H20 | Macro Paper Warehouse

"Compensate the Losers?" Economic Policy and the Origins of U.S. Partisan Realignment

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

Layer 1 — Overview

Research Question. Why have less-educated voters in the United States abandoned the Democratic Party over recent decades? The paper argues that the Democratic Party’s evolution on economic policy — specifically its retreat from “predistribution” — is a central, previously understudied driver of partisan realignment by education.

Conceptual Framework. The authors distinguish between two categories of egalitarian economic policy: (1) predistribution — policies that alter the pre-tax-and-transfer earnings distribution, including job guarantees, minimum wage increases, union support, and protectionist trade policies (following Hacker 2011); and (2) redistribution — taxes and transfers. The paper’s central claim is that these two types of policy have sharply different educational gradients among voters, and that the Democratic Party moved away from predistribution beginning in the 1970s, triggering educational realignment.

Data and Methodology. The authors harmonize over 1,000 surveys (N ≈ 2.2 million observations) spanning 1942–2020, drawn from Gallup, ANES, GSS, CCES, and historical survey archives housed at iPoll/Cornell. Education is translated into a common metric (adjusted years of schooling) using Census data, controlling for sex, race, year, and birth cohort to address the changing selectivity of educational categories over time. Congressional roll-call data come from the Comparative Agendas Project (CAP). Campaign finance data come from FEC filings, Congressional hearing records, and watchdog sources. DLC membership data are compiled from official Democratic Leadership Council records (available for 1985, 1986, 1991, 1993, and 1997 onward) and DLC-aligned Congressional caucus lists. House election returns are taken from King and Palmquist (1997) at the minor-civil-division-group (MCDG) level (~60 units per Congressional district), matched to 1980 Census demographic data.

Main Findings.

Voter preferences (demand side): The educational gradient for predistribution is large and negative: averaged across the four predistribution questions (job guarantee, minimum wage, union support, trade protection), each additional year of education reduces support by 0.044 standard deviations (p < 0.001). A college graduate relative to a high school graduate supports predistribution 0.176 standard deviations less — equivalent to roughly half the average Democrat-Republican gap in predistribution support (which is 0.34 standard deviations). This gradient has been stable since at least the 1940s. By contrast, the educational gradient for redistribution (higher taxes on the rich, views on own taxes, welfare spending) is close to zero (summary β = 0.004, not distinguishable from zero in the full sample). The difference between the two gradients is statistically significant (p < 0.001). These results replicate in white-only samples. Notably, the educational gradient on social issues — measured across nine questions on racial attitudes, gender roles, sexual norms — is positive (more education predicts more liberal positions) but has been largely stable since the 1940s, not increasing, conditional on the long-run sample.

Party supply (supply side): Before 1976, predistribution topics accounted for roughly one-quarter of Democratic House roll-call votes when Democrats controlled the chamber. After 1976 (taking Jimmy Carter’s presidency as the start of the “New Democrat” era), this share falls by approximately nine to ten percentage points, while the redistribution share of votes holds steady. Between 1968 and 1980, the union share of total PAC donations to Democratic Congressional candidates falls from approximately 90 percent to 40 percent, coincident with 1970s campaign finance reforms that placed union and corporate PACs on equal legal footing and allowed corporations to exploit their naturally deeper pockets. Corporate PAC share of Democratic donations correspondingly rises from approximately 10 percent to 45 percent over the same period. In individual contributions to primary elections (data beginning in 1980), Democratic primaries rely on increasingly more-educated census tracts relative to Republican primaries; by 2018 Democratic primaries are financed from census tracts averaging 0.41 more years of education than Republican primaries (against a within-year standard deviation of 1.56 years).

The New Democrat/DLC faction: The authors identify the anti-predistribution faction through official DLC membership records and aligned caucus lists. DLC membership as a share of Democratic House seats grows from near zero in the mid-1970s to approximately half by the early 2000s. Roll-call voting analysis (N = 3,428,405 vote-observations) shows DLC members are more conservative than other Democrats overall, and especially so on predistribution: for a 10-percentage-point increase in the share of Republicans voting for a bill, the probability a DLC member votes in favor increases 36 percent more on predistribution bills than on other bills. DLC members show no differential conservatism on redistribution. They are also significantly more socially conservative — more likely than other Democrats to support the Defense of Marriage Act (by 16 pp), the Partial-Birth Abortion Ban (by 7 pp), and restrictive immigration bills (by 10 pp). DLC candidates receive significantly less from labor PACs and significantly more from corporate PACs, and draw their out-of-district individual donations from census tracts averaging more than 0.1 years more educated than non-DLC Democrats.

Voter reaction and the inflection point: Using the N ≈ 2.2 million partisan identification dataset, the authors estimate a structural break in the education-party identification gradient. From the 1940s through the mid-1970s, each additional year of education reduces the probability of identifying as a Democrat by approximately 3 percentage points. A Chow breakpoint test identifies 1976 as the inflection point. Since 1976, the gradient steadily rises; by 2000 it reaches zero; and today (as of the sample period end ~2020) each additional year of education increases Democratic identification by approximately 3 percentage points — an almost exact reversal. The breakpoint for Republican identification occurs later, in 1992, consistent with the Democratic agenda changing first. A Gallup prosperity question (“which party will better keep the country prosperous?”) shows a parallel pattern: controlling for views on parties’ economic performance explains approximately 44 percent of partisan realignment, interpreted as an upper bound on economic policy’s contribution.

Factional tests — hypothetical elections and actual results: In hypothetical general-election matchups from 1972–1992 Democratic primaries (in which most contests pitted a “New Democrat” against an “Old Democrat”), a voter with a college degree is roughly 3 percentage points more likely to vote Democratic when the candidate is a New Democrat rather than an Old Democrat. In 1980s actual House elections using MCDG-level data, DLC candidates out-perform other Democrats in more educated neighborhoods by a magnitude large enough to erase approximately 90 percent of the general Democratic underperformance in highly educated areas. Combining these estimates, the party’s shift toward the DLC accounts for a lower bound of approximately 20 percent, and an upper bound (from the prosperity question) of approximately 50 percent, of educational realignment.

Scope Conditions. The analysis focuses on the United States, 1942–2015 (with some post-2015 discussion in the conclusion). The faction analysis focuses on the Democratic side; Republican faction changes are discussed but not the primary focus. The paper is explicit that between 20–50 percent of realignment is explained, leaving room for other factors, including social issues. The analysis ends mostly before 2016 to avoid complications from the closure of the DLC in 2011 and shifting post-2010 party dynamics.

In depth

Q1. What is the paper’s central conceptual innovation, and how does it differ from prior realignment research?

The paper separates egalitarian economic policies into “predistribution” (pre-tax-and-transfer market interventions such as minimum wages, job guarantees, union support, and protectionism) and “redistribution” (taxes and transfers) and shows these two types have sharply different educational gradients. Prior work typically aggregated all economic policies into a single index, which the authors argue masks essential heterogeneity. By documenting that the educational gradient is large and negative for predistribution but close to zero for redistribution — a pattern stable since the 1940s — the paper reframes the “voting against economic interest” puzzle: less-educated voters leaving the Democratic Party may be responding rationally to changes in the supply of the type of economic policy they actually prefer.

The average coefficient on adjusted years of schooling across the four predistribution questions is -0.044 (p < 0.001), stable over eight decades. A four-year difference in education (high school vs. college) shifts an individual’s support for predistribution by 0.176 standard deviations in the conservative direction — about half the average Democrat-Republican gap in predistribution support (0.34 standard deviations). For social issues, the summary gradient is positive (+0.028, p < 0.001 for the full sample), but this gradient has been largely stable since the 1940s across nine social issue questions, not increasing over time. This stability undermines the interpretation that rising social liberalism among the educated is a new phenomenon driving realignment, at least through the supply of parties’ social positions.

