.

Q: How does the ideologically nonsalient (LSE researcher) treatment compare to aligned and opposite arms?

A: The nonsalient arm increases policy adoption by 0.94 percentage points (a 37% relative increase), approximately half the effect of the aligned arm (1.68 percentage points). However, the p-value is 0.27, and the effect is not statistically different from either the aligned arm (p-value = 0.34) or the control group at conventional confidence levels. The result should therefore be interpreted with caution.

Q: Are policy briefs or newspaper articles more effective in promoting policy adoption?

A: Neither format is significantly more effective than the other. Conditional on ideological alignment, the difference between policy brief and newspaper article effects is 0.1 percentage points with a p-value of 0.82. Both are equally effective when ideologically aligned with the receiving policymaker, a finding the authors describe as a novel contribution to the policy communication literature.

Q: Does ideological alignment affect whether policymakers choose to access the full information (selective exposure)?

A: No. Click-through rates on the links to policy briefs or newspaper articles — measured after policymakers have seen the informing institution’s identity — do not differ significantly across treatment arms. The observed average click-through rate is 6.42%. This null result is consistent with the hypothesis that policymakers do not strategically filter information acquisition based on the messenger’s ideology, at least for non-ideological policies.

Q: What does the survey experiment reveal about belief updating?

A: In the post-intervention survey experiment with 1,600 policymakers, participants first reported beliefs about a purportedly beneficial (but actually harmful) policy, then were randomly assigned to receive information about its negative effects from an aligned, opposite, or nonsalient think tank. Those receiving information from an aligned or nonsalient institution updated their beliefs significantly more than those receiving information from an ideologically opposite institution. This implicates belief updating — not just selective exposure — as a channel through which ideological alignment affects policy adoption.

Q: Why do the authors conclude that ideological alignment also affects the third stage (policy implementation) beyond belief updating?

A: In the survey experiment, aligned and nonsalient institutions produce statistically similar belief updating. Yet in the main field experiment, the aligned arm adopts policy at nearly twice the rate of the nonsalient arm (1.68 vs. 0.94 percentage points), although this difference is not statistically significant. The authors interpret this gap as suggestive evidence that ideological alignment affects policy implementation through channels beyond belief updating — such as career concerns, party cues, or the political economy of implementation — though they acknowledge the evidence is indirect and the treatment difference is not statistically distinguishable.

Q: What is the estimated economic cost of ideological misalignment?

A: The authors estimate a cost of 2,192 euros per municipality per year attributable to ideological misalignment between the informing institution and the receiving policymaker. This calculation uses the estimated impact of Wikipedia changes on touristic revenues from Hinnosaar et al. (2021) and reflects not the cost of not implementing the policy, but the marginal cost of using an ideologically opposite rather than aligned institution to disseminate the research evidence.

Q: How did outside researchers’ predictions compare to actual results?

A: Researchers surveyed on the Social Science Prediction Platform correctly anticipated the rank ordering of treatment effectiveness (aligned > nonsalient > opposite > control) but substantially overestimated adoption rates in every arm. They predicted relative increases of 144%, 103%, and 48% for aligned, nonsalient, and opposite conditions respectively, compared to actual relative increases of roughly 65%, 37%, and ~0%. Email opening rates were the most accurately predicted (49% predicted vs. 38% actual). The results highlight the difficulty of translating evidence into policy even for simple, low-cost interventions.

Q: What are the main threats to validity and how are they addressed?

A: Three main threats are considered. First, differential email opening rates across treatment arms: addressed by showing the informing institution was revealed only after email opening, and confirmed by finding no significant differences in opening rates across groups. Second, spillovers between municipalities: the endline survey shows only 5 of 236 control-group respondents reported receiving any information from external sources; spillover distance analyses in Table D.II find no significant effect on control municipalities’ adoption rates. Third, contamination bias in multi-arm RCTs with strata fixed effects: addressed by replicating main results using the Goldsmith-Pinkham et al. (2022) method, yielding nearly identical estimates.

Q: What heterogeneity is observed across left- and right-wing municipalities?

A: The positive effect of receiving information from an ideologically aligned institution appears larger for left-wing municipalities, with coefficients approximately three times larger than for right-wing municipalities, but this difference is not statistically significant at conventional confidence levels. The authors caution that the strength of ideological alignment may differ systematically between the partner think tanks on the left and right, making direct comparisons between left- and right-wing effects difficult to interpret cleanly.

Q: How does the paper relate to prior work on evidence-based policymaking?

A: The closest prior work is Hjort et al. (2021) and Mehmood et al. (2024), which examine the impact of scientific evidence access on actual policy adoption, and DellaVigna and Kim (2022), which identifies ideology as a factor in the diffusion of innovative policies across governments. The present paper’s main contribution is being the first to isolate the causal effect of ideological alignment on policy adoption using a large-scale field experiment with real, authoritative ideological institutions — rather than surveys or hypothetical scenarios — while using a non-ideological policy recommendation to avoid confounding messenger ideology with policy ideology.

Ideological alignment: In this paper’s usage, the congruence between the political ideology of the institution disseminating research evidence (think tank or newspaper) and the political ideology of the local government receiving that information. Alignment is operationalized by matching right-wing municipalities with right-leaning institutions (FAES, El Mundo) and left-wing municipalities with left-leaning institutions (Fundación Alternativas, Eldiario.es).

Evidence-based policy adoption: The actual implementation by local policymakers of a policy recommendation derived from published peer-reviewed research — measured here as whether a municipality’s Wikipedia page was edited in line with specific recommended guidelines during the study period, not merely expressed intention or stated support.

Knowledge brokers: Institutions, such as think tanks, that serve as intermediaries between academic researchers and policymakers, translating and disseminating research findings in accessible formats (policy briefs) to bridge the gap between evidence and policy.

Nonsalient ideology: A condition in which the informing institution carries no salient or recognizable partisan affiliation, operationalized here by a foreign research university professor (LSE) whose institutional identity does not carry a clear left-right signal in the Spanish political context.

Three-stage policy adoption framework: The authors’ conceptual structure positing that ideology can interfere at three sequential stages: (1) selective exposure — whether policymakers choose to access information once the messenger’s ideology is revealed; (2) belief updating — whether policymakers revise their assessment of a policy’s effectiveness upon receiving evidence; and (3) policy implementation — whether policymakers act on updated beliefs to adopt the policy.

Selective exposure: The tendency of individuals to avoid information from sources whose ideology conflicts with their own prior beliefs; in this paper, operationalized as differential click-through rates on links to policy briefs or news articles after the informing institution’s identity is revealed.

Motivated reasoning: A documented tendency, also observed in policymakers, to reject or discount evidence that contradicts ideologically held prior beliefs — the mechanism proposed to explain why opposite-ideology information fails to update beliefs as effectively as aligned-ideology information.

Open Rule Legislative Bargaining

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

This paper revisits the open rule legislative bargaining model of Baron and Ferejohn (1989) — the dominant workhorse model in political economy for analyzing how legislatures divide a surplus — and provides a more complete characterization of its stationary equilibria. The core research question is whether the equilibrium typically cited in the literature as the “open rule equilibrium” is actually the unique equilibrium, or whether it rests on implicit and unstated assumptions that, once relaxed, reveal a much richer equilibrium set.

The model features n=3 negotiators dividing a surplus normalized to one, operating under simple majority rule (2 of 3 votes required). The common discount factor is Delta in (0,1). In each period, a proposer is selected uniformly at random; under the open rule, an amender is then selected uniformly at random from the two non-proposers and may either accept or counter-propose. Sincere voting determines the outcome. The authors analyze stationary subgame perfect equilibria (SSPE), in which strategies depend only on current role, not history.

The existing literature implicitly adopted what the authors call the “standard assumption”: when given the opportunity to amend, the amender proposes the same allocation she would propose as a proposer in a closed rule game. Under this assumption, the unique SSPE has the proposer receiving share 1-Delta and each of the other two negotiators receiving Delta/2 (in the Pareto-efficient equilibrium). The literature treated this as the definitive open rule solution.

The paper’s first main result is that this standard-assumption equilibrium is indeed a valid SSPE, but it is not the only one. The key mechanism generating multiplicity is the treatment of off-path behavior: what the amender does when the proposer deviates to a non-equilibrium proposal. With n=3, a deviating proposer can exploit the structure so that the amender becomes a “free” coalition member — the proposer does not need to buy the amender’s vote separately, because the amender is already included in the majority once she counter-proposes. This expands the set of credible threats and supports a continuum of additional Pareto-undominated SSPEs.

The paper’s second main result characterizes the broader equilibrium set: all Pareto-undominated SSPEs belong to a class in which the proposer offers (1-Delta) to herself and equal shares to both other negotiators. In the non-standard equilibria, the amender always amends, generating equilibrium delay — agreements are not reached immediately, and payoffs are discounted by Delta^(t-1) for each period of delay.

The third main result is that among all Pareto-undominated SSPEs, the unique Pareto-efficient one is the standard-assumption equilibrium (no delay). All other equilibria involve delay and are therefore Pareto-inferior in expectation.

The institutional design implication reverses a widely held view: the open rule was thought to promote more egalitarian allocations relative to the closed rule. The authors show this is not the case for Pareto-efficient equilibria. The Pareto-efficient open rule equilibrium is actually a special case of the closed rule equilibrium — the proposer captures 1-Delta and offers Delta to the coalition. More broadly, open rule bargaining tends to generate longer equilibrium delays and less egalitarian surplus allocations than previously predicted by Baron and Ferejohn. Scope conditions: the formal analysis is restricted to n=3 negotiators; generalization to larger legislatures is noted as an open direction.

Q: What is the “standard assumption” and why does the existing literature rely on it?

A: The standard assumption holds that when an amender gets the opportunity to counter-propose, she proposes the same allocation she would choose if she were the proposer in a closed rule game. The existing open rule literature — including Baron and Ferejohn (1989), Jackson and Morelli (2004), Baron (2012), van Weelden (2013), and Austen-Smith and Banks (1999) — accepted this assumption implicitly, treating the resulting equilibrium as the unique open rule equilibrium. The assumption sidesteps the question of off-path behavior: what happens when the proposer deviates to a non-equilibrium proposal that the amender would want to amend. Because deviations are resolved within the same bargaining session under the open rule, off-path specifications are consequential.

Q: What is the unique SSPE under the standard assumption, and what are its payoff implications?

A: Under the standard assumption with n=3 and discount factor Delta, the unique SSPE has the proposer receiving a share of 1-Delta of the surplus and each of the other two negotiators receiving Delta/2. There is no delay: the proposal passes immediately in the period it is made. This equilibrium is Pareto-efficient relative to all other stationary equilibria identified in the paper.

Q: What is the mechanism by which the equilibrium set is larger than the standard assumption predicts?

A: With n=3, when a proposer deviates to a non-equilibrium proposal, the amender — who responds by counter-proposing — automatically becomes part of the passing coalition without the proposer needing to separately compensate her. This makes the amender a “free” coalition member in the deviation subgame, which changes the cost structure of deviations and expands the range of proposals the proposer can credibly make. Consequently, a wider set of strategies by the amender can be sustained as equilibrium responses, yielding a continuum of additional Pareto-undominated SSPEs beyond the standard-assumption equilibrium.

Q: What do the non-standard equilibria look like in terms of proposals, delay, and payoffs?