Using the Comparative Agendas Project classification, predistribution topics (labor regulation, industrial policy, public works, trade) accounted for roughly one-quarter of all House roll-call votes during years Democrats controlled the Speakership before 1977. After 1977, this share falls by approximately 9–10 percentage points (a decline of nearly half from its pre-1977 share), and the decline is statistically significant (p < 0.001). The redistribution share of votes holds essentially constant. Party platform data from Hopkins et al. (2022) show a sharp decline in Democratic use of terms like “minimum wage,” “full employment,” and labor-relations language beginning in the 1970s and 1980s, while Republican platforms use these terms sparingly throughout.

Q4. How did 1970s campaign finance reforms change the financial composition of the Democratic Party?

Before the early 1970s, unions enjoyed substantially more freedom than corporations under separate legal regimes governing PAC donations; mid-1970s reforms placed them on equal legal footing, enabling corporations to exploit their deeper pockets. The union share of total PAC donations to Democrats fell from approximately 90 percent in 1968 to approximately 40 percent by 1980, while the corporate share rose from approximately 10 percent to 45 percent. For Republicans, both series barely changed: unions had never donated substantially to the GOP, and the corporate share rose only modestly (from approximately 70 to 80 percent). The authors note the rapid decline cannot be attributed to falling union density in the economy, since both union and corporate PAC donations grew in absolute terms during this period; the relative shift was the result of the regulatory change.

Q5. Who are the “New Democrats” / DLC, and when did they emerge?

The DLC officially operated from 1985 to 2011, but members who would join it began entering Congress in large numbers in the 1970s (“Watergate Babies” of 1974, “Atari Democrats”). The DLC grew to approximately half of all Democratic House seats by the early 2000s. Members were drawn from suburban, affluent districts; their founder Al From explicitly criticized all four predistribution policies the paper studies (minimum wage, job guarantees, unions, and protectionism). The breakpoint test on DLC share in Congress identifies 1975 as the pivotal year — one year before the 1976 inflection point in partisan identification.

Q6. How do DLC members vote differently from other Democrats, and how is this differential conservatism distributed across policy types?

In roll-call regressions (N = 3,428,405 observations, with roll-call fixed effects), a 10 pp increase in the Republican vote share for a bill increases the probability a DLC member votes in favor by 1.48 pp more than for other Democrats (baseline result for all bills). For predistribution-classified bills, this excess alignment with Republicans is 36 percent larger than for non-predistribution bills. Crucially, DLC members are no more conservative than other Democrats on redistribution-classified votes (the interaction with redistribution is near zero and insignificant). DLC members are also differentially more conservative on social issues, a result that proves useful in separating economic from social-issue explanations of realignment.

Q7. Do DLC members finance differently from other Democrats?

Yes. In primary elections, DLC candidates receive approximately 9.7 pp less of their PAC financing from labor unions and approximately 6.7 pp more from corporate PACs (with state fixed effects) relative to non-DLC Democrats. Out-of-district individual contributions to DLC primary candidates come from census tracts averaging more than 0.1 years more educated than those for non-DLC Democrats, while within-district contributions show no significant difference (0.060 years, insignificant). This pattern suggests educated out-of-district donors, rather than local constituency demands, drive DLC candidates’ anti-predistribution orientation.

Q8. When precisely did educational realignment in Democratic party identification begin, and what does the inflection-point analysis show?

Using N ≈ 2.2 million observations from 1,006 surveys, a Bai-Perron breakpoint test on the year-by-year education gradient in Democratic party identification identifies 1976 as the inflection point (with robustness to alternative specifications yielding breakpoints of 1978–1980 for white-only samples and unadjusted years of schooling). Before 1976, each additional year of education reduces the probability of Democratic identification by approximately 3 percentage points (a stable, significantly negative relationship since the 1940s). After 1976, the gradient steadily rises; it reaches zero around 2000 and today is approximately +3 percentage points per year of education — nearly an exact reversal of the baseline. The corresponding Republican inflection point occurs in 1992, about 16 years later, consistent with the Democratic Party’s agenda changing first.

Q9. How do hypothetical presidential matchup surveys test the DLC mechanism?

The authors identify six Democratic primaries from 1972–1992 where a “New Democrat” and an “Old Democrat” were the top two contenders (e.g., Hart vs. Mondale in 1984, Clinton vs. Brown in 1992). Gallup and other surveys asked all respondents — regardless of party — whom they would vote for if either the New or the Old Democrat faced the eventual Republican nominee. A voter with a college BA is approximately 3 percentage points more likely to vote for the Democrat when the candidate is a New Democrat versus an Old Democrat (the “difference in differences” of hypothetical vote shares). This holds after controlling for state × election fixed effects and in five of the six election cycles studied (the 1976 exception is attributed to Mo Udall’s low name recognition, with 28 percent of respondents unfamiliar with him in a May 1976 poll). The result is attenuated but remains marginally significant when excluding non-white respondents, consistent with New Democrats’ success with white voters due in part to their more conservative civil rights positioning.

Q10. What do actual House election results (MCDG-level data) show about DLC electoral performance by neighborhood education?

Using 1980s House returns at the MCDG level (~60 neighborhoods per Congressional district), the authors regress Democratic vote share on neighborhood years of education interacted with a DLC candidate indicator, with Congressional district fixed effects. More-educated neighborhoods generally depress Democratic vote share (reflecting the still-negative overall educational gradient in the 1980s), but DLC candidates dramatically out-perform other Democrats in educated areas: the interaction coefficient is positive and significant, and its magnitude is large enough to erase approximately 90 percent of the general Democratic underperformance in highly educated neighborhoods. This result is robust to including District × Year fixed effects (so the identification comes from within-election, cross-neighborhood variation) and to adding controls for share white and share under age 35.

Q11. How much of educational realignment can the paper’s mechanism account for, and how is this calculated?

Two bounding estimates are provided. Upper bound (~44–50%): controlling for a respondent’s view on which party is better for economic prosperity (from Gallup since 1950) explains approximately 44 percent of the change in the education-party identification gradient (specifically, the total difference in the unconditional gradient between the 1948–1967 baseline and 2001–2020 is 2.411 pp per year of schooling; after controlling for the prosperity question, the unexplained residual is 1.342 pp, leaving a share explained of 44.3 percent). Lower bound (~20%): the difference in the education gradient between matchups involving New versus Old Democrats in Table 4 (~0.75 pp) divided by the total realignment shift (~4 pp from pre-1976 to post-2008 for presidential voting) implies the faction shift accounts for at least approximately one-fifth of realignment. The authors interpret these as bounds because the prosperity question may partly capture party identification itself (upper bound concern), while the hypothetical matchup estimate misses the broader ideological shift not captured in a single election (lower bound).

Three alternative explanations are addressed. (1) Civil Rights: Regional analysis shows that educated white Southerners left the Democrats in the 1940s–1960s (not the 1970s), consistent with their realignment being driven by Democrats’ liberal turn on civil rights rather than economic policy. After the 1960s, the South follows all other regions in the pace of educational realignment. (2) Republican changes: The Republican party identification inflection point occurs in 1992, about 16 years after the Democratic inflection in 1976. Reagan elections in 1980 and 1984 do not appear to have differentially attracted less-educated voters (the “Reagan Democrats” were not differentially less educated). (3) Social issues: The New Democrats were actually more socially conservative than other Democrats (more likely to vote for DOMA, anti-abortion bills, restrictive immigration legislation), yet they disproportionately attracted educated voters. This internal inconsistency rules out a pure social-issues explanation for why educated voters preferred the DLC faction. (4) Religion: Flexibly controlling for religious affiliation explains essentially none of partisan realignment (Appendix Figure A.24).