A: In the non-standard Pareto-undominated SSPEs, the proposer offers (1-Delta) to herself and equal shares (Delta/2 each) to the other two negotiators — note the proposer’s own share is the same as in the standard equilibrium, but the off-path behavior differs — and the amender always chooses to amend rather than accept. The amendment triggers a vote in which the amendment fails (or the process repeats), pushing resolution to the next period. This generates equilibrium delay: agreements take multiple periods to reach, and all payoffs are discounted by Delta^(t-1) per period of delay, making these equilibria Pareto-inferior to the no-delay equilibrium.

Q: Which equilibrium is Pareto-efficient among all Pareto-undominated SSPEs, and why?

A: The unique Pareto-efficient SSPE is the standard-assumption equilibrium, because it is the only one that involves no delay. All other Pareto-undominated SSPEs involve at least one period of delay, which destroys surplus through discounting (payoffs shrink by a factor of Delta per period). Since delay is costly for all negotiators and generates no compensating redistribution, any equilibrium with delay is Pareto-dominated by the no-delay equilibrium.

Q: What are the implications for the classic efficiency comparison between open and closed rules?

A: The closed rule always generates an efficient outcome (no delay in SSPE). The open rule can also generate an efficient outcome — under the standard-assumption equilibrium — but uniquely admits a continuum of inefficient equilibria involving delay. Therefore the open rule is weakly dominated by the closed rule from an efficiency standpoint: at best it matches the closed rule (one efficient equilibrium), and at worst it generates costly delay. This reverses the common inference that open rule unambiguously improves outcomes.

Q: What are the implications for the classic fairness comparison between open and closed rules?

A: The open rule was commonly believed to promote more egalitarian surplus divisions relative to the closed rule, which allows the proposer to extract a large share. The paper shows this view is misleading. In the Pareto-efficient open rule equilibrium, the proposer still captures 1-Delta — the same as under the closed rule — and the result is no more egalitarian. In the delay equilibria, the proposer does offer equal shares to both other negotiators, but this comes at the cost of inefficiency (delay). There is no Pareto-undominated open rule equilibrium that is both efficient and more egalitarian than the closed rule.

Q: What is the class of “Pareto-undominated stationary strategies” and why does the paper focus on it?

A: A stationary strategy profile is Pareto-undominated if no other stationary strategy profile gives every negotiator at least as high an expected payoff with at least one strictly better off. The paper focuses on this class to provide a tractable but principled selection criterion within the large set of SSPEs: it eliminates equilibria that are dominated from every player’s perspective, retaining only those that could plausibly arise if players coordinate on mutually beneficial outcomes. The characterization of this class reveals that equilibrium multiplicity is already substantial even after imposing this selection.

Q: What is the scope of the formal results, and what is left open?

A: The formal analysis is restricted to n=3 negotiators with simple majority rule (2 of 3 votes). The authors acknowledge that generalization to larger n is an important open question. The three-legislator case is the simplest non-trivial instance of the majority-rule bargaining problem, and the authors use it to isolate the mechanism cleanly. The model assumes sincere voting, a common discount factor Delta in (0,1), and stationary strategies.

Q: How does this paper relate to Baron and Ferejohn (1989)?

A: Baron and Ferejohn (1989) originated both the closed rule and open rule bargaining frameworks and derived the standard-assumption equilibrium for the open rule. Subsequent literature (Eraslan 2002, Cho and Duggan 2003, 2009, Banks and Duggan 2000) extended various aspects of the B&F framework. The present paper takes the B&F open rule model as given but demonstrates that B&F’s open rule analysis was incomplete: it did not systematically address off-path behavior, and as a result the equilibrium it identified is not unique. The paper’s main contribution is to show that the B&F open rule predictions — more egalitarian allocations and prompt agreement — do not hold generally across the full equilibrium set.

Open Rule: A bargaining protocol in which, after an initial proposal is made, a nominated amender may make a counter-proposal before a vote is taken; contrasted with the closed rule, under which the initial proposal is voted on without amendment.

Closed Rule: A bargaining protocol in which a vote is taken directly on the first proposal, with no opportunity for amendment.

Standard Assumption: The implicit assumption, used by Baron and Ferejohn (1989) and subsequent literature, that when the amender counter-proposes under the open rule, she proposes the same allocation she would choose as a proposer in a closed rule game; the paper shows this assumption is consequential for equilibrium uniqueness.

Stationary Subgame Perfect Equilibrium (SSPE): An equilibrium concept in which each player’s strategy depends only on her current role (proposer, amender, or voter) and not on the history of play; the paper characterizes SSPEs of the open rule model.

Pareto-Undominated Stationary Strategy Profile: A stationary strategy profile for which no other stationary strategy profile gives every negotiator weakly higher expected payoff with at least one strictly higher; used as a selection criterion to prune the large equilibrium set.

Equilibrium Delay: The phenomenon in which agreement is not reached in the current period because the amender always counter-proposes and the counter-proposal also fails, pushing resolution to a future period and discounting payoffs; all non-standard-assumption Pareto-undominated SSPEs involve delay.

Off-Path Behavior: The specification of what strategies players use following a deviation from equilibrium play; the paper shows that different specifications of off-path behavior by the amender support different equilibria, and that the existing literature was not systematic about this.

Political Pressure on the Fed

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

This paper combines a hand-collected archival data set of over 800 personal interactions between U.S. Presidents and Federal Reserve officials from 1933 to 2016 with a narrative structural VAR to identify shocks to political pressure on the Fed and quantify their macroeconomic effects. The identification strategy exploits the well-documented Nixon-Burns episode of 1971—corroborated by Nixon Tapes recordings and Burns’s personal diary—as a narrative restriction that the spike in personal interactions that year was driven primarily by a political pressure shock rather than by economic conditions. Political pressure shocks are found to (i) increase inflation strongly and persistently, (ii) lead to statistically weak negative effects on activity, (iii) contribute to inflationary episodes outside the Nixon era, and (iv) transmit differently from standard expansionary monetary policy shocks because political pressure can be publicly observed, generating a stronger direct effect on inflation expectations. Quantitatively, increasing political pressure by half as much as Nixon, sustained for six months, is estimated to raise the price level by more than 8%.

Summary of a forthcoming paper, AI-assisted and human-reviewed. See the linked original for the authoritative claims and full conditions.

In depth

Q1. What is the narrative identification strategy and how is the Nixon-Burns episode exploited?

The identification strategy imposes that the spike in President-Fed personal interactions in 1971 is mainly driven by a political pressure shock, exploiting the well-documented fact that Nixon pressured Burns to ease monetary policy in the run-up to his 1972 re-election. Recordings from the “Nixon Tapes” and Burns’s personal diary corroborate this interpretation: Burns wrote that “the President will do anything to be reelected” and that Nixon urged him to “start expanding the money supply.” Romer and Romer (2004) estimated large easing shocks to monetary policy prior to Nixon’s re-election, contrasting with a large systematic tightening after it, further supporting that Burns eased in response to the pressure. Narrative evidence from Johnson’s pressure in the 1960s is additionally used to strengthen the identification.

Q2. What does the new data on President-Fed personal interactions show?

The paper hand-collects over 800 personal interactions between U.S. Presidents and Fed officials from the historical daily schedules made available by the Presidential Libraries from Franklin D. Roosevelt (1933) through Barack Obama (2016). The average interaction lasts 53 minutes; 36% are one-on-one; 11% occur on weekends; 16% are in social settings such as dinners; 92% involve the Fed Chair and 8% other Fed officials. There is large variation across administrations: President Nixon interacted with Fed officials 160 times, while only 6 interactions occurred under Clinton. These interactions arise endogenously in response to economic conditions, which is why narrative identification is needed to isolate the political pressure component.

Q3. What are the estimated macroeconomic effects of political pressure shocks?

Political pressure shocks are found to increase inflation strongly and persistently, to have statistically weak negative effects on activity, and a pressure shock half as large as Nixon’s sustained over six months is estimated to raise the price level by more than 8%. The weak activity effect distinguishes these shocks from standard demand expansions; the mechanism operates more through expectations channels than through aggregate demand, consistent with the public observability of political pressure on the central bank. The evidence also suggests political pressure shocks contributed to inflationary episodes in periods beyond the Nixon era.

Q4. Why do political pressure shocks transmit differently from conventional monetary policy easing shocks?

Political pressure shocks transmit differently from standard expansionary monetary policy shocks primarily because political pressure on the Fed can be publicly observed, which generates a stronger direct effect on inflation expectations than a private Fed decision to ease. The paper finds a stronger effect of political pressure shocks on inflation expectations relative to the activity effect, consistent with this channel: when the public observes that the President is pressuring the central bank, expected inflation rises even before the Fed acts on that pressure.

Key concepts

President-Fed personal interactions : face-to-face or telephone contacts between U.S. Presidents and Federal Reserve officials recorded in historical presidential daily schedules 1933–2016; used as a noisy observable proxy for political attention to the Fed, from which a political pressure shock series is extracted via narrative restrictions.

political pressure shock : an exogenous, structurally identified shock to the intensity of political influence on Fed policy, isolated using a narrative SVAR restriction that the 1971 Nixon-Burns spike in interactions was driven by political pressure rather than economic conditions.

narrative identification : an approach that imposes sign or zero restrictions on a structural VAR at specific historical episodes known from external archival evidence to be driven predominantly by a particular structural shock; here used to exploit the Nixon-Burns and Johnson-Fed pressure episodes.

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.

Layer 2 — Q&A

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.

The Confederate Diaspora

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

This paper investigates how white migration out of the postbellum South diffused Confederate culture and entrenched racial norms across the United States during a critical juncture of westward expansion and post-Civil War reconciliation. The central question is whether the “Confederate diaspora” — Southern white migrants who left the former Confederacy from 1870 to 1900 — causally shaped the geography of Confederate memorialization, white supremacist organizations, racial violence, and long-run racial inequity outside the South.

Using complete-count U.S. Census records from 1870–1900 and linked Census records from the Census Linking Project, the authors track nearly one million white migrants from former Confederate states, including more than 61,000 former enslavers and 127,000 of their household kin, who settled outside the South by 1900. By 1900, migrants from the former Confederacy comprised on average 2.2% of the population in destination counties. Four outcomes measuring Confederate culture at the county level are constructed: Confederate memorialization (monuments, place names, schools), United Daughters of the Confederacy (UDC) chapters, Ku Klux Klan (KKK) chapters, and lynchings of Black people.

The primary identification strategy is a shift-share instrumental variable (SSIV) that combines the cross-sectional distribution of Southern white migrants across non-Southern counties in 1870 (shares) with predicted migration flows out of each Southern state between 1870 and 1900 (shifts). The predicted shifts are constructed from origin-county economic and ideological push factors estimated via LASSO, insulating the IV from endogenous location sorting. Conditional on the 1870 Southern white population share, the SSIV identifies the distinct causal influence of the postbellum Confederate diaspora.

Main findings are large relative to the diaspora’s modest population share. Moving from zero to the mean Confederate diaspora share implies an 8 percentage point (p.p.) increase in the likelihood of KKK activity relative to a mean prevalence of 35% in non-Southern counties. Effects on post-1900 lynching events are even larger proportionally: a 4 p.p. increase in likelihood relative to a mean of only 5%. IV estimates for Confederate memorialization show that a 1 p.p. increase in the Southern white share in 1900 raised the likelihood of memorialization by 3.4 p.p. (after controlling for the 1870 share), relative to a baseline prevalence of 25% outside the South. Effects on UDC chapters are similarly large given the organization’s limited non-Southern footprint (present in only 10% of counties). IV estimates consistently exceed OLS estimates, consistent with economic sorting biasing OLS downward.