Q13. What is the role of out-of-district individual donors in shifting Democratic Party positions?

Out-of-district primary donors are analytically important because they influence candidate supply without being able to vote in the election, isolating the “within-party” financial influence of educated supporters. By 1980, out-of-district primary donors to Democratic candidates already come from census tracts more educated than those for Republican candidates, even as local Democratic voters and within-district donors remain less educated than Republican counterparts. Democratic candidates also receive a substantially higher share of out-of-district contributions than Republican candidates — by almost 10 percentage points (Appendix Table A.7). Out-of-district donors thus represent a channel through which educated, anti-predistribution preferences are transmitted into the Democratic Party’s candidate supply before the electoral realignment is visible in vote totals.

Q14. Are predistribution policies becoming less popular overall, which might independently push Democrats away from them?

The paper tests this alternative in Appendix Table A.9 and finds no evidence that predistribution has become less popular relative to redistribution over time. Predistribution appears on average more popular than redistribution across the sample period. If anything, support for predistribution has held steady or slightly risen relative to redistribution over time, conditional on the paper’s survey harmonization. The stability of the educational gradient (shown in Appendix Table A.10 to be unchanged even using educational rank within cohort rather than raw years of schooling) further suggests the negative education-predistribution relationship is a relative, not absolute, phenomenon — consistent with rising average education and stable preferences by education rank.

Key Concepts

Predistribution: Policies that aim to change the distribution of earnings or income before taxes and transfers are applied. In this paper, this comprises government job guarantees, minimum wage increases, support for unions and collective bargaining, and protectionist trade policies. Distinguished from redistribution in that it operates on pre-tax market income rather than post-tax outcomes. The paper uses this term following Hacker (2011): “a focus on market reforms that encourage a more equal distribution of economic power and rewards even before government collects taxes or pays out benefits.”

Redistribution: Policies that change post-market income through the tax and transfer system, including higher taxes on the rich, views on own tax burden, prioritization of tax cuts, and transfers to the poor (welfare spending). In the paper’s usage, redistribution is analytically distinct from predistribution and has a near-zero educational gradient, in contrast to predistribution’s strongly negative gradient.

Educational Gradient: The coefficient on adjusted years of schooling in a regression of an outcome variable (policy preference or partisan identification) on education, estimated separately by time period. The paper’s core finding is that the educational gradient for predistribution is stably negative (approximately -0.044 per year of schooling over the full sample), while the gradient for redistribution is close to zero, and the gradient for Democratic party identification shifts from approximately -0.03 to +0.03 per year of schooling between the 1940s and 2020.

New Democrats / DLC (Democratic Leadership Council): An explicitly anti-predistribution faction within the Democratic Party, identified through official DLC membership records and affiliated Congressional caucus lists. Founded formally in 1985 (operating through 2011), the DLC arose in part from the “Watergate Babies” cohort of 1974. DLC members were more conservative than other Democrats especially on predistribution and social issues, relying differentially on corporate PACs and educated out-of-district donors. The paper treats DLC membership as a proxy for an anti-predistribution faction that gained bargaining power within the Democratic Party from the 1970s onward.

Adjusted Years of Schooling (AdjYearsEduc): The paper’s harmonized education variable across more than 1,000 surveys spanning eight decades. Because raw educational categories change over time and represent different selectivity (e.g., in 1940 only one-quarter of adults had completed twelfth grade, versus nearly 90 percent today), the authors use Census microdata to predict years of schooling as a function of self-reported educational category, sex, race, year, and birth cohort in ten-year bins. This provides a common unit of measurement across surveys with incompatible category systems.

Inflection Point (1976): The structural break in the trend of the education-Democratic identification gradient, estimated using Bai-Perron (1998) methods on N ≈ 2.2 million observations. The data select 1976 as the year at which the previously stable negative gradient begins its upward trajectory. The corresponding Republican inflection point occurs in 1992. The paper argues that identification of this inflection point — not previously documented in the realignment literature — is made possible only by the large historical dataset assembled.

Minor Civil Division Group (MCDG): The granular geographic unit used in the House election analysis for the 1980s, with approximately sixty MCDGs per Congressional district. Matched to 1980 Census demographic data to assign average years of education. Used to test whether DLC candidates out-perform other Democrats in more-educated neighborhoods, within the same Congressional district and election year, to address the concern that DLC candidates sort into more-educated districts.

Global Working Hours

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

Drawing on about 5,000 labor force and household surveys from 160 countries that cover 97% of the world’s population, this paper builds a new global database of hours worked and shows that hours worked per adult decline only slightly with GDP per capita and are weakly correlated with economic development overall: the unconditional elasticity of hours with respect to GDP is about -0.04 across countries and -0.01 within countries over time, GDP explains roughly 5% of cross-country and under 1% of within-country historical variation in hours, and the implied reduction is 0-20% over the entire development spectrum. The strong age and gender gradients the authors document are, in their cross-country regressions, driven less by development itself than by institutions: hours worked by the young (aged 15-19) and the elderly (aged 60+) fall with development almost entirely because of rising school attendance and public pension coverage, while prime-age (20-59) hours stay roughly flat but undergo what the authors call a “great gender reshuffling,” in which falling male hours per worker are quantitatively offset by rising female labor force participation. Across countries and over time, labor taxes are strongly negatively correlated with prime-age hours worked; controlling for government transfers only partly reduces this link, which the authors read as ruling out income and substitution effects on labor supply as the only driver, while controlling for working-hours regulations and the size of the formal sector reduces the link much more sharply, suggesting to them that regulation—not just the incentive effects of taxes—plays a large role in shortening intensive-margin hours in richer countries. The authors conclude that collective choices and social norms, often encoded in public policy (schooling, pensions, cultural norms about women’s work, and hours regulation), powerfully shape working hours over and above pure economic development. These are correlational cross-country and time-series patterns rather than identified causal effects, and hours are measured as weekly hours in all GDP-producing jobs (including unpaid agricultural work but excluding unpaid home services).

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 new data does the paper assemble, and how does it improve on prior global hours databases?

The authors mobilize roughly 5,000 nationally representative household and labor force surveys to build a database of hours worked covering 160 countries and 97% of the world population in cross section, plus time series spanning over 20 years in 86 countries. They combine six groups of sources, principally the ILO’s Microdata Repository (about 1,800 surveys in 150 countries since 1990) and the World Bank’s I2D2 database, which include survey data not publicly disclosed by the countries that created them. This extends the most comprehensive prior effort, Bick, Fuchs-Schündeln, and Lagakos (2018), whose core database covered 49 countries (23% of world population) and whose extended database covered 80 countries (41%); large countries such as China and India (35% of world population) that were absent from that study are now included. The authors state they are publishing and plan to regularly update the underlying database at the country×year×age×gender level so that researchers can reproduce their results.

Q2. How seriously does the seasonality concern affect the estimates?

The authors investigate seasonality directly and conclude that monthly seasonality in hours worked is limited in developing countries—actually larger in richer countries because of summer holidays—which gives them confidence that surveys not fielded over the full year still provide reliable annual hours estimates. This matters because Bick, Fuchs-Schündeln, and Lagakos (2018) had restricted their core sample partly out of concern that surveys run in specific months (e.g., around seasonal agricultural work) could bias hours estimates. Resolving this concern is what lets the authors retain the far larger country coverage.

Q3. How much do hours worked actually vary with economic development?

Hours worked per adult slightly decline with GDP but are only weakly correlated with development overall, with an unconditional elasticity of about -0.04 in the cross section and -0.01 in panel data—implying a reduction in hours of 0-20% over the entire development spectrum. GDP explains around 5% of cross-country variation in hours worked and less than 1% of historical within-country variation. Decomposing the margins, employment rates are essentially uncorrelated with development, while hours per worker are bell-shaped: they rise at low levels of development because of structural change (hours in manufacturing and services are very high in middle-income countries, while agricultural hours are moderate and flat with GDP), then flatten. Globally, 59% of the adult population (aged 15+) is employed, working an average of 42 hours per week, which implies about 25 weekly hours per adult; hours are strongly bell-shaped with age, and women supply 35% of GDP-producing hours versus 65% for men, a gap driven mostly by the extensive employment-rate margin.