Beyond Confederate symbolism, the diaspora also contributed to a novel form of racial exclusion: the “sundown town.” A 1 p.p. increase in the Confederate diaspora share in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation (defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900).

Former slaveholders, though only about 6% of Confederate migrants, played an outsized role. They disproportionately sorted into frontier counties and into positions of public authority — more than twice as likely to work as lawyers or judges and nearly three times as likely to work in public administration as the average non-slaveholding Southern white migrant. Their cultural influence was especially pronounced in frontier communities where institutions were weak and norms malleable. In Denver, first-generation Southern white migrants were 11% more likely to join the KKK than men with no Southern heritage, with a similar differential observed for second-generation migrants.

The diaspora’s effects persist into the 21st century: counties with larger Confederate diasporas in 1900 exhibit larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, higher rates of police-induced Black mortality, and more conservative racial attitudes among whites, as measured in modern survey data. These long-run findings are identified using the same county-level SSIV strategy. Scope conditions: effects are larger in frontier counties (weaker institutions, more malleable norms), in counties with fewer Union Army enlistees, and in newly incorporated areas with fewer than 2 residents per square mile in 1860.

Q: What is the central research question and why does it matter? A: The paper asks whether postbellum Southern white migration causally diffused Confederate culture — memorialization, organized white supremacy, and racial violence — beyond the South, and whether this early cultural transplantation has persistent effects on racial inequity today. It matters because Confederate monuments and persistent Black disadvantage in labor, housing, and policing are often attributed to the legacies of slavery within the South; this paper shows the mechanism by which those norms spread nationally through internal migration at a critical juncture of westward expansion and post-war reconciliation.

Q: How large was the Confederate diaspora, and who comprised it? A: Estimates from linked Census records suggest that nearly one million whites left the former Confederacy for the rest of the U.S. in the three decades after the war, including more than 61,000 former enslavers and 127,000 of their household kin. By 1900, migrants from the former Confederacy averaged 2.2% of the population in non-Southern destination counties. The diaspora hailed primarily from the upper South — Virginia, Tennessee, and North Carolina — and later from Texas, Arkansas, and Oklahoma.

Q: How do the authors construct the shift-share instrumental variable, and what identifying assumption does it require? A: The SSIV multiplies each Southern origin state’s 1870 settlement shares across non-Southern counties (the shares) by predicted total Southern white outflows from 1870 to 1900 (the shifts), where the predicted shifts are constructed by summing LASSO-selected origin-county push factors — economic conditions, cotton and tobacco potential, Civil War battle locations, Black population share — rather than actual flows. The exclusion restriction requires that these predicted push-factor-driven outflows affect destination county outcomes only through the Confederate diaspora they deliver, not through direct economic linkages with origin counties. Conditioning on the 1870 Southern white share absorbs time-invariant destination heterogeneity correlated with antebellum settlement.

Q: What are the IV estimates for Confederate memorialization and UDC chapters? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of Confederate memorialization by 3.4 p.p. after controlling for the 1870 share (relative to a baseline prevalence of 25% outside the South). For UDC chapters, which were present in only 10% of non-Southern counties, IV estimates show similar or larger proportional effect sizes. IV estimates are consistently more than twice the size of OLS estimates, consistent with downward bias from economic sorting of Southern whites toward productive, culturally-diverse destinations.

Q: What are the IV estimates for KKK activity and Black lynchings, and how are they interpreted? A: A 1 p.p. increase in the Southern white share in 1900 raised the likelihood of KKK chapter presence by 3.5 p.p. (controlling for 1870 shares), relative to a mean KKK prevalence of 37% in non-Southern counties, implying that moving from zero to the mean diaspora share is associated with an 8 p.p. increase in the probability of KKK activity. For Black lynchings, the corresponding IV estimate is 1.5 p.p. (column 5), with the effect rising when earlier migration is controlled, against a mean prevalence of only 5% — implying moving from zero to the mean raises lynching likelihood by 4 p.p. Critically, the authors find no diaspora effect on white lynchings, which distinguishes racially-targeted violence from a generalized Southern culture of violence.

Q: What is a “sundown town” and what does the paper find about the diaspora’s role in producing them? A: Sundown towns, described in historical research by Loewen (2005), are all-white towns where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960 and representing a novel form of racial exclusion distinct from de jure Jim Crow institutions. The authors find that a 1 p.p. increase in the size of the Confederate diaspora in 1900 led to a 2.4 p.p. increase in the likelihood of Black depopulation — defined as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 — changing the geography of Black settlement throughout the 20th century.

Q: What role did former slaveholders specifically play, and how are their effects separately identified? A: Former slaveholders comprised just over 6% of the Confederate migrant sample but played an outsized role: they were about 50% more likely than the average Southern white migrant to work in any public-facing authority occupation, more than twice as likely to work as lawyers or judges, and nearly three times as likely to work in public administration. Their effects are identified using an analogous SSIV that, conditional on the instrumented overall diaspora, draws on distinct identifying variation in slaveholder-specific push factors. Former slaveholders gravitated toward Western, lower-density, cotton-suitable counties with higher Breckinridge vote shares and fewer Union Army soldiers, consistent with seeking to reconstruct antebellum hierarchies in malleable frontier spaces.

Q: Why were effects stronger in frontier counties? A: The paper finds that diaspora impacts on Confederate culture diffusion were significantly larger in counties along the frontier, where state institutions were weak and cultural norms not yet deeply ingrained. Restricting the sample to counties with fewer than 2 residents per square mile in the 1860 Census yields somewhat larger estimates than baseline, and the differential sorting of Southern whites (especially former slaveholders) into these nascent communities suggests that institutional malleability amplified the cultural entrepreneurs’ influence. Fewer Union Army enlistees in destination counties also amplified effects, as those families might otherwise have opposed resurgent Confederate ideology.

Q: How did the diaspora transmit its norms to subsequent generations and non-Southern neighbors? A: In the Denver metropolitan area, using newly digitized KKK membership records, first-generation Southern migrants were 11% more likely to join the KKK than men with no Southern heritage, and a similar differential holds for second-generation migrants (born in the diaspora), with patterns holding within Census enumeration blocks. White men without Southern heritage living next door to first- or second-generation Southern whites were significantly more likely to join the KKK, consistent with horizontal cultural spillovers. For naming patterns, non-Southern white parents who moved to counties with a larger Confederate diaspora gave their later-born children names more evocative of Confederate heroes than those given to earlier-born children — providing direct evidence of cultural spillovers beyond the diaspora.

Q: What long-run effects of the diaspora are documented through the 21st century? A: Using the county-level SSIV strategy, the paper finds that a larger Confederate diaspora in 1900 is associated with larger racial wage gaps, greater residential segregation, higher rates of Black incarceration, and higher rates of police-induced Black mortality through the 21st century. These disparities are mirrored in more conservative racial attitudes among whites in these counties as measured in modern survey data. These persistent effects suggest that, despite racially progressive national policy reform since the 1960s, locally institutionalized mechanisms reinforced by a culture of racial animus continue to generate inequity.

Q: How robust are the main estimates to alternative specifications? A: The authors show robustness across: (i) alternative spatial standard errors using Conley (1999) distance-based clustering and Adao et al. (2019) shift-share inference corrections; (ii) Belloni et al. (2014) double LASSO control selection; (iii) replacing predicted shifts with actual shifts; (iv) a random-shifts placebo where fewer than 5% of coefficients are significant; (v) dropping individual origin or destination states one-by-one (all estimates remain significant with 97% positive Rotemberg weights); (vi) excluding border states with antebellum slavery (Delaware, Kentucky, Maryland, Missouri, West Virginia), which actually increases estimates; and (vii) restricting to newly incorporated counties with near-zero 1860 populations, which yields somewhat larger effects.

Q: What is the paper’s contribution to the culture-institutions literature? A: The paper uses granular data on migration, occupational choices, and local governance to shed light on the historical process by which Confederate “cultural entrepreneurs” captured early institutions across America, illustrating how culture and institutions reinforce each other during critical junctures of nation-building. The findings suggest that laws to reduce racial discrimination may have limited impact where a culture of racial animus is ingrained in local institutions — an institutionalized persistence mechanism that helps explain the gap between formal legal reforms and observed racial outcomes. The paper also identifies a prestige-biased cultural transmission channel, consistent with Henrich and Gil-White (2001), wherein non-elite masses emulate former slaveowners in positions of power.

Confederate diaspora: The approximately one million white migrants, including more than 61,000 former enslavers and 127,000 of their household kin, who left former Confederate states for the rest of the U.S. in the three decades after the Civil War, comprising on average 2.2% of destination county populations by 1900 and retaining strong cultural attachments to the Confederacy.

Confederate culture: A cluster of symbolic and material expressions that coalesced in the postbellum South, encompassing Lost Cause narratives (glorifying Confederate figures and reframing secession as a defense of states’ rights rather than slavery), public memorialization (monuments, place names, school names), United Daughters of the Confederacy chapters, Ku Klux Klan activity, and lynchings of Black people — together functioning as technologies to transmit white supremacist norms and maintain racial hierarchies.

Lost Cause: A revisionist narrative emerging after the Civil War that sought to redeem the image of the South by offering noble rationalizations for secession — emphasizing Northern aggression and states’ rights while downplaying slavery — and portraying enslaved people as content and slaveowners as generously paternalistic; central to the ideology propagated by the UDC and to Confederate memorialization.

Shift-share instrumental variable (SSIV): An identification strategy that combines the 1870 distribution of Southern white migrants across non-Southern counties (shares, reflecting historical migration networks) with predicted total Southern white outflows from 1870 to 1900 constructed from origin-county push factors via LASSO (shifts), to isolate exogenous county-level variation in Confederate diaspora exposure that is insulated from endogenous location sorting.

Sundown town: An all-white municipality where Black residents and other minorities were excluded from residing after sunset, spreading throughout the non-South from 1890 to 1960, operationalized in this paper as towns with at least 25 Black residents in 1870 having zero Black residents after 1900 (Black depopulation), representing a novel form of racial exclusion distinct from de jure Jim Crow institutions associated with the Confederacy.

Prestige-biased cultural transmission: An evolutionary transmission mechanism, formalized in Henrich and Gil-White (2001), in which non-elite populations emulate culturally salient leaders; invoked in this paper to explain how former slaveholders in positions of authority could diffuse Confederate norms to non-Southern whites who had no direct connection to the Confederacy.

Cultural entrepreneur: A migrant (especially a former slaveholder) who, by sorting into positions of public-facing authority — judges, lawyers, law enforcement, clergy, public administrators — at early stages of community formation when institutions are most malleable, actively embeds cultural norms into nascent local institutions, amplifying influence beyond their small population share.

Why Doesn't the United States Have National Health Insurance?

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

This paper investigates a critical juncture in the development of national health insurance (NHI) in the United States: the post-World War II period when most peer nations moved to establish comprehensive public coverage while the U.S. did not. The authors examine the causal role of the American Medical Association (AMA), which in 1949 hired Whitaker & Baxter’s Campaigns, Inc. — the country’s first political public relations firm — to direct a nationwide campaign opposing NHI and promoting private (voluntary) health insurance (PHI).

The Campaign had two main components. First, a physician outreach component in which AMA members distributed pamphlets to patients warning against “socialized medicine” and encouraging enrollment in private plans, and acted as liaisons to local civic organizations to solicit resolutions against NHI sent to elected officials (nearly 50 million pieces of material were sent to physicians). Second, a mass newspaper advertising component, in which a standard ad was placed across newspapers nationwide, with an additional $19 million (approximately $240 million in current dollars) in coordinated tie-in advertising from roughly 23,000 corporations and industry associations. The messaging framed NHI as “un-American” and associated private insurance with “freedom” and “the American way,” providing little substantive information about insurance products.