Q4. Why do hours worked by the young and the elderly fall with development?

In simple cross-country regressions, the decline in hours worked by the young (15-19) and the elderly (60+) as countries develop is entirely driven by rising school attendance for the young and rising public pension coverage for the elderly, in line with a broad body of prior work. In the time series the two margins diverge: the fall in youth work is particularly pronounced, whereas elderly work is stable rather than falling. The authors read this as consistent with developing countries expanding schooling faster, but rolling out elderly pensions more slowly, than frontier economies did historically.

Q5. What happens to prime-age hours, and what is the “great gender reshuffling”?

Prime-age (20-59) hours worked are flat, if not slightly increasing, with GDP per adult, but this stability masks a large compositional shift the authors term a “great gender reshuffling”: female hours rise with development while male hours decline, and the fall in male hours (driven by reduced hours per worker) is quantitatively offset by increases in female employment rates. The authors interpret this as development tending to equalize hours across genders—shortening the long hours of working men while allowing more women into GDP-generating employment. They emphasize considerable heterogeneity across countries and over time in this pattern.

Q6. What role do religion and political history play in female hours worked?

The authors report that Muslim/Hindu religion depresses female hours worked enormously, while former communist status increases them. Grouping countries into former-communist, Muslim/Hindu-majority, and other categories, they show female hours rise with development on average but with large level differences across these groups, which they treat as evidence that cultural and institutional factors—not development alone—shape the gender allocation of work. These are descriptive cross-country associations, not causal estimates.

Labor taxes are strongly negatively related to prime-age hours worked, both in international comparisons and within-country time series; once tax variables are controlled for, GDP per capita is only weakly positively correlated with hours, with an elasticity of around 0.1. The authors probe what drives the tax-hours link. Controlling for social spending (cash or quasi-cash transfers) attenuates it, consistent with income effects from transfers playing some role—but the attenuation is only partial, which the authors read as ruling out income and substitution effects on labor supply as the sole driver. Controlling instead for the share of formal workers and working-hours regulations reduces the link much more sharply. They therefore suggest labor taxes depress hours not mainly through income and substitution effects but rather because high labor taxes correlate with the development of a formal sector with regulated working hours.

Q8. Can a standard labor supply model rationalize these findings?

The authors note that a standard labor supply model with a low uncompensated but large compensated labor supply elasticity can rationalize the joint pattern of weak hours-GDP but strong hours-tax correlations. The logic they invoke from the macroeconomics literature is that economic growth raises the wage rate (an uncompensated labor supply effect, which is weak here) while labor taxes fund transfers (a compensated labor supply effect, which is stronger). The partial attenuation of the tax effect when social spending is controlled is consistent with this account, but the sharper attenuation from regulation and formal-sector controls leads the authors to give regulation a large role alongside—rather than instead of—these labor supply channels.

Q9. What is the paper’s overall interpretation?

The authors conclude that collective choices and public policies—schooling and pension systems, cultural norms regarding women, and regulations on hours worked—have first-order effects on the level and allocation of working hours by age and gender, over and above economic development. They argue that while growth may help develop such institutions, many are only partially determined by it, which is why large cross-country variations in hours worked persist at all levels of development. The paper is framed as documenting and interpreting robust correlations across countries and over time, not as identifying causal policy effects.

Q10. What are the main scope conditions and caveats?

Throughout, hours worked follow international conventions: weekly hours in all jobs that contribute to GDP, including unpaid agricultural work but excluding unpaid home services such as cleaning, cooking, and care. Coverage is 97% of world population, with the missing 3% concentrated in parts of the Middle East and North Africa. The central results on taxes, transfers, regulations, religion, and communist history are correlational—drawn from cross-country regressions and within-country time series—and the authors repeatedly use calibrated language (“correlated,” “suggests,” “consistent with”) rather than claiming identified causal effects.

Key concepts

Hours worked (GDP-producing) : Weekly hours in all jobs that contribute to GDP, following international conventions—this includes unpaid agricultural work (which produces goods counted in GDP) but excludes unpaid home services such as cleaning, cooking, and caring for children or the elderly. Great gender reshuffling : The paper’s term for the pattern in which, as countries develop, declining male hours per worker are quantitatively offset by rising female labor force participation, leaving prime-age (20-59) hours worked roughly stable while its gender composition shifts markedly. Unconditional elasticity of hours with respect to GDP : The raw cross-country (about -0.04) or panel (about -0.01) elasticity of hours worked to GDP per adult before conditioning on taxes, transfers, or institutions; its small size is the paper’s headline evidence that development per se explains little hours variation. Uncompensated vs. compensated labor supply elasticity : In the standard labor supply model the authors invoke, growth raises wages (an uncompensated effect, weak in their data) while labor taxes fund transfers (a compensated effect, stronger in their data); a low uncompensated and large compensated elasticity reconciles weak hours-GDP with strong hours-tax correlations. Formal sector / working-hours regulations : Regulated wage employment in which statutory limits on hours bind; the authors emphasize that the expansion of this regulated formal sector with development, rather than the incentive effects of taxes alone, is the channel that most sharply accounts for shorter intensive-margin hours in richer countries.

Key concepts

Place-Based Redistribution

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

Place-Based Redistribution: Overview

Research Question

Should national governments redistribute income to residents of poor areas through place-based transfers, or should redistribution rely solely on place-blind (income-only) taxes? The longstanding view in urban economics—“help poor people, not poor places”—holds that place-based aid is inefficient because it channels activity to less productive locations. This paper challenges that view by formalizing the conditions under which place-based redistribution improves on purely income-based transfers, using tools from optimal tax theory embedded in a spatial equilibrium model.

Model and Methodology

The paper develops a two-location model (“Distressed” and “Elsewhere”) with a unit mass of heterogeneous households who differ in skill level (θ) and idiosyncratic preference for living in Distressed (φ). Households choose where to live and how much to earn, facing competitive labor and housing markets in each location. Locations may differ in amenity levels, wage schedules (which may embody skill-specific comparative advantage), and housing costs. A utilitarian planner sets location-specific income tax schedules—observed earnings and location are the only signals of unobserved skill—maximizing a weighted average of household utilities and landlord profits subject to a budget constraint.

The paper proceeds in three steps. First, it derives closed-form conditions for the optimality of a lump-sum place-based transfer under a fixed income tax. Second, it characterizes fully general optimal nonlinear, location-specific marginal tax rate (MTR) schedules (Proposition 2). Third, it calibrates the model numerically, anchoring to the U.S. Empowerment Zone (EZ) program.

Three Sorting Mechanisms and Their Policy Implications

The paper identifies three polar mechanisms that generate sorting of lower-skill households into Distressed:

Skill-taste correlation: higher-skill households have stronger tastes for Elsewhere, independent of wages or rents.
Comparative advantage: higher-skill workers are relatively more productive in Elsewhere.
Income-based sorting: because Elsewhere is more expensive, lower-income households are priced into Distressed.

Under skill-taste correlation, place-based transfers to Distressed are unambiguously welfare-improving even when income taxes are already optimal, because high-skill households prefer Elsewhere for reasons that are orthogonal to income. Under comparative advantage, the direction of the optimal transfer depends on migration elasticities: low migration elasticities favor transfers to Distressed, while high migration elasticities can reverse the sign. Under pure income-based sorting (with homogeneous locational preferences), the conditions for superfluous commodity taxation (Atkinson-Stiglitz 1976) are satisfied, and optimal place-based transfers are zero—though idiosyncratic preference heterogeneity restores non-zero optimal transfers even in this case.

Quantitative Findings

Numerical simulations use Census data and ACS moments calibrated to EZ areas. With high migration responsiveness (κ = 0.5, approximating urban EZs) and skill-taste correlation as the sole sorting driver, the optimal average place-based transfer to Distressed is $4,805, with about 40% ($1,943) arising from lower MTRs rather than a higher demogrant. With low migration responsiveness (κ = 4, approximating rural EZs), the optimal transfer more than doubles to $10,918.

When comparative advantage alone drives sorting and migration is low (κ = 4), the optimal transfer to Distressed is $7,091, with a $3,740 larger demogrant. With high migration and comparative advantage, the transfer reverses to −$2,763 (i.e., Elsewhere receives the subsidy). For intermediate migration under comparative advantage (e.g., κ ≈ 1), the optimal policy is nonlinear: the poorest Distressed residents receive a place-based transfer of $1,254, while high-skill Distressed residents face a place-based tax of $12,398 at the 99th percentile.

In the empirically calibrated urban EZ baseline (migration elasticity 0.82, rent ratio 0.86, sorting driven by skill-taste correlation and income effects), the optimal average place-based transfer is $3,143, roughly matching the magnitude of actual EZ wage tax credits (~$3,000 for full-time eligible workers). The demogrant advantage for Distressed is $1,462, with just over half of the transfer arising from lower MTRs.

In the rural EZ baseline (migration elasticity 0.20, rent ratio 0.54, comparative advantage and income effects), the optimal average transfer rises to $4,329, concentrated in lower MTRs rather than a larger demogrant. Halving the migration elasticity from the rural baseline raises the optimal transfer to $6,906, while doubling it reduces the transfer to near zero ($573).

Scope Conditions

All results are derived under the assumption of no market failures; the model deliberately excludes agglomeration spillovers or other Pigouvian motives, attributing the case for place-based redistribution purely to redistributive goals.
The planner observes only earnings and location, not skill type directly.
Household Pareto weights are set equal to one across types in the simulations, so redistribution is driven solely by diminishing marginal utility of consumption.
The model abstracts from interactions with subnational governments, local public services, and endogenous amenities.
Results on the desirability of transfers to Distressed hinge critically on the motive for sorting, not simply on the existence of spatial income inequality.

In depth

Q1. What is the equity-efficiency tradeoff formula for a lump-sum place-based transfer, and what does it reveal?

Lemma 1 shows that the first-order welfare effect of a small per-capita transfer from Elsewhere to Distressed starting from a place-blind tax system is dSWF/dt = (λ̄₁ − λ̄₀) + Eθ{m(0)·[T(z₁*) − T(z₀*)]}. The equity gain (λ̄₁ − λ̄₀) is positive when Distressed households have higher average social marginal welfare weights, which holds when their skill distribution is first-order stochastically dominated by Elsewhere’s. The fiscal cost equals the earnings-tax-revenue loss from movers: households induced to migrate to Distressed who earn less there generate lower tax payments. This formula identifies the earnings response to migration as a sufficient statistic for the efficiency cost of place-based policy.

Q2. What characterizes the optimal lump-sum transfer t* in Proposition 1?

Proposition 1 shows t* = [λ̄₁(t*) − λ̄₀(t*) + Eθ{m(t*)·[T(z₁*) − T(z₀*)]}] / (Eθ[m(t*)] / [L₀(t*)L₁(t*)]). The optimal transfer is larger when (i) the average social marginal welfare weight gap between Distressed and Elsewhere is greater, (ii) migration responses m(t*) are small, and (iii) the earnings difference between locations for marginal movers is small. This formula holds regardless of whether the income tax schedule T(·) is itself set optimally.

Q3. Under skill-taste correlation, why are place-based transfers always welfare-improving even under an optimal income tax?

When sorting is driven by skill-taste correlation (high-skill households have stronger preferences for Elsewhere despite identical wages and rents), the equity gain λ̄₁ − λ̄₀ is positive because low-skill households concentrate in Distressed. A small positive transfer starting from t = 0 also incurs zero fiscal cost because movers between locations face identical wages and do not change their earnings. Thus, welfare unambiguously increases. The key insight is that skill-taste correlation violates the Atkinson-Stiglitz condition: high earners would still prefer Elsewhere even if forced to earn less, so location serves as a proxy for skill not captured by income taxes alone.

Q4. Under comparative advantage, why can the sign of the optimal transfer reverse with migration elasticity?

When higher-skill workers are more productive in Elsewhere, movers to Distressed experience wage and earnings reductions, generating a fiscal externality. When migration elasticities are high (low κ), this fiscal cost is large and can dominate the equity gain, making transfers to Elsewhere optimal (simulated optimal transfer of −$2,763 at κ = 0.5). When migration elasticities are low (high κ), the fiscal cost is small and equity considerations dominate, yielding transfers to Distressed ($7,091 at κ = 4). At intermediate elasticities, the optimal policy is nonlinear, redistributing to poor Distressed residents while taxing rich Distressed residents more.

Q5. Why are place-based transfers superfluous under pure income-based sorting with homogeneous locational preferences?

Example 6 (and its formal proof in Appendix B.3.5) demonstrates that when sorting arises solely from higher rents in Elsewhere and preferences over location are homogeneous (no idiosyncratic φ heterogeneity), the Atkinson-Stiglitz sufficient condition for commodity tax superfluousness is met: hypothetically forcing high earners to earn less would not change their preferred consumption bundle relative to low earners. Hence a place-blind income tax implements optimal redistribution without spatial supplements. As the variance of idiosyncratic location preferences κ shrinks toward zero, Figure 3 confirms that optimal place-based transfers tend toward zero across all three sorting motives.

Q6. What new terms appear in the optimal location-specific MTR formulas (Proposition 2) relative to a standalone-economy optimum?

The optimal MTR schedules in Proposition 2 contain two new terms beyond the standard Mirrlees (1971)/Saez (2001) formula. The term Δτ+(θ) captures the fiscal externality from migration: raising Elsewhere’s MTR at skill level θ and above induces movers to Distressed who change their tax revenue by T₁(z₁*(s)) − T₀(z₀*(s)). The term (λ_L − 1)Δr+(θ) captures the equilibrium rent effect: MTR changes shift households between locations, altering rents in both communities and redistributing between renters and landlords. When λ_L < 1 (landlords are weighted less than average households), the rent term creates additional motives for spatial redistribution depending on the ratio of rents to housing supply elasticities across locations.

Q7. How do housing supply elasticities affect the optimal spatial transfer, and why does the sign differ between urban and rural settings?

The rent redistribution term Δr+(θ) has sign determined by r₁/ϱ₁ − r₀/ϱ₀. For urban EZs, where Distressed has lower rents but also lower housing supply elasticity than Elsewhere (ϱ₁ = 0.24, ϱ₀ = 0.34 in the baseline), this ratio is positive, meaning transfers to Distressed shift households into relatively inelastic markets, raising rents there and generating landlord income. When λ_L < 1, this reduces the desirability of transfers to Distressed. For rural EZs, Distressed has higher housing supply elasticity (ϱ₁ = 0.60), so the ratio is negative: transfers shift households to more elastic markets where rents rise minimally. When λ_L < 1, this actually motivates more transfers to rural Distressed areas. In the 75%-landlord-weight sensitivity, optimal urban transfers fall by ~$1,000 while rural transfers rise by ~$1,000, illustrating this asymmetry.

Q8. What does the urban EZ baseline calibration find about optimal transfers and how does it compare to actual EZ policy?