The authors construct novel measures of Campaign exposure by combining (a) per capita pamphlets distributed by AMA physicians and (b) per capita advertising circulation scaled by local newspaper readership, using archival data from the Whitaker & Baxter Archives (Sacramento), the National Archives (Washington D.C.), digitized AMA Medical Directories, the N.W. Ayer & Son’s Newspaper Directory, and newly discovered Blue Shield enrollment data from AMA Council on Medical Service annual reports covering 1946–1954.

The primary estimation strategy exploits spatial variation in Campaign intensity combined with its timing, using event studies with state and year fixed effects and design controls for income per capita and unionization. The identifying assumption — that Campaign intensity was conditionally as-good-as-randomly assigned — is supported by balance tests showing no pre-Campaign correlation between exposure and enrollment or sociodemographic characteristics (with the exception of Black population share), and by the historical record that the Campaign was organized hastily following Truman’s unexpected 1948 electoral victory.

Main findings: A one standard deviation increase in Campaign exposure explains approximately 20% of the post-Campaign increase in PHI enrollment, corresponding to roughly 14 million additional enrollees — an effect comparable in magnitude to increasing average per capita income by approximately $100 (about 7 percent). On public opinion, a one standard deviation increase in Campaign exposure led to a six percentage point decline in popular support for NHI per Gallup survey wave, a reversal occurring against a backdrop of 69% pre-Campaign approval that was trending upward. For context, this six-point magnitude approximates the entire gap in NHI support between union and non-union households, or one-third the racial gap in support. Campaign intensity also predicts civic organizations passing resolutions favoring PHI, Republican legislators adopting speech semantically similar to Campaign propaganda, and — by 1952 — AMA members being five times more likely to donate to the Eisenhower-Nixon ticket than non-AMA physicians, with donation rates increasing in Campaign intensity.

Scope conditions: The analysis covers 48 U.S. states from 1946 to 1954, ending at the 1954 IRS tax code change that expanded commercial insurers’ market share. The enrollment data capture Blue Shield (physician-run) plans specifically; the paper explicitly notes that commercial insurer granular data are unavailable for the main Campaign period. The authors argue that multiple subsequent factors — middle-class acquisition of private coverage reducing demand for a public option, incumbent interests defending the status quo, and the persistent ideological linkage of private insurance with freedom — help explain why NHI was not adopted in subsequent decades, though these persistence mechanisms are outside the paper’s direct empirical scope.

Q: What was the AMA’s Campaign, and what prompted it? A: In response to Harry Truman’s unexpected 1948 presidential victory alongside a Democratic Congress — and with a majority of informed voters favoring NHI — the AMA hired Whitaker & Baxter’s Campaigns, Inc. to run the National Education Campaign (NEC). The Campaign had two components: physician outreach (pamphlet distribution to patients, liaison to civic organizations) and mass newspaper advertising. The AMA paid Whitaker & Baxter approximately $1.2 million per year in current terms, and coordinated an additional $19 million in 1950 dollars (roughly $240 million today) in tie-in advertising from allied corporations and trade groups.

Q: How is Campaign exposure measured, and how is it validated as conditionally exogenous? A: Campaign exposure combines two standardized components: per capita pamphlets distributed by AMA physicians (pamphlet quantity from W&B archives scaled by state AMA membership share) and per capita advertising circulation scaled by local newspaper readership (share of adults with more than five years of schooling). The two components are summed and standardized. Exogeneity is supported by balance tables showing no pre-Campaign correlation between exposure and enrollment or Gallup opinion, by the absence of discontinuous changes in income or unionization at Campaign onset, and by the historical fact that Campaign logistics relied on pre-existing networks assembled hastily in response to Truman’s unanticipated victory.

Q: What is the main effect of the Campaign on private health insurance enrollment? A: A one standard deviation increase in Campaign exposure is associated with a two percentage point increase in the share enrolled in PHI in the preferred specification (Column 4 of Table 1, which includes income, unionization, state fixed effects, and year fixed effects; coefficient 0.020, se 0.007, significant at 1%). This accounts for approximately 20% of the overall post-Campaign increase in PHI enrollment, corresponding to roughly 14 million new enrollees. The pre-Campaign coefficient is not statistically significant (coefficient 0.004, se 0.005), and the F-test p-value for pre-trends is 0.958.

Q: What is the effect of the Campaign on public opinion toward NHI? A: Using Gallup survey data, a one standard deviation increase in Campaign exposure led to an approximately six percentage point decline in individual support for NHI legislation per survey wave, against a pre-Campaign approval level of 69% that was trending upward. The F-test p-value for pre-trends in the Gallup event study is 0.179. This six-point effect is approximately equal to the gap in NHI support between union and non-union households, and approximately one-third the racial gap in support.

Q: What evidence links the Campaign to civic organizations and the legislative process? A: The Campaign’s archives document all civic organizations “on record against compulsory health insurance,” meaning they had passed resolutions in favor of PHI. The authors find a positive relationship between Campaign intensity and civic organizations passing such resolutions at the county level. Resolutions sent to elected officials were traced to the Congressional Record and to physical folders in the National Archives; their semantic similarity to AMA-WB propaganda is confirmed. Republican legislators’ speech in the 81st Congress shows increased similarity to Campaign language in proportion to Campaign intensity in their district or state, while Democrat legislators do not show this pattern. NHI and the AMA experienced spikes in mention frequency in the Congressional Record during this period.