The urban baseline targets a migration elasticity of 0.82 (from Busso et al. 2013), a Distressed-to-Elsewhere rent ratio of 0.86, and 56% of Distressed residents earning under $50,000. The calibrated κ is 0.44. At the optimum, Distressed residents receive an average place-based transfer of $3,143, with $1,462 as a higher demogrant and the remainder from lower MTRs. By comparison, actual EZs provide a wage tax credit of approximately $3,000 per eligible full-time worker. The paper concludes that the magnitude—but not the capped, flat structure—of EZ transfers approximates the optimal level.

Q9. What does the rural EZ calibration find, and how sensitive are results to migration assumptions?

The rural baseline targets a migration elasticity of 0.20 (from Sprung-Keyser et al. 2022), a rent ratio of 0.54, and 60% of Distressed residents earning under $50,000, with sorting attributed to comparative advantage and income effects. The calibrated κ is 4.06. The optimal average transfer is $4,329, primarily arising from lower MTRs rather than a higher demogrant ($532). Doubling the migration elasticity reduces the optimal transfer to near zero ($573); halving it raises it to $6,906. The direction and magnitude of optimal transfers are therefore highly sensitive to the assumed level of migration responsiveness, highlighting the empirical importance of estimating migration elasticities—particularly heterogeneity in migration by income level and earnings changes for marginal movers.

Q10. Do within-income transfers arising from differences in marital and parental status across communities effectively constitute place-based redistribution?

Online Appendix A investigates this by estimating the implicit place-based transfer induced by marital and parental status differences between EZ communities and the rest of the country. Using ACS tract-level data merged with Piketty-Saez-Zucman distributional national accounts (DINA), the authors find that marital status and parental status have offsetting effects: marital status raises taxes on single households (common in Distressed), while parental status increases transfers to households with children (also common in Distressed). Across all preferred CPS-adjusted estimates, net within-earnings transfers are below $1,000 in magnitude, and the two factors essentially cancel. The authors conclude that marital and parental status differences do not yield substantial de facto place-based redistribution within income levels.

Q11. What does the MTR decomposition (Table 3) reveal about why sorting motives generate different MTR patterns?

The decomposition separates the optimal MTR into a within-community component (standard equity-efficiency tradeoff) and a between-community component (fiscal externality from migration). Under skill-taste correlation with high migration (κ = 0.5), both components contribute positively to the Distressed MTR (0.246 within + 0.234 between = 0.479), yielding lower MTRs in Distressed (0.479) than in Elsewhere (0.510). Under comparative advantage with high migration, the within-community component is negative (−0.111) because high MTRs at the optimum reduce the concentration of high-skill types in Distressed, depressing the standard revenue-raising benefit of MTRs. The large positive between-community component (0.655) reflects the large fiscal externality from movers and overcomes this, yielding higher Distressed MTRs (0.544 vs. 0.509 in Elsewhere). With low migration (κ = 4), between-community components shrink substantially, and MTRs in Distressed fall below Elsewhere in all sorting scenarios.

Q12. What does the crosswalk from urban to rural baseline reveal about which assumptions drive the change in optimal transfers?

Table 5 traces the urban-to-rural transition step by step. Starting from the urban baseline ($3,143 average transfer), replacing the migration elasticity target with the rural value of 0.20 triples the optimal transfer to $9,870. Subsequently replacing skill-taste correlation with comparative advantage as the sorting mechanism reduces the transfer by roughly half ($6,402). Adjusting rent to match the rural ratio (0.54) reduces it further to $2,780, as lower Distressed rent reduces the marginal utility of consumption at the bottom and increases income-based sorting. Targeting the rural income share (60% below $50K) raises it back to $4,140, and incorporating rural housing supply elasticities yields the rural baseline result of $4,329. This decomposition reveals that lower migration responsiveness is the single largest driver of higher optimal transfers in rural settings.

Key Concepts

Place-based redistribution: Transfer schemes in which economic benefits or tax burdens are conditioned on the geographic location of residence, as distinct from place-blind income taxes that condition only on earned income. In this paper, modeled as location-specific tax schedules T_j(z) that may differ across communities j.

Skill-taste correlation: A source of spatial sorting in which households with higher skill levels (θ) have systematically stronger preferences for the “Elsewhere” location, independently of wage or rent differences. Formally, the conditional distribution G_θ(φ) of locational tastes given skill is weakly increasing in θ. This correlation breaks the Atkinson-Stiglitz sufficient condition for commodity tax superfluousness and generates unambiguously positive optimal transfers to Distressed.

Comparative advantage (spatial): A sorting mechanism in which higher-skill workers are disproportionately more productive in Elsewhere than in Distressed, captured by the wage elasticity with respect to skill being higher in Elsewhere (γ₀(θ) > γ₁(θ)). Households with skill above a threshold sort into Elsewhere even with homogeneous locational preferences. The existence of spatial comparative advantage means that migrants to Distressed earn less, creating a fiscal externality for place-based transfers.

Income-based sorting: Sorting of lower-income, lower-skill households into Distressed arising purely from the higher cost of living in Elsewhere, without any systematic skill-taste correlation or comparative advantage. Because high-skill households are less sensitive to rent differences, they sort into Elsewhere when rents there are higher. When this is the sole sorting mechanism and locational preferences are homogeneous, the Atkinson-Stiglitz commodity tax superfluousness conditions are satisfied and optimal place-based transfers are zero.

Fiscal externality (migration): The change in income tax revenue caused by migration responses to place-based policy changes, not by changes in incentives for stayers. When movers from Elsewhere to Distressed earn less in their new location, they generate lower tax payments, imposing a first-order cost on the government budget. This externality is measured by Δτ+(θ) in the optimal MTR formulas and equals the earnings-tax-revenue loss from movers across all skill levels above θ. This term is a “sufficient statistic” for the efficiency cost of place-based transfers in the sense of Chetty (2009).

Demogrant (∆₀): The difference in lump-sum transfers provided to zero-earners across the two locations (−T₀(0) − (−T₁(0)) = T₀(0) − T₁(0)). A positive ∆₀ means Distressed provides a larger transfer to non-earners. It represents the place-based redistribution that occurs at the bottom of the earnings distribution, independently of MTR differences. In the paper’s decomposition, total optimal place-based redistribution (∆_z) exceeds ∆₀ when Distressed also has lower MTRs, meaning redistribution grows with income.

Income-constant average tax difference (∆_z): The paper’s preferred summary measure of the average place-based transfer, defined as an equally weighted average of two tax-difference indices: the tax difference evaluated at Elsewhere earnings levels and the tax difference evaluated at Distressed earnings levels. This measure isolates tax schedule differences from productivity differences across locations, avoiding conflation of tax policy and wage effects on measured income.

Landlord welfare weight (λ_L): The social marginal welfare weight assigned to landlords relative to the multiplier on the government budget constraint. When λ_L < 1, the planner values a marginal dollar of public funds more than a marginal dollar to landlords, creating a motive to use place-based taxes to shift rent incidence. The rent redistribution effect on optimal MTRs operates through the term (λ_L − 1)Δr+(θ), which has opposite signs in urban (positive) and rural (negative) distressed areas because of their different housing supply elasticities.

The Effects of Mandatory Profit-Sharing on Workers and Firms

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

This paper studies the causal effects of mandatory profit-sharing on workers and firms using a quasi-experimental design arising from a 1990 French reform that lowered the eligibility threshold for mandatory profit-sharing from 100 to 50 employees. The institutional setting is the French RSP (Réserve Spéciale de Participation), a profit-sharing scheme in place since 1967 that requires firms above the threshold to distribute a fraction of their excess profits — defined as net income above 5% of book equity — to employees according to a formula scaled by the firm’s labor share. For the median firm, this amounts to roughly 10.5% of pre-tax income transferred to workers.

The authors employ two primary empirical strategies. First, a bunching analysis exploits the pre-reform distribution of firm employment around the 100-employee threshold as a revealed-preference test of whether firms perceive profit-sharing as a net cost. Second, a difference-in-differences design compares treated firms (55–85 employees in 1989–1990, who become newly subject to the regulation after 1991) against two control groups: small firms (35–45 employees, likely never subject) and large firms (120–300 employees, already subject). Data come from the universe of French corporate tax files (FICAS) and a linked employer-employee panel (DADS) covering approximately 4% of private-sector workers, spanning 1985–1997.

The bunching analysis documents a 22.3% excess density in the 95–99 employee bin before the reform, which disappears after 1991. Three tests — comparing wage bills per employee across the threshold, cross-checking with DADS employment records, and examining profitability patterns — collectively support the conclusion that bunching reflects genuine employment reductions rather than under-reporting. The implied employment loss is approximately 1.67% of total employment among affected firms.

The difference-in-differences results yield the following firm-level findings: (a) the total compensation share (wages plus profit-sharing divided by value added) rises by 1.8 percentage points for firms with positive excess profits; (b) 77% of this increase comes at the expense of firm owners — the profit share falls by 1.37 percentage points; (c) the remainder is borne by the government through a reduction in the corporate income tax share; (d) the wage share (base wages only) is unaffected, indicating that owners do not reduce wages to offset the cost of profit-sharing; (e) investment and total factor productivity show no statistically significant change — effects on productivity are bounded below ±1% for several TFP measures; and (f) the capital-labor ratio shows a small, mostly insignificant negative effect, consistent with a model-implied increase in the cost of capital of only 0.43 percentage points.

Worker-level analysis using the linked employer-employee data confirms that average total compensation rises by approximately 3.5% for workers in treated firms, with no decline in base wages. Critically, this average conceals distributional heterogeneity across the skill spectrum. For low- and medium-skill workers (blue-collar workers, clerks, supervisors, skilled technicians), total compensation rises while base wages are unchanged — consistent with wage rigidity binding for these groups. For high-skill workers (managers, engineers, executives), base wages fall by enough to leave total compensation unchanged, consistent with more flexible wages at the upper end of the skill distribution. This pattern implies that mandatory profit-sharing is a progressive policy within firms, redistributing excess profits predominantly to lower-skill workers.

The paper concludes that France’s mandatory profit-sharing scheme, as implemented, functions as a non-distortive redistributive tool: it transfers excess profits from shareholders to lower-skill workers without generating measurable productivity losses or large investment distortions. The fiscal cost is non-trivial: each dollar transferred to workers costs approximately 20 cents in foregone corporate income tax. The scheme also has an inherent inequality in its redistribution since it exclusively benefits workers in profitable firms, and firms’ excess profits are highly persistent.

Q: What is the French RSP and how does the formula work? A: The RSP (Réserve Spéciale de Participation) is a mandatory profit-sharing fund established by executive order in 1967. The formula is RSP = 0.5 × (wage bill / value added) × max(net income − 5% × book equity, 0). The 5% deduction represents lawmakers’ view of fair compensation to shareholders; any excess is split between shareholders and workers, with the split scaled by the firm’s labor share. For the median firm in the sample — ROE of 12%, labor share of 0.52, corporate tax rate of 37% — the formula yields roughly 9.5% of pre-tax income, and in post-1991 data the realized average is 10.5% of pre-tax income for firms with positive excess profits.

Q: Why can’t a standard regression discontinuity be used at the 100-employee threshold? A: Because firms strategically control their position relative to the threshold — the bunching analysis itself demonstrates this. When firms sort non-randomly around the cutoff, the local randomization assumption underlying RD is violated. The authors instead use a difference-in-differences design exploiting the time variation introduced by the 1990 reform.

Q: How large is the pre-reform bunching and what does it imply? A: The distribution of employment shows 22.3% excess density in the 95–99 employee bin relative to the post-reform counterfactual distribution. Interpreting this as real employment reduction (supported by three empirical tests), the implied employment loss is approximately 1.67% of total employment among firms in the 85–120 employee range. Dynamic bunching analysis shows this is persistent rather than temporary — the 100-employee threshold significantly constrained three-year employment growth for firms in the 85–99 range in the pre-reform period.

Q: How do the authors establish that bunching is real rather than under-reporting of employment? A: Three tests are conducted. First, wage bills per employee show no discontinuity around the 100-employee threshold in either period, ruling out systematic under-reporting of headcount while truthfully reporting wages. Second, employment from DADS payroll records — harder to manipulate — shows only a statistically insignificant gap of roughly 0.5 employees relative to tax-file employment just below the threshold, far too small to shift firms across the 100-employee bin. Third, profitability and value added per employee are significantly higher just below the threshold, consistent with more profitable firms having stronger incentives to bunch through genuine employment reductions.

Q: What is the main identification strategy for the firm-level analysis? A: A difference-in-differences design where treated firms have 55–85 employees in both 1989 and 1990 (newly subject to the mandate after 1991), compared to small control firms with 35–45 employees (likely never subject) and large control firms with 120–300 employees (likely always subject). Specifications include firm fixed effects and county-by-year and industry-by-year fixed effects. Parallel pre-trends are confirmed graphically and in event-study regressions. The design is intent-to-treat: by 1997, 26.7% of treated firms had shrunk below 50 employees and did not actually pay profit-sharing. LATE estimates are obtained via 2SLS.

Q: What are the main firm-level findings on compensation and profit shares? A: For treated firms with positive excess profits, the total compensation share rises by 1.8 percentage points. The wage share (base wages only, excluding profit-sharing) is precisely estimated at zero — owners do not reduce wages. The profit share falls by 1.37 percentage points, accounting for 77% of the increase in total compensation. The remaining approximately 23% is borne by the tax authority through a reduction in the corporate income tax share, since profit-sharing reduces the corporate income tax base. These findings are robust to balanced vs. unbalanced samples and to alternative control group definitions.

Q: Does mandatory profit-sharing raise or lower firm productivity? A: Across five different TFP estimators (Olley-Pakes, Olley-Pakes with Ackerberg-Caves-Frazer correction, Wooldridge, Levinsohn-Petrin, and Ackerberg-Caves-Frazer), the effect of mandatory profit-sharing on productivity is a precisely estimated zero. For several measures, effects larger than ±1% in magnitude can be rejected. Softer measures of effort — sick leave rates and the probability of working extra hours — also show no significant change. This null finding contrasts with the literature on voluntary profit-sharing adoption, which typically finds 3–5% productivity gains, likely reflecting selection bias in that literature.

Q: Does mandatory profit-sharing distort investment? A: The effect on investment is small and mostly statistically insignificant. The theoretical model shows why: the profit-sharing formula is based on excess profits (net income minus 5% of book equity), not total profits. When the firm’s actual cost of equity approximately equals the regulatory 5% benchmark, the distortion to the cost of capital is zero. The calibrated distortion to the user cost of capital is only 0.43 percentage points — approximately 1.9% of the standard user cost — implying an investment ratio reduction of about 0.84 percentage points using estimated elasticities from Chodorow-Reich et al. (2024). Empirically, capital-labor ratios show a small, largely insignificant negative effect.

Q: How does profit-sharing incidence differ across the skill distribution? A: The worker-level DADS analysis reveals that the average 3.5% increase in total compensation masks sharp heterogeneity. For low- and medium-skill workers (blue-collar workers, clerks, supervisors, skilled technicians), total compensation rises while base wages are unchanged. For high-skill workers (managers, engineers, executives), base wages decline sufficiently to leave their total compensation unchanged. The authors interpret this pattern as consistent with wage rigidity being more binding for lower-skill workers — due to the federal minimum wage and collective agreements — than for managers whose pay is more flexibly set.

Q: Why does profit-sharing not affect base wages for low-skill workers? A: Two candidate explanations are considered. The risk channel — that profit-sharing is risky and thus less valuable to risk-averse workers, who demand wage compensation — is rejected empirically because profit-sharing only marginally increases the variability of workers’ total earnings. The wage rigidity channel is supported: France’s binding federal minimum wage and widespread collective agreements constrain downward adjustment in base wages for lower-skill workers, so firms cannot pass through profit-sharing costs as lower wages for this group.

Q: What is the fiscal cost of the profit-sharing scheme? A: Each dollar transferred to workers through mandatory profit-sharing costs approximately 20 cents in reduced corporate income tax receipts, since profit-sharing payments are deductible from taxable income. The paper notes this is a partial fiscal evaluation; a full assessment would also require analyzing personal income tax implications, which are left for future work.

Q: How does this scheme compare to a corporate income tax as a redistributive tool? A: Both instruments reduce firm profits and can benefit workers, but differ in three key respects. First, the tax base differs: profit-sharing targets excess profits above 5% of book equity whereas the corporate income tax applies to all corporate earnings, generating different distortions to investment. Second, profit-sharing goes directly to workers in the same firm, whereas corporate tax revenues are redistributed through general government spending — making the incidence more direct and more closely monitored by workers. Third, workers have stronger incentives to monitor firm compliance with profit-sharing (each euro of diverted excess profit reduces workers’ collective income by roughly 10–15 cents) than with corporate taxes.

Q: How does this paper compare to findings on mandatory profit-sharing in Peru? A: Tolentino (2022) studies a mandatory profit-sharing scheme in Peru exploiting a 20-employee eligibility threshold and finds larger distortions — reductions in both investment and productivity. The authors attribute this difference to two features: the Peruvian scheme applies to the entirety of post-tax profits rather than excess profits above an equity deduction, creating a broader and more distortionary base; and there is pre-existing bunching at the Peruvian threshold even before the scheme was introduced, suggesting confounding pre-existing regulations.

Q: What are the scope conditions on the external validity of the findings? A: The findings apply specifically to mandatory profit-sharing under the French RSP formula — which exempts a 5% equity return from the profit-sharing base, limiting distortions — during 1985–1997, for firms in the 55–300 employee range. The null productivity effect may not generalize to voluntary schemes, where selection on anticipated gains likely produces positive correlations. The redistributive finding (benefiting lower-skill workers) is specific to a context with binding minimum wages and collective agreements that constrain wage adjustment for that group. The fiscal cost calculation also excludes personal income tax effects.

Excess profits: Defined in the paper as net income minus 5% of book equity — the amount above what lawmakers considered fair compensation to shareholders. Only excess profits (not total profits) are subject to the mandatory profit-sharing formula.

RSP formula (Réserve Spéciale de Participation): The statutory formula RSP = 0.5 × (wage bill / value added) × max(net income − 5% × book equity, 0), scaled by the firm’s labor share to reflect labor’s contribution to production. Unchanged since 1967.

Total compensation share: The ratio of (wage bill plus profit-sharing) to value added — the paper’s primary measure of workers’ overall claim on firm output, as distinct from the wage share (wage bill alone divided by value added).

Wage incidence parameter (λ): The fraction of profit-sharing that firms pass through to workers as lower base wages. λ = 1 means full incidence (workers’ total compensation unchanged); λ = 0 means no incidence (workers fully benefit). The paper’s empirical findings are consistent with λ ≈ 0 for low-skill workers and λ ≈ 1 for high-skill workers.

Bunching: The empirical phenomenon whereby firms cluster employment just below the 100-employee regulatory threshold to avoid mandatory profit-sharing. The paper uses the pre- vs. post-reform shift in the employment distribution as a revealed-preference test of whether firms perceive the scheme as a net cost.

Intent-to-treat (ITT) design: The empirical design comparing firms that were in the newly eligible size range (55–85 employees) just before the 1990 reform against firms that were either always or never eligible, regardless of whether treated firms actually ended up paying profit-sharing post-reform. LATE estimates are obtained via 2SLS to recover effects on actual compliers.

Distortion to user cost of capital: The additional cost of capital induced by profit-sharing, equal to ϕ × γ(1−λ) / [1 − γ(1−τ)] × (re − ρ), where ρ = 5% is the regulatory equity benchmark. When the firm’s actual cost of equity equals the 5% benchmark, this distortion is zero — a feature that distinguishes the French scheme from a standard corporate income tax.

H20 | Macro Paper Warehouse

"Compensate the Losers?" Economic Policy and the Origins of U.S. Partisan Realignment

Layer 1 — Overview

In depth

Q1. What is the paper’s central conceptual innovation, and how does it differ from prior realignment research?

Q2. How large and stable is the educational gradient on predistribution, and how does it compare to social issues?

Q3. What happened to predistribution as a share of the Democratic House agenda after the 1970s?

Q4. How did 1970s campaign finance reforms change the financial composition of the Democratic Party?

Q5. Who are the “New Democrats” / DLC, and when did they emerge?

Q6. How do DLC members vote differently from other Democrats, and how is this differential conservatism distributed across policy types?

Q7. Do DLC members finance differently from other Democrats?

Q8. When precisely did educational realignment in Democratic party identification begin, and what does the inflection-point analysis show?

Q9. How do hypothetical presidential matchup surveys test the DLC mechanism?

Q10. What do actual House election results (MCDG-level data) show about DLC electoral performance by neighborhood education?

Q11. How much of educational realignment can the paper’s mechanism account for, and how is this calculated?

Q12. Can social issues, Civil Rights realignment, or Republican changes better explain the 1970s inflection point?

Q13. What is the role of out-of-district individual donors in shifting Democratic Party positions?

Q14. Are predistribution policies becoming less popular overall, which might independently push Democrats away from them?

Key Concepts

Global Working Hours

In depth

Q1. What new data does the paper assemble, and how does it improve on prior global hours databases?

Q2. How seriously does the seasonality concern affect the estimates?

Q3. How much do hours worked actually vary with economic development?

Q4. Why do hours worked by the young and the elderly fall with development?

Q5. What happens to prime-age hours, and what is the “great gender reshuffling”?

Q6. What role do religion and political history play in female hours worked?

Q7. How are labor taxes related to hours worked, and what explains the relationship?

Q8. Can a standard labor supply model rationalize these findings?

Q9. What is the paper’s overall interpretation?

Q10. What are the main scope conditions and caveats?

Key concepts

Key concepts

Place-Based Redistribution

Place-Based Redistribution: Overview

In depth

Q1. What is the equity-efficiency tradeoff formula for a lump-sum place-based transfer, and what does it reveal?

Q2. What characterizes the optimal lump-sum transfer t* in Proposition 1?

Q3. Under skill-taste correlation, why are place-based transfers always welfare-improving even under an optimal income tax?

Q4. Under comparative advantage, why can the sign of the optimal transfer reverse with migration elasticity?

Q5. Why are place-based transfers superfluous under pure income-based sorting with homogeneous locational preferences?

Q6. What new terms appear in the optimal location-specific MTR formulas (Proposition 2) relative to a standalone-economy optimum?

Q7. How do housing supply elasticities affect the optimal spatial transfer, and why does the sign differ between urban and rural settings?

Q8. What does the urban EZ baseline calibration find about optimal transfers and how does it compare to actual EZ policy?

Q9. What does the rural EZ calibration find, and how sensitive are results to migration assumptions?

Q10. Do within-income transfers arising from differences in marital and parental status across communities effectively constitute place-based redistribution?

Q11. What does the MTR decomposition (Table 3) reveal about why sorting motives generate different MTR patterns?

Q12. What does the crosswalk from urban to rural baseline reveal about which assumptions drive the change in optimal transfers?

Key Concepts

The Effects of Mandatory Profit-Sharing on Workers and Firms