Q: Did the Campaign affect physician political behavior beyond the clinic? A: By 1952, when the Republican platform had fully adopted the AMA’s position, AMA members were approximately five times more likely to donate to the Eisenhower-Nixon ticket than non-AMA physicians, with donation probability increasing in Campaign intensity. The authors digitized the donor list from the National Professional Committee for Eisenhower (NPCE) — a separate lobbying entity created because the AMA legally could not endorse candidates — and linked approximately 80% of physician donors to the AMA Medical Directory.

Q: What alternative explanations for PHI growth does the paper address, and how? A: The standard literature attributes PHI growth to the 1942 Stabilization Act wage freeze (which left benefits unconstrained), collective bargaining rights clarified in the late 1940s, and the 1954 IRS tax exemption for employer-paid premiums. The authors include income per capita and unionization as core design controls and show that their Campaign exposure coefficient is stable across specifications with and without these controls (coefficients of 0.025 and 0.020 in Table 1 Columns 1–2 vs. 3–4, respectively). The analysis stops in 1954 before the tax change, and the authors note that by 1952 roughly 63% of households already had some form of medical expense insurance.

Q: What is the conceptual mechanism through which the Campaign operated? A: The authors adapt Sobbrio (2011)’s indirect lobbying model. Voters hold uniform priors over whether NHI enactment yields net positive or negative social surplus. The private-sector advocate (AMA-WB) sends messages that shift voters’ posterior beliefs toward the negative-surplus state and, simultaneously, encourage PHI enrollment, which reduces voters’ private valuation of a public option. Because citizens were likely unaware of the coordinated tie-in advertising across industries and the financial motivation behind physician messaging, the framing operated through naive belief updating. The public-sector advocate (Truman administration, Committee for the Nation’s Health) was vastly outresourced — the CNH raised only $104,000 in 1949 — and faced legal constraints on executive lobbying.

Q: What advertising tactics specifically characterized the Campaign, and what do they imply about mechanisms? A: Campaign pamphlets and ads provided little or no substantive information about insurance products (coverage, eligibility, cost) and instead tied health insurance to ideological symbols: “freedom,” “the American way,” “the voluntary way,” and warnings about “socialized medicine.” Word clouds from Campaign materials confirm “America” and “freedom” as dominant terms. The authors connect this to behavioral models of advertising (Mullainathan, Schwartzstein and Shleifer 2008) whereby advertisers create or exploit associations to influence product beliefs. The absence of informational content is consistent with effects operating through ideology and identity rather than rational product evaluation.

Q: What explains why the U.S. did not adopt NHI in subsequent decades after the immediate Campaign period? A: The authors offer three mechanisms (discussed outside their main empirical scope): First, as middle-class Americans obtained PHI through employers, demand for a public option diminished — the model formalizes this as reduced private valuation of NHI. Second, incumbents who benefit from the private status quo — Blue Cross Blue Shield, AMA, American Hospital Association, and pharmaceutical companies, which today comprise four of the top ten direct federal lobbyists — actively work to maintain it (Acemoglu, Egorov and Sonin 2021). Third, the Campaign’s ideological framing proved durable: ideologically similar rhetoric opposing “socialized medicine” appeared in campaigns against both Clinton-era and Obama-era reform efforts, and has been linked to increased adverse selection and preventable deaths (Bursztyn et al. 2022; Galvani et al. 2022).

Q: What are the paper’s main contributions to the literature? A: The paper provides the first causal evidence on the AMA’s political role in blocking NHI at the post-WWII juncture, contributing to the economic history of U.S. social insurance development. It contributes to the advertising literature by providing credible estimates of a sustained national campaign combining trusted field agents (physicians) with mass media, and to the lobbying literature by documenting indirect lobbying — persuasion of ordinary citizens — as a distinct and effective tool alongside direct lobbying. It also documents physician behavior outside the clinical setting, showing how rents from supply-side constraints were deployed to shape the market for medical services.

Indirect lobbying: In the paper’s usage, persuasion of ordinary citizens via campaigns — as distinct from direct lobbying of policymakers — used to shift median voter beliefs and behavior to achieve legislative goals. Whitaker & Baxter are credited with creating this field through their work at Campaigns, Inc.

Campaign exposure: The paper’s composite treatment variable, constructed as the sum of two standardized components: per capita pamphlets distributed by AMA physicians (physician outreach) and per capita advertising circulation scaled by local newspaper readership (mass communications), then re-standardized to mean 0, standard deviation 1.

Tie-in advertising: Coordinated newspaper advertisements by third-party corporations and trade associations placed simultaneously with the main AMA-WB Campaign ad, sharing the “Voluntary Way is the American Way” slogan. Approximately 60% of newspapers with a main Campaign ad also had tie-in ads, averaging three per issue; third-party spending totaled approximately $19 million in 1950 dollars (~$240 million current).

Voluntary (private) health insurance: In the paper’s framing, the AMA-promoted alternative to NHI — prepaid medical service plans run by state medical societies (Blue Shield) or nonprofit hospitals (Blue Cross) — deliberately labeled “voluntary” to contrast with “compulsory” NHI, embedding the product within an ideological frame of free choice.

National Education Campaign (NEC): The AMA’s official name for the anti-NHI campaign directed by Whitaker & Baxter starting in 1949, characterized as “educational” to provide legal cover; the name itself illustrates the indirect lobbying strategy of framing political advocacy as public information.

Source text origin / abstract-only block: Not a paper-defined concept; excluded.

Naive voter updating: The paper’s modeling assumption (drawn from Sobbrio 2011) that voters held uniform priors on health insurance policy outcomes and updated beliefs via Bayesian message receipt, without awareness of coordination across industries or the financial motivation of physician messengers — making the ideological framing effective.

Physician field agents: In the Campaign’s design, AMA member physicians served as credible, trusted intermediaries who distributed pamphlets to patients and solicited civic organization resolutions, leveraging their social status to amplify the Campaign’s reach into communities where mass advertising alone would be insufficient